Author Response

Reviewer 1 (Public Review):

Protein oligomerization is essential to their in vivo function, and it is generally challenging to determine the distribution of oligomeric states and the corresponding conformational ensembles. By combining coarse-grained molecular dynamics simulations and experimental small-angle X-ray scattering profiles at different protein concentrations, the authors have established a robust approach to self-consistently determine the oligomeric state(s) and the conformational ensemble. The approach has been applied specifically to the speckle-type POZ protein (SPOP) and generated new insights into the conformational ensemble and structural features that determine the ensemble. The model was further tested by the analysis of several relevant mutants as well as models with different types of structural restraints. The results also support the isodesmic selfassociation model, with KD values comparable to those measured from independent experiments in the literature. The approach is potentially applicable to a broad set of systems.

We thank the reviewer for taking the time to assess our work.

Reviewer 2 (Public Review):

This manuscript applied the SAXS data analysis of protein selfassembly by implementing the simultaneous fitting of intra- and intermolecular motions/conformations against SAXS data at a series of oligomerization states/concentrations. Despite several major assumptions hinted, a diverse pool of conformational and oligomeric candidates was generated from CG simulations, and more importantly, these candidates were fitted into these SAXS data to reach a reasonable agreement, suggesting a somewhat convergence (even if the ensemble-fitting could well be at a local minimal). This is considered a technical advance, given the fairly large numbers of both the oligomer fraction phi_i (i=1, ..., N) and the conformational weight w_k (k=1, ..., n), where N is the number of oligomers and n is the number of internal conformational states.

We thank Prof. Yang for taking the time to assess our work.

Central is optimizing phi_i and w_k, simultaneously. The former has been illustrated in Fig. 4 and SI-Fig. 7 for the total number of 60mers. The latter relies on an overfitting-preventing strategy, as shown in SI_Fig. 1, where an effective fraction cutoff was used from 0.1 to 1.0, as opposed to the number of conformational states. What are the numbers of conformational states for these oligomers? This should be quantifiable, e.g., defining the conformational differences by chi_2.

The reviewer is correct that the entropy-based term for preventing overfitting is a key aspect of the method. In contrast to some of the other methods to combine experiments with simulations, our approach does, however, not require us to define individual conformational states. Instead, the weights in the entropy term refer to individual configurations rather than states, and we can thus integrate the SAXS experiments and simulations without, for example, clustering the conformations. Indeed, for most of the collective variables that we have calculated from the ensembles, such as the radii of gyration, end-to-end distances, and MATH-MATH distances, we observe continuous monomodal probability distributions, which suggests that it might be difficult to define a few distinct conformational states. For the MATH-BTB/BACK distance, we observe a trimodal distribution, and these distinct conformational states are shown as overlaid structures in Fig. 4i. Thus, while these “states” change populations during reweighting, this is the result from changing weights of the individual configurations.

Reviewer 3 (Public Review):

Molecular-level interpretations of SAXS data are challenging, especially for oligomeric systems of variable length with intrinsic flexibility and the possibility of multiple association interfaces. In order to make this challenge tractable, a number of assumptions are made here: 1) There is a single pathway by which individual domains associate first into homodimers and then into longer oligomers; 2) the association kinetics is isodesmic, which allows the direct calculation of oligomer distributions based on the given value of a single dissociation constant; 3) the internal dynamics within dimers is restricted essentially to relative domain-domain motions, that are sampled comprehensively via MD simulations. As a result, excellent fits to the SAXS data are obtained and the underlying conformational ensembles are highly plausible. The resulting models are useful to further understand SPOP function, especially in the context of liquidliquid phase separation.

We thank the reviewer for taking time to read our work and for their various suggestions.

Author Response

Reviewer #1 (Public Review):

This work provides a new general framework for estimating missing data on cervical cancer epidemiology, including sexual behavior, HPV prevalence, and cervical cancer incidence. These data are useful to determine impact projections of cervical cancer prevention. The authors suggest a three-step approach: 1) a clustering method applied on registries with an intermediate level of data availability to cluster cervical cancer incidence based on a Poisson-regression-based CEM algorithm, 2) a classification method applied on registries with a low level of data availability to classify cervical cancer incidence based on a Random Forest, 3) a projection method applied on missing data based on the mean of available data. The authors use India as a case study to implement this new methodology. Results indicate that two patterns of cervical cancer incidence are identified in India (high and low incidence), classifying all Indian states with missing data to a low incidence. From this classification, missing data is approximated using the mean of the available data within each cluster.

A strength of this approach is that this methodology can be applied to regions with missing data, although a minimum set of information is needed. This makes it possible to have individual data for each unit in the region.

One of the weaknesses of this methodology is the need for a minimum set of epidemiological data to enable impact projections. It is true that when epidemiological cervical cancer data is not available, authors mentioned that general indicators (e.g., human development index, geography) can be used but projections will be probably less realistic. As observed with other techniques, countries with fewer resources have less data available and cannot benefit from these types of techniques to have more adequate guidelines.

Imputation of missing data is always a challenging issue. The technique proposed in this manuscript is an interesting new approach to missing data imputation that could be applied with a minimum set of available data. However, we must focus on obtaining reliable data from each region of the world to help local health authorities implement better preventive measures for the local population.

We thank the reviewer for the considerate comments and suggestions and have tried to incorporate them as much as possible in the revised manuscript.

As the reviewer has pointed out, the applicability of the proposed methodology depends on the available data. In our opinion, it is a general challenge for approximating missing data, rather than a weakness particular to our methodology. In fact, we believe that our framework is flexible to address missing data in many situations. To clarify this point, we have included the following sentences in the Discussion (lines 363-376, page 18): “It is important to note that, in general, the applicability the proposed framework depend on the actual amount of data available. However, in our opinion, it is a general challenge for approximating missing data, rather than a weakness particular to our methodology. By allowing possible adaptations, we believe that our framework is sufficient flexible to address missing data in many situations.”

Finally, we fully agree with the reviewer that we should continue our effort to collect more data for countries where these are not available. The proposed framework should be considered as a solution to the situation in which collection of additional data is not or not yet possible.

Reviewer #2 (Public Review):

The burden of cervical cancer worldwide is well recognized. While prevention strategies, including vaccination against human papillomavirus (HPV), cervical cancer screening, and pre-cancer treatment, can reduce the burden of cervical cancer, access to these measures is still limited, especially in low- and middle-income countries. Since the impact of prevention strategies is heavily dependent on the disease's burden on a particular population, we need to know the latter to assess the impact of these context-specific prevention strategies.

However, epidemiological data on cervical cancer are not always available for all geographical areas. This paper uses India as a case study to propose a framework called "Footprinting" to comprehensively evaluate the burden of cervical cancer. The authors applied a three-step analytical strategy to impute cervical cancer epidemiological data in states where this information was unavailable using data from cervical cancer incidence, HPV prevalence, and sexual behaviour from other regions. The findings suggest a high and low incidence of cervical cancer incidence in different parts of India; all Indian states with missing data were classified as low incidence.

The proposed analytical strategy presents an important solution for imputing data from geographic areas of a country where data are missing.

We thank the reviewer for the considerate comments and suggestions and have tried to incorporate them as much as possible in the revised manuscript.

One conceptual limitation of this work is the lack of explanation or evidence that sexual behaviour can be used to approximate cervical cancer and/or HPV rates.

A similar comment was raised by Reviewer #1. It is well established that sexual contact is the only transmission route of carcinogenic HPV infection, and hence necessary for the occurrence of cervical cancer [ref #26 Vaccerella 2006, Muñoz 1992 Int J Cancer 52, 743-749].

We have included sexual behaviour variables that have previously been shown to be risk factors of HPV infection and cervical cancer risk, e.g., age of sexual debut and number of sexual partners [ref #26 Vaccerella 2006, ref #27 Schulte-Frohlinde 2021]. Furthermore, we used variables that are commonly available so that the analyses can be easily applied to other settings.

As far as we know, there is no established set of sexual behaviour variables for predicting the patterns of HPV prevalence and cervical cancer incidence. The good prediction performance in the India case study shows that using the selected set is sufficient. As sexual behaviour variables are highly correlated, including more variables might even risk overfitting.

To clarify these points we have included the following paragraph in the Discussion (lines 319-325, page 16): “In our analysis of classifying clusters of cervical cancer incidence, we only included some of the sexual behaviour variables available in the NACO report [15]. We selected variables that were previously shown to be risk factors of HPV infection and cervical cancer risk and that are commonly available so that the analyses can be easily applied to other settings, e.g., age of sexual debut and number of sexual partners [26, 27]. As far as we know, there is no established set of sexual behaviour variables for predicting the patterns of HPV prevalence and cervical cancer incidence. The good prediction performance shows that using the selected set is sufficient. As sexual behaviour variables are highly correlated, including more variables might even risk overfitting.”

Also, full information on the three main indicators is only available in two states. This is used to impute the values for the other states.

Indeed, HPV prevalence data were only available for two states. While we acknowledge that this affects the certainty in the imputed HPV prevalence, we considered the imputed results to be satisfactory based on the good accordance with the cervical cancer incidence data we found in the validation step (lines 286-23, page 14). We verified that the ratio of HPV prevalence between the high-and low-incidence cluster (1.7-fold) was very similar to the ratio of age-standardized cervical cancer incidence (1.9-fold).

Furthermore, we note that previous modelling works on India relied on even less data, namely one source of HPV prevalence and cervical cancer incidence data [ref #29 Brisson 2020, Diaz 2008 Br J Cancer].

Moreover, the available data used in this study also present some limitations; for example, cervical cancer incidence data were from 2012 to 2016, while sex behaviour data were from 2006. This large gap is likely to have a significant cohort effect, especially given changes in sexual norms in Western countries over the last few decades, which may have gradually influenced other countries, especially in this age of the internet and social media.

In our opinion, for the purpose of modelling the natural history of cervical cancer, it is not necessarily more adequate to use the most recent data of sexual behaviour data. Arguably, as sexual behaviour is the “exposure” for the “outcome” cervical cancer, calibration of HPV transmission and cervical cancer model is best done with data of sexual behaviour and cervical from the same cohorts, hence, sexual behaviour data from an earlier period than the cervical cancer data.

In addition, if changes of sexual behaviour occur across the country, it should not affect the clustering much.

Finally, due to delay in reporting, cervical cancer incidence from the period 2012-2016 is the most recent edition at the moment of writing. Regarding sexual behaviour data, there is at the moment no later edition of the NACO report published after that of year 2006.

Finally, it would be interesting to validate this methodology to confirm its utility.

We agree that it would be very interesting to validate this proposed methodology in other regions. Unfortunately, it was beyond the scope of this work. Currently, we are working on a project in which we try to apply footprinting to a collection of low- and middle-income countries.

The proposed framework's strength is difficult to evaluate because the steps and justification for the model variables were not clearly presented, nor were the models validated.

We acknowledge that the framework could be more clearly presented and have added additional explanation in the following places to do so:

• Concerning the framework steps, in Method (144-163, pages 7-8): “For convenience of explanation, we assumed earlier that data availability occurs hierarchically. However, the framework can also be applied with less stringent data requirements. First, the source of Footprint data needs not necessarily cover all geographical units. It is still possible to train a classifier in the classification step with Footprint data available for only a part of clustered geographical units. Second, if none of the key cervical cancer epidemiological data (sexual behavior, HPV prevalence, and cervical cancer incidence data) have large enough coverage to serve as Footprint data, alternatives indicators of similarity, such as human development index and geographical distance, could also be used as substitute. However, the resulting classification performance might be suboptimal, as we expect these indicators to correlate less well with cervical cancer risk. Third, for the projection step, data of cervical cancer incidence, sexual behavior, and HPV prevalence needed for calibration of projection models need not necessarily belong to the same geographical unit. Calibration can be performed as long as the three types of data are available within each cluster.

With these less stringent data requirements, the proposed framework should sufficient flexible to be applied to many situations. However, one should still be cautious in applying the framework when there are little data. This means that, in some cases, we might need to exclude from the analysis some geographical units with too little data or redefine bigger geographical units if the data are not granular enough. Furthermore, we should assess the goodness-of-fit of the obtained clustering, performance of classification, correlation of data within different clusters, and calibration fits to ensure the validity of the final impact projections.”

• Concerning selection of model variables (lines 319-325, page 16): “In our analysis of classifying clusters of cervical cancer incidence, we only included some of the sexual behaviour variables available in the NACO report [15]. We selected variables that were previously shown to be risk factors of HPV infection and cervical cancer risk and that are commonly available (e.g., age of sexual debut and number of sexual partners) so that the analyses can be easily applied to other settings [26, 27]. In the India case study, the good classification performance shows that using the selected set is sufficient. As sexual behaviour variables are highly correlated, including more variables might even risk overfitting.”

Based on the authors' interpretation of the framework findings, this framework may help extrapolate data from one country to another. I'm curious as to whether this framework could be applied across states and countries.

We thank the reviewer for this comment. Currently, we are working on a multi-year projects in which we try to apply the framework to all low- and middle-income countries.

Author Response:

eLife assessment

This work is an attempt to establish conditions that accurately and efficiently mimic a drought response in Arabidopsis grown on defined agar-solidified media - an admirable goal as a reliable experimental system is key to conducting successful low water potential experiments and would enable high-throughput genetic screening (and GWAS) to assess the impacts of environmental perturbations on various genetic backgrounds. The authors compare transcriptome patterns of plant subjected to water limitation imposed using different experimental systems. The work is valuable in that it lays out the challenges of such an endeavor and points out shortcomings of previous attempts. However, a lack of water relations measurements, incomplete experimental design, and lack of critical evaluation of these methods in light of previous results render the proposed new methodology inadequate.

We thank eLife for the initial assessment and comments to our work. In our revised manuscript we plan to address the main concerns raised by reviewers. Specifically, we plan to perform water relations measurements for all our treatment assays, as well as explore the separate effects agar hardening and nutrient concentration have in our low-water agar assay. We will also provide a more in depth critical review of our results compared to previously published results.

Reviewer #1 (Public Review):

High-throughput genetic screening is a powerful approach to elucidate genes and gene networks involved in a variety of biological events. Such screens are well established in single-celled organisms (i.e. CRISPR-based K/O in tissue culture or unicellular organisms; screens of natural variants in response to drugs). It is desirable to extend such methodology, for example to Arabidopsis where more than 1000 ecotypes from around the Northern hemisphere are available for study. These ecotypes may be locally adapted and are fully sequenced, so the system is set up for powerful exploration of GxE. But to do so, establishing consistent "in vitro" conditions that mimic ecologically relevant conditions like drought is essential. 

The authors note that previous attempts to mimic drought response have shortcomings, many of which are revealed by 'omics type analysis. For example, three treatments thought to induce osmotic stress; the addition of PEG, mannitol, or NaCl, fail to elicit a transcriptional response that is comparable to that of bonafide drought. As an alternative, the authors suggest using a low water-agar assay, which in the things they measure, does a better job of mimicking osmotic stress responses. The major issues with this assay are, however, that it introduces another set of issues, for example, changing agar concentration can lead to mechanical effects, as illustrated nicely in the work of Olivier Hamant's group.

We thank the reviewer for their comments. We hypothesize that our low-water agar assay is able to replicate drought gene expression patterns through a combination of hardened agar and higher nutrient concentration. However, we did not explore the separate effects each of these factors may play in eliciting such responses. Thus, in our revised manuscript, we will explore what role the mechanical effects of changing agar concentration has on root gene expression. However, we suspect that the mechanical effects introduced by hard agar does not introduce another issue per se, but in fact may help with replicating the transcriptional effects seen under drought.

Reviewer #2 (Public Review):

[…] The authors have not always considered literature that would be relevant to their topic. For example, there is a number of studies that have reported (and deposited in the public database) transcriptome analysis of plants on PEG-plates or plants exposed to well-controlled, moderate severity soil drying assays (for the latter, check the paper of Des Marais et al. and others, for the former, Verslues and colleagues have published a series of studies using PEG-agar plates). They also overlook studies that have recorded growth responses of wild type and a range of mutants on properly prepared PEG plates and found that those results agree well with results when plants are exposed to a controlled, partial soil drying to impose a similar low water potential stress. In short, the authors need to make such comparisons to other data and think more about what may be wrong with their own experimental designs before making any sweeping conclusions about what is suitable or not suitable for imposing low water potential stress. 

To solve the problem of using these other systems to impose low water potential stress, the authors propose the seemingly logical (but overly simplistic) idea of adding less water to the same mix of nutrients and agar. Because the increased agar concentration does not substantially influence water potential (the agar polymerizes and thus is not osmotically active), what they are essentially doing is using a concentrated solution of macronutrients in the growth media to impose stress. This is a rediscovery of an old proposal that concentrated macronutrient solutions could be used to study the osmotic component of salt stress (see older papers of Rana Munns). There are also effects of using very hard agar that is of unclear relationship to actual drought stress and low water potential. Thus, I see no reason to think that this would be a better method to impose low water potential. 

We thank the reviewer for their comments. In our revised manuscript, we will address points regarding plant and soil water potential; similar concerns were also raised by Reviewer 1 and 3. We note that we report vermiculite water content in Supplementary Table 4.

We would like to clarify that both the PEG media and overlay solution were buffered - we did not include this within the written description in the methods, but will do in our revised manuscript.

We agree with the reviewer’s concern that it may be problematic to compare the transcriptomic profiles of seedling and mature plants. In light of this, we plan to explore what effects our treatment media has on mature rosettes.

We note that we do not claim that PEG is unable to produce low-water potential responses similar to partial soil drying. Indeed, we indicate that it is a good technique for eliciting phenotypes comparable to drought at the physiological level (line 48). Rather, we claim that PEG is unable to produce gene expression responses that are sufficiently similar to partial vermiculite drying.

Reviewer #3 (Public Review):

[…] The authors observed that gene expression responses of roots in their 'low-water agar' assay resembled more closely the water deficit in pots compared to the PEG, mannitol, and salt treatments (all at the highest dose). In particular, 28 % of PEG led to the down-regulation of many genes that were up-regulated under drought in pots. Through GO term analysis, it was pointed out that this may be due to the negative effect of PEG on oxygen solubility since downregulated genes were over-represented in oxygen-related categories. The data also shows that the treatment with abscisic acid on plates was very good at simulating drought in roots. Gene expression changes in shoots showed generally a high concordance between all treatments at the highest dose and water deficit in pots, with mannitol being the closest match. This is surprising, since plants grow in plates under non-transpiring conditions, while a mismatch between water loss by transpiration on water supply via the roots leads to drought symptoms such as wilting in pot and field-grown plants. The authors concluded that their 'low-water agar' assay provides a better alternative to simulate drought on plates. 

Strengths: 

The development of a more robust assay to simulate drought on plates to allow for high-throughput screening is certainly an important goal since many phenotypes that are discovered on plates cannot be recapitulated on the soil. Adding less water to the media mix and thereby increasing agar strength and nutrient concentration appears to be a good approach since nutrients are also concentrated in soils during water deficit, as pointed out by the authors. To my knowledge, this approach has not specifically been used to simulate drought on plates previously. Comparing their new 'low-water agar' assay to popular treatments with PEG, mannitol, salt, and abscisic acid, as well as plants grown in pots on vermiculite led to a comprehensive overview of how these treatments affect gene expression changes that surpass previous studies. It is promising that the impact of 'low-water agar' on the shoot size of 20 diverse Arabidopsis accessions shows some association with plant fitness under drought in the field. Their methodology could be powerful in identifying a better substitute for plate-based high-throughput drought assays that have an emphasis on gene expression changes. 

Weaknesses: 

While the authors use a good methodological framework to compare the different drought treatments, gene expression changes were only compared between the highest dose of each stress assay (Fig. 2B, 3B). From Fig. 1F it appears that gene expression changes depend significantly on the level of stress that is imposed. Therefore, their conclusion that the 'low-water agar' assay is better at simulating drought is only valid when comparing the highest dose of each treatment and only for gene expression changes in roots. Considering how comparable different levels of stress were in this study leads to another weakness. The authors correctly point out that PEG, mannitol, and salt are used due to their ability to lower the water potential through an increase in osmotic strength (L. 45/46). In soils, water deficit leads to lower water potential, due to the concentration of nutrients (as pointed out in L. 171), as well as higher adhesion forces of water molecules to soil particles and a decline in soil hydraulic conductivity for water, which causes an imbalance between supply and demand (see Juenger and Verslues, The Plant Cell 2022 for a recent review). While the authors selected three different doses for each treatment that are commonly used in the literature, these are not necessarily comparable on a physiological level. For example, 200 mM mannitol has an approximate osmotic potential of around -5 bar (Michel et al. Plant Physiol. 1983) whereas 28 % PEG has an osmotic potential closer to -10 bar (Michel et al. Plant Physiol. 1973). It also remains unclear how the increase in agar concentration versus the increase in nutrient concentration in the 'low-water agar' affect water potentials. For these reasons it cannot be known whether a better match of the 'low-water agar' at the 28% dose to water deficit in pots for roots in comparison to the other treatments is due to a good match in stress levels with the 'low-water agar' or adverse side-effect of PEG, mannitol, or and salt on gene regulation. Lastly, since only two biological replicates for RNA sequencing were collected per treatment, it is not possible to know how much variance exists and if this variance is greater than the treatments themselves. 

We thank the reviewer for their comments. In our statistical analyses, we found that dose-responsive genes (as fit by a linear model) were very similar to those genes found differentially expressed at the highest dose. Thus, for clarity, we decided to simply present the genes differentially expressed at the highest dose. We see now that this might have been an oversimplification. In our revised manuscript, we will present genes that are dose responsive across the range of treatment doses, thus providing more evidence that lower doses of low-water agar are also capable of simulating drought (as is suggested by overlap analysis of Figure 2A).

Additionally, we will also explore the osmotic potential of each of our different assays to provide a better benchmark of how comparable each of our treatments are (as similarly requested by Reviewer 1 and 2). Lastly, to address concerns regarding the size of variance in gene expression, we will sequence a 3rd replicate of RNA.

Author Response

Reviewer #2 (Public Review):

1) Although the images and videos were of great quality, the results derived from them provided little new knowledge and few conceptual insights into male reproductive tract biology and basically confirmed what has been published using traditional methods. For example, the high intensity of the vascular network in the initial segment was previously reported by Abe in 1984 and Suzuki in 1982; the pattern of the major lymphatic vessel and drainage was beautifully depicted by Perez-Clavier, 1982.

We thank the reviewer for his/her appreciative comments regarding the quality of the images/videos we provide in this study. We do not fully agree with his/her assessment of the lack of novelty. Our work confirms earlier reports that are now dated (1980s), which in itself is worth mentioning for the interested community, especially when the confirmation uses the most advanced technologies available today. We have never said that nothing was done in the past, and we have acknowledged all past contributors (including those mentioned by the reviewer) by pointing out the limitations of the technical tools that were available at the time. In addition, our current work provides a more comprehensive and global view by extending our approach to the entire mouse epididymis, whereas previous work was much more limited.

2) The authors were very cautious when interpreting the results of marker immunostaining however these markers were not specific for a definite cell type. For example, as the authors stated, VEGFR3 marks both lymphatic vessels and fenestrated blood vessels. how could the authors claim the VEGFR3+ network was lymphatic? The authors claimed that they used three markers for the lymphatic vessel. But staining results of the networks were very different. How could the author make conclusions about the network of lymphatic vessels in the epididymis?

We broadly agree with the reviewer and have made it clear that one cannot be 100% sure that all the VEGFR3+ structures we present are lymphatic. However, in total, we used 4 documented lymphatic markers (not 3 as mentioned by the reviewer) which are (VEGFR3, LYVE1, PROX1 and PDPN). Three of them give very similar profiles, while only PDPN shows some differences. We are currently studying in more detail the expression of PDPN in the mouse epididymis because we speculate that this marker may target a population of pluripotent cells in this tissue. Therefore, with the 3 similar profiles and with the subtraction of PVLAP+ structures, we are pretty confident that what we show corresponds to the different lymphatic structures.

3) To understand the vascular network development in the epididymis, would the authors please look at the fetal stage when the vascular network is established in the first place? Wolffian duct tissues are much smaller and thinner and would be amenable for 3D imaging probably even without clearing.

We generally agree with the reviewer that this could be an interesting addition. However, it represents a significant amount of additional work. Organ clearing will certainly be required because it is unlikely that Wolffian duct will be sufficiently transparent to allow lightsheet microscopy. In the literature, the study of Wolffian duct relies primarily on whole mounts, inclusions, and cryosections. Besides the fact that this represents a lot of extra work, we are not totally convinced that this would be of much use. A key reason is that the epididymis is an organ that differentiates completely after birth (Robaire and Hinton, 2015). It is reported that differentiation of mouse caput segment 1 occurs around 19DPN (Xu et al., 2016) and is intimately related to the development of the vasculature (Lebarr et al., 1986). Regarding the lymphatic network, Swingen et al, (2012) reports that lymphangiogenesis in the mouse testis and epididymis is initiated late in gestation after 15DPC. Videos showing the external lymphatic vessels of the testis and epididymis at 17.5DPC can be seen at https://doi.org/10.1371/journal.pone.0052620.s002. The authors indicate that lymphangiogenesis occurs via sprouting from the adjacent mesonephros. We hypothesize that the more internal lymphatics evolve between birth and 10DPN, which corresponds to the time when we observed LEPC Lyve1pos cells.

4) Immunofluorescence staining of VEGF factors was not convincing. As a secreted factor, VEGF will be secreted out of the cells, would it be detected more in the interstitium? I am always skeptical about the results of immunostaining secreted growth factors. Would it be possible to perform in situ or RNAscope to confirm the spatial expression pattern of VEGFs?

Well, active VEGF factors result from alternative mRNA splicing events and posttranslational proteolytic cleavage. Therefore, in our opinion, the study of VEGF mRNA by in situ hybridization or RNAscope analysis will not be very informative about the actual presence of active forms of VEGF in the epididymis. If necessary, we can provide as supplementary material immunohistochemistry data showing the presence of VEFG-A in the epididymal principal cells. Our major objective with these data was to show that VEGF factors and their respective receptors were present in the epididymis. Nevertheless, in an attempt to convince the reviewer, we provide as accompanying data to this rebuttal letter new sets of figures (Figures VEGF-A-response editor & VEGFC /VEGF-D-response editor) that we believe can improve the perception of our data. If the editorial office feels it is necessary, these figures could be added to the supplementary figure set (as Figure 6figure supplement 1 and Figure 6-figure supplement 2). For VEGF-A the data exists already in the literature as we have indicated (Korpelainen, 1998). In fine, our goal was not to show which cell types of the epididymis epithelium produce VEGFs but rather than VEGF factors and their receptors where there in order to support angiogenesis or lymphangiogenic activity in the tissue. In addition, we hypothesize that because septa have been reported to constitute barriers between segments restricting passive diffusion of molecules (Turner et al., 2003; Stammler et al., 2015), the VEGF factors are expected to be produced locally.

Figure VEGF-A - response editor : Immunofluorescence of the angiogenic ligand VEGF-A in the epididymis. Figure 6 shows that this ligand is mainly found in the caput and more precisely in S1.It is very strongly expressed in the peritubular microvascularization of the SI which expresses the VEGFR3:YFP transgene whereas it is less expressed by intertubular blood vessels (asterisk). This seems to indicate that it is the peritubular vessels that are in the majority responsible for the angiogenic activity measured in our study. Furthermore, it is expressed by the epithelium as secretory vesicles (IS, and S3 and enlargement) which is in agreement with in situ hybridization work performed by Korpelainene E.I et al J.Cell.biol 1998). The enlargement shown in S3_Z shows the sagital plane of the tubule where one can distinguish VEGFR:YFP positive cells that strongly express are also VEGF-A positive indicating that the same cells of the epithelium express both the receptor and the ligand. Here the transgene is detected directly without the use of an anti-GFP which allows to enhance the signal.

Figure VEGF-C / VEGF-D - response editor : Immunofluorescence of VEGF-C and VEGF-D lymphangiogenic ligands in the epididymis. This figure shows that these ligands are mainly found in the interstitial tissue throughout the organ with a higher proportion in the caudal part. This expression may be largely driven by fibroblasts, which are widely represented in the interstitium, or by endothelial cells, since these two ligands are expressed by these cell types. However, as shown in the figures and in the enlargement of panel A, VEGF-C is also produced by epithelial cells within what may appear as secretory vesicles. In contrast, for VEGF-D, we observe only few weakly positive epithelial cells (panel B). These ligands are also detected in the lumen of epididymal tubules (visible for VEGF-C Panel A S2). This presence may be explained by lumicrine transfer from the testis, in addition to secretion from epithelial cells. Here the transgene is detected directly without the use of an anti-GFP which allows to enhance the signal.

5) The study is descriptive and does not provide functional and mechanistic insights. Maybe, the combination of 3D imaging with lineage tracing of endothelium cells or ligation study (removal/ligation of the certain vessel) would help better understand how the vascular network is established and their functional significance.

The technical approaches suggested by the reviewer could certainly improve our understanding of the rather complex epididymal vascular network. Taken together, they represent the body of a comprehensive follow-up study that is worth undertaking.

6) Immune response is among many physiological processes in which vascular networks play significant roles. Discussion would be needed in other physiological processes, such as tissue metabolism and stem/progenitor cell niche microenvironment.

We agree with the reviewer that the mammalian vasculature is involved in other physiological processes beyond immune/inflammatory responses. We have deliberately chosen to focus our discussion on the inflammatory and immune context of the epididymis, as we believe this is the most relevant aspect. It is also in full agreement with the research that our team has been conducting for 15 years to try to understand the complex orchestration of tolerance versus immune surveillance in this territory. This is a finely tuned process that, if properly understood, can help to understand and appropriately treat clinical situations of infertility and/or urological problems. As our discussion section is already quite long, we feel that it was not justified to extend it further on other aspects. However, in response to the reviewer's suggestion, we now mention at the end of the first paragraph of the discussion that the epididymal vascular network is likely to serve different processes in this tissue (page 9, lines 299 to 303).

7) How could the author determine the Cd-A labeled vessel in Fig 1 was an artery, not a vein? This leads to another critical question. Would it be possible to stain with artery and vein markers to help illustrate the blood flow directions of the vessel?

The reviewer is right on the fact that we arbitrarily called the Cd-A vessel in Figure 1 an artery. Cd-A is not an acronym we use anymore. What we have done is to use the acronym SEA (superior epididymal artery) to indicate what we firmly believe to be an artery, as also suggested by previous literature (e.g., Suzuki, 1982; Abe et al, 1982) in which this same structure has been consistently referred to as an artery. For other blood vessels, we now have used the acronym "Cd-BV" because we do not know whether we are dealing with a vein or an artery as rightfully pointed out by the reviewer. This is clearly stated in the legend of Figure 1.

Author Resposnse

Reviewer #2 (Public Review):

This manuscript reassesses the strength of evidence for rapid human germline mutation spectrum evolution, using high coverage whole genome sequencing data and paying particular attention to the potential impact of confounders like biased gene conversion. The authors also refute some recently published arguments that historical changes in the age of reproduction might explain the existence of such mutation spectrum changes. My overall impression is that the paper presents a useful new angle for studying mutation spectrum evolution, and the analysis is nicely suited to addressing whether a particular model such as the parental age model can explain a set of observed polymorphism data. My main criticism is that the paper overstates certain weaknesses of previously published papers on mutation spectrum evolution as well as the generation time hypothesis; correcting these oversimplifications would more accurately capture what the paper's new analyses add to the state of knowledge in these areas.

As part of the motivation for the current study, the introduction states in lines 97-99 that "it thus remains unclear if the numerous observed [mutation spectrum] differences across human populations stem from rapid evolution of the mutation process itself, other evolutionary processes, or technical factors." This seems to overstate the uncertainty that existed prior to this study, given that Speidel, et al. 2021 found elevated TCC>TTC fractions in ancient genomes from a specific ancient European population, which seems like pretty airtight evidence that this historical mutation rate increase really happened. In addition, earlier papers (Harris 2015, Mathieson & Reich 2016, Harris & Pritchard 2017) already presented analyses rejecting the hypothesis that biased gene conversion or genetic drift could explain the reported patterns-in fact, the Mathieson & Reich paper reports one mutation spectrum difference between populations that they conclude is an artifact caused by the Native American population bottleneck, but they conclude that other mutation spectrum differences appear more robust.

We completely agree with the reviewer that there has been compelling evidence from multiple independent groups supporting transient elevation of TCC>TTC mutation rate in Europeans. Beyond the TCC signal, however, the mechanisms underlying the observed differences in mutation spectrum across populations remain unclear. In particular, several biological and technical factors impact the mutation spectrum and none of the previous studies have investigated their effects, independently or altogether. Thus, it remains unclear if the mutation rate is evolving rapidly across populations, or if one or more factors (like biased gene conversion) differ across groups or over evolutionary time. Our analysis framework attempts to control these effects together to more reliably investigate the effects of various factors and examine when and how often there has been evolution of mutation rate over the course of human evolution.

As the authors acknowledge in the discussion of their own results, biased gene conversion and non-equilibrium demography are difficult confounders to deal with, and neither previous papers nor the current paper are able to do this in a way that is 100% foolproof. The current manuscript makes a valuable contribution by presenting new ways of dealing with these issues, particularly since previous papers' work on this topic was often confined to supplementary material, but it seems appropriate to acknowledge that earlier papers discussed the potential impacts of biased gene conversion and demographic complexity and presented their own analyses arguing that these phenomena were poor explanations for the existence of mutation spectrum differences between populations.

For the most part, I found the paper's introduction to be a useful summary of previous work, but there are a few additional places where the limitations of previous work could be described more clearly. I'd suggest noting that the data artifacts discovered by Anderson-Trocmé, et al. were restricted to a few old samples and that the large differences the current manuscript focuses on were never implicated as potential cell line artifacts. In addition, when the authors mention that their new approach includes "minimiz[ing] confounding effects of selection by removing constrained regions and known targets of selection" (lines 106-107), they should note that earlier papers like Harris & Pritchard 2017 also excluded conserved regions and exons.

We agree with the reviewer that some of the previous work also attempted to account for the contributions of selection or other factors in post hoc ways; we now acknowledge this in the Results section more explicitly. However, we note that our contribution is in introducing a framework to account for these effects a priori and then assess if there are differences in mutation spectrum across populations and over the course of human evolution. In particular, an innovation of our framework is to better control for the effect of gBGC, which has not been done in previous studies.

One innovative aspect of the current paper's approach is the use of allele ages inferred by Relate, which certainly has advantages over using allele frequencies as a proxy for allele age. Though the authors of Relate previously used this approach to study mutation spectrum evolution, they did not perform such a thorough investigation of ancient alleles and collapsed mutation type ratios. I like the authors' approach of building uncertainty into the use of Relate's age estimates, but I wonder about the validity of assuming that the allele age posterior probability is distributed uniformly between the upper and lower confidence bounds. Can the authors address why this is more appropriate than some kind of peaked distribution like a beta distribution?

The lower and upper bounds of the allele age reported by Relate reflect the start and end points of the branch that the mutation falls on in the reconstructed genealogical tree. If Relate does a perfect job in reconstructing the tree and estimating the branch lengths, the mutation age should be uniformly distributed in the inferred interval. It is unrealistic that Relate can perform perfectly in tree building, and there is likely considerable uncertainty and even bias in the time to endpoints of the branch. Unfortunately, Relate does not report the uncertainty in the lower and upper bounds of the mutation age, so we were not able to model the posterior distribution of the allele age properly. However, assuming a uniform distribution of the mutation age between the upper and lower confidence bounds should be valid to first approximation.

I would also argue that the statement on line 104 about Relate's reliability is not yet supported by data-there is certainly value in using Relate ages to investigate mutation spectrum change over time and compare this to what has been seen using allele frequencies, but I don't think we know enough yet to say that the Relate ages are definitely more reliable. Relate's estimates might be biased by the same processes like selection and demography that make allele frequencies challenging to interpret. The paper's statements about the limitations of allele frequencies are fair, but there is always a tradeoff between the clear drawbacks of simple summary statistics and the more cryptic possible blind spots of complicated "black box" algorithms (in the case of Relate, an MCMC that needs to converge properly). DeWitt, et al. 2021 noted that the demographic history inferred by Relate doesn't accurately predict the underlying data's site frequency spectrum, indicating that the associated allele ages might have some problems that need to be better characterized. While testing Relate for biases is beyond the scope of this work, the introduction should acknowledge that the accuracy and precision of its time estimates are still somewhat uncertain.

We agree with the reviewer and have now added a paragraph in the Discussion highlighting some issues of Relate regarding mutation age estimation and ancestral allele polarization.

The paper's results on C>T mutations in Europeans versus Africans are a nice confirmation of previous results, including the observation from Mathieson & Reich that neither SBS7 nor SBS11 is a good match for the mutational signature at play. More novel is the ancient mutational signature enriched in Africa and the interrogation of the ability of parental age to explain the observed patterns. I just have a few minor suggestions regarding these analyses:

1) I like the idea of using maternal age C>G hotspots to test the plausibility of the maternal age as an explanatory factor, but I think this would be more convincing with the addition of a power analysis. Given two populations that have average maternal ages of 20 and 40, and the same population sample sizes available from 1000 Genomes, can the authors calculate whether the results they'd predict are any different from what is observed (i.e. no significant differences within the maternal hotspots and significant differences outside of these regions)?

We thank the review for this suggestion. We performed simulations to estimate the power of observing significant inter-population differences within and outside the maternal C>G mutation hotspots, under the assumption that all differences in the mutation spectrum between the two populations are related to the parental age (i.e., generation time). We found that, because of the extraordinarily strong maternal age effects in the maternal mutation hotspots, the power for detecting variation in C>G/T>A ratio due to change in generation age is much greater within maternal hotspots than outside, despite the smaller total size of the maternal hotspot regions (and hence fewer SNPs; Figure 3 – figure supplement 4). For example, even with an age difference of five years, there is nearly 100% power to detect significant differences in the maternal hotspots, compared to <12% for regions outside the maternal hotspots. In other words, if inter-population differences in the mutation spectrum are driven by differences in maternal age across populations, we should have enough power to observe a signal in the maternal hotspot regions alone, the lack of which (Figure 2C) strongly suggests that maternal age is not driving these signals.

2) Is it possible that the T>C/T>G ratio is elevated in all variants above a certain age but shows up as an African-specific signal because the African population retains more segregating variation in this age range, whereas non-African populations have fixed or lost more of this variation? Since Durvasula & Sankararaman identified putative tracts of super-archaic introgression within Africans, is it possible to test whether the mutation spectrum signal is enriched within those tracts?

The observation that the T>C / T>G signal is driven by TpG>CpG mutations (which might be mis-polarized CpG transitions) casts a doubt on the signal. Given the unresolved technical issue, we have now removed any discussion of the biological explanations behind the signal and instead focus on describing the challenges with ancestral allele polarization under context-dependent mutation rate variation.

3) Although Coll Macià, et al. argued that generation time is capable of explaining all mutation spectrum differences between populations, including the excess of TCC>TTC in Europeans, Wang et al. argue something slightly different. They exclude TCC>TTC and the other major components of the European signature from their analysis and then argue that parental age can explain the rest of the differences between populations. I think the analysis in this paper convincingly refutes the Coll Macià, et al. argument, but refuting the Wang, et al. version would require excluding the same mutation types that are excluded in that paper.

Although we did not present an analysis that explicitly excludes TCC>TTC mutations, our analysis still shows that generation time alone cannot explain the remaining variations in the mutation spectrum observed (Figure 4). Specifically, the temporal trend of T>C/T>G ratio would suggest a decreasing generation time of Europeans with time, whereas the C>G/T>A ratio suggests the opposite. In addition, the power analysis for C>G maternal hotspots (suggested by the reviewer) further supports that the inter-population differences observed cannot be entirely driven by differences in parental ages. These observations, which do not involve TCC>TTC mutations, strongly suggest that generation time is not the sole or primary driver of differences in mutation spectrum across populations. Further, our analysis shows that several technical issues and biological processes, in addition to changes in life history traits can lead to changes in the mutation spectrum of polymorphisms. Therefore, inferring generation time using changes in mutation spectrum is not straightforward as Wang et al. proposed, because generation time is not the only or dominant factor impacting mutation spectrum.

Author Response

Reviewer #1 (Public Review):

This is an awesome comprehensive manuscript. Authors start by sorting putative stromal cellcontaining BM non-hematopoietic (CD235a-/CD45-) plus additional CD271+/CD235a/CD45- populations to identify nine individual stromal identities by scRNA-seq. The dual sorting strategy is a clever trick as it enriches for rare stromal (progenitor) cell signals but may suffer a certain bias towards CD271+ stromal progenitors. The lack of readable signatures already among CD45-/CD45- sorts might argue against this fear. This reviewer would appreciate a brief discussion on number & phenotype of putative additional MSSC phenotypes in light of the fact that the majority of 'blood lineage(s)'-negative scRNA-seq signatures identified blood cell progenitor identities (glycophorin A-negative & leukocyte common antigen-negative). The nine stromal cell entities share the CXCL12, VCAN, LEPR main signature. Perhaps the authors could speculate if future studies using VCAN or LEPRbased sort strategies could identify additional stromal progenitor identities?

We would like to thank the reviewer for critically evaluating our work and for the generally positive evaluation of the paper. We apologize for delayed resubmission as it took a long time for a specific antibody to arrive to complete the confocal microscopy analyses.

The reviewer asks for a brief discussion on the cell numbers and phenotypes of MSSC phenotypes. The cell numbers and percentages of MSSC in sorted CD45low/-CD235a- and CD45low/-CD235a-CD271+ cells can be found in Supplementary File 3 and we have added a summary of the phenotypes of MSSC in the new Supplementary File 7.

Due to the extremely low frequency of stromal cells in human bone marrow, we chose a sorting strategy that also included CD45low cells (Fig 1A) to ensure that no stromal cells were excluded from the analysis. Although stromal elements are certainly enriched using this approach, the CD45low population contains several different hematopoietic cell types. These include CD34+ HSPCs which are characterized by low CD45 expression2, as well as the CD45low-expressing fractions of other hematopoietic cell populations such as B cells, T cells, NK cells, megakaryocytes, monocytes, dendritic cells, and granulocytes. Furthermore, CD235a- late-stage erythroid progenitors, which are negative for CD45, are represented as well. Of note, our data are consistent with previously reported murine studies showing the presence of a number of hematopoietic populations in CD45- cells, which accounted for the majority of CD45-Ter119-CD31- murine BM cells3,4. However, despite a certain enrichment of stromal elements in the CD45low cell fraction, frequencies were still too low to allow for a detailed analysis of this important bone marrow compartment. This prompted us to adopt the stromal cell-enrichment strategy as described in the manuscript to achieve a better resolution of the stromal compartment. In fact, sorting based on CD45low/-CD235a-CD271+ allowed us to sufficiently enrich bone marrow stromal cells to be clearly detectable in scRNAseq analysis. According to the reviewer’s suggestion, a brief discussion on this issue is now included in the Discussion (page 28, lines 10-15).

The reviewer also suggested using VCAN or LEPR-based sorting strategy to identify additional stromal identities in future studies.

However, as an extracellular matrix protein, FACS analysis of cellular VCAN expression can only be achieved based on its intracellular expression after fixation and permeabilization5,6. Additionally, while VCAN is highly and ubiquitously expressed by stromal clusters, VCAN is also expressed by monocytes (cluster 36). Therefore, VCAN is not an optimal marker to isolate viable stromal cells.

LEPR is the marker that was reported to identify the majority of colony-forming cells in adult murine bone marrow7. We have previously reported that the majority of human adult bone marrow CFU-Fs is contained in the LEPR+ fraction 8. In our current scRNAseq surface marker profiling analysis, group A cells showed high expression of several canonical stromal markers including VCAM1, PDGFRB, ENG (CD73), as well as LEPR (Fig. 4A). However, the four stromal clusters in Group A could not be separated based on the expression of LEPR. Therefore, we chose not to use LEPR as a marker to prospectively isolate the different stromal cell types.

The authors furthermore localized CD271+, CD81+ and NCAM/CD56+ cells in BM sections in situ. Finally, referring to the strong background of the group in HSC research, in silico prediction by CellPhoneDB identified a wide range of interactions between stromal cells and hematopoietic cells. Evidence for functional interdependence of FCU-F forming cells is completing the novel and more clear bone marrow stromal cell picture.

We thank the reviewer for the positive comments.

An illustrative abstract naming the top9 stromal identities in their top4 clusters by their "top10 markers" + functions would be highly appreciated.

We thank the reviewer for the suggestion. A summary of the characteristics of stromal clusters is now shown in the new Supplementary File 7, which we hope matches the reviewer’s expectations.

Reviewer #2 (Public Review):

Knowledge about composition and function of the different subpopulations of the hematopoietic niche of the BM is limited. Although such knowledge about the mouse BM has been accumulating in recent years, a thorough study of the human BM still needs to be performed. The present manuscript of Li and coworkers fills this gap by performing single cell RNA sequencing (scRNAseq) on control BM as well as CD271+ BM cells enriched for non-hematopoietic niche cells.

We apologize for delayed resubmission as it took a long time for a specific antibody to arrive to complete the confocal microscopy analyses. We thank the reviewer for the critical expert review and overall positive comments.

Based on their scRNAseq, the authors propose 41 different BM cell populations, ten of which represented non-hematopoietic cells, including one endothelial cell cluster. The nine remaining skeletal subpopulations were subdivided into multipotent stromal stem cells (MSSC), four distinct populations of osteoprogenitors, one cluster of osteoblasts and three clusters of pre-fibroblasts. Using bioinformatic tools, the authors then compare their results and divisions of subpopulations to some previously published work from others and attempt to delineate lineage relationships using RNA velocity analyses. From these, they propose different paths from which MSSC enter the progenitor stages, and might differentiate into pre-osteoblasts and -fibroblasts.

It is of interest to note, that apparently adipo-primed cells may also differentiate into osteolineage cells, something that should be further explored or validated. Furthermore, although this analysis yields a large adipo-primed populations, pre-adipocytes and mature adipocytes appear not to be included in the data set the authors used, which should also be explained.

We thank the reviewer for this comment. We chose to annotate Cluster 5 as adipoprimed cluster based on the higher expression of adipogenic differentiation markers as well as a group of stress-related transcription factors (FOS, FOSB, JUNB, EGR1) (Fig. 2B-C, Figure 2-figure supplement 1C) some of which had been shown to mark bone marrow adipogenic progenitors1. Although at considerably lower levels compared to adipogenic genes, osteogenic genes were also expressed in cluster 5 cells (Fig. 2B and D), indicating the multi-potent potential of this cluster. Therefore, our initial annotation of these cells as adipoprimed progenitors was too narrow as it did not include the possible osteogenic differentiation potential. We apologize for the confusion caused by the inappropriate annotation and, in order to avoid any further confusion, cluster 5 has now been re-annotated as ‘highly adipocytic gene-expressing progenitors (HAGEPs), which we believe is a better representation of the cells. We furthermore agree with the reviewer that in-vivo differentiation needs to be performed to address potential differentiation capacities in future studies.

With regard to the lack of adipocytes in our data set, we described in the Materials and Methods section that human bone marrow cells were isolated based on density gradient centrifugation. After centrifugation, the mononuclear cell-containing monolayers were harvested for further analysis. However, the resulting supernatant containing mature adipocytic cells was discarded14. Therefore, adipocyte clusters were not identified in our dataset. We have amended the manuscript accordingly (page 5, line 7).

Regarding the pre-adipocytes, we are not aware of any specific markers for pre-adipocytes in the bone marrow. We examined the only known markers (ICAM1, PPARG, FABP4) that have been shown to mark committed pre-adipocytes in human adipose tissue15. As illustrated in Fig. R1 (below), low expression of all three markers was not restricted to a single distinct cluster but could be found in almost all stromal clusters. These data thus allow us to neither confirm nor exclude the presence of pre-adipocytes in the dataset. Due to the lack of specific markers for pre-adipocytes and the absence of mature adipocytes in the current dataset, it is therefore difficult to identify a well-defined pre-adipocytes cluster.

Figure R1. UMAP illustration of the normalized expression of the markers for pre-adipocytes in stromal clusters.

In addition, based on a separate analysis of surface molecules, the authors propose new markers that could be used to prospectively isolate different human subpopulations of BM niche cells by using CD52, CD81 and NCAM1 (=CD56). Indeed, these analyses yield six different populations with differential abilities to form fibroblast-like colonies and differentiate into adipo-, osteo-, and chondrogenic lineages. To explore how the scRNAseq data may help to understand regulatory processes within the BM, the authors predict possible interactions between hematopoietic and non-hematopoietic subpopulations in the BM. These should be further validated, to support statements as the suggestion in the abstract that separate CXCL12- and SPP1-regulated BM niches might exist.

We agree with the reviewer that functional validation of the CellPhoneDB results using for example in vivo humanized mouse models would be needed to demonstrate the presence of different niches in the bone marrow. At this point of time we only put forward the hypothesis that different niche types exist while we will work on providing experimental proof in our future studies.

The scRNAseq analysis is indeed a strong and important resource, also for later studies meant to increase knowledge about the hematopoietic niche of the BM. Although the analyses using different bioinformatic tools is very helpful, they remain mostly speculative, since validatory experiments, as already mentioned, are missing. As such, I feel the authors did not succeed in achieving their goals of understanding how non-hematopoietic cells of the BM regulate the different hematopoietic processes within the BM. Nevertheless, they have created valuable resources, both in the scRNAseq data they generated, as well as the different predictions about different cell populations, their lineage relationships, and how they might interact with hematopoietic cells.

We thank the reviewer for the appreciation of the value of this dataset. We agree with the reviewer that it is of great importance to validate the contribution of potential driver genes for stromal cell differentiation and verify the in vitro data and in-silico prediction using in-vivo models. As the main goal of the current study was to formulate hypotheses based on the scRNAseq data for future studies, we believe that in vivo validation experiments using engineered human bone marrow models or humanized bone marrow ossicles are out of the scope of the current study, but certainly need to be performed in the future.

The impact of this work is difficult to envision, since validations still need to be performed. Also, it has the born in mind that humans are not mice, which can be studied in neat homogeneous inbred populations. Human populations on the other hand, are quite diverse, so that the data generated in this manuscript and others will probably have to be combined to extrapolate data relevant to the whole of the human population. However, as it is equally difficult to generate reliable scRNAseq data from human BM, it seems likely that the data will indeed an important resource, when more data from different donors become available.

We thank the reviewer for the generally positive evaluation of this study.

Taken at point value, the authors provide evidence that human counterparts exist to several BM populations described in mice. In my opinion, the lineage relationships predicted using the RNA velocity analyses need more substance, as it seems the differentiation-paths may diverge from what is known from mice. If so, this issue should be studied more stringently. Similarly, the paper would have been strengthened considerably if a relevant experimental validation would have been attempted, perhaps by using genetically modified (knockdown) MSSC, similar to Battula et al. (doi: 10.1182/blood-2012-06-437988).

In the study from Welner’s group, stromal differentiation trajectory was inferred based on scRNAseq analysis of murine bone marrow cells using Velocyto16. Velocyto identified MSCs as the ‘source’ cell state with pre-adipocytes, pro-osteoblasts, and prochondrocytes being end states. In our study, the MSSC population was predicted to be at the apex of the trajectory and the pre-osteoblast cluster was placed close to the terminal state of differentiation, which is consistent with the murine study. However, different stromal cell types were identified in mice compared with humans. For example, we have identified prefibroblasts in our dataset which are absent in the murine study, while a well-defined murine pre-adipocyte population was not identified in our human dataset. Therefore, it is not surprising to find some discrepancies between human and murine stromal differentiation trajectories. Of course and as mentioned before, critical in-vivo functional validations need to be carried out to address these important issues in the future.

In summary, this is a very interesting but also descriptive paper with highly important resources. However, to prospectively identify or isolate human non-hematopoietic/nonendothelial niche populations, more stringent validations should have been performed to strengthen the validity of the different analyses that have been performed. As such, it remains an open question which niche subpopulations has the most impact on the different hematopoietic processes important for normal and stress hematopoiesis, as well as malignancies.

Thank you for this comment. We completely agree that more stringent validations are necessary but are outside of the aim of our current hypothesis-generating study. Accordingly, we are planning functional verification studies using genetically manipulated stromal cells in combination with in-vivo humanized ossicles. Furthermore, other groups will hopefully use our database and contribute with functional studies in model systems that are currently not available to us, e.g. iPS-derived bone marrow in-vitro proxies.

Specific remarks

• Since CD45, CD235a, and CD271 are used as distinguishing markers in the sample preparation of the scRNAseq, it would be helpful to highlight these markers in the different analyses (Figures 1D, 2B, 2C-F, and 4A), and restrict the analyses to those cells that also not express CD45, CD235a (why use CD71?) and highly express CD271.

Thank you for this comment. As shown in Fig. R2, we have modified figures Fig. 1D, 2B, and 4A showing now also the expression of PTPRC (CD45), GYPA (CD235a), and NGFR (CD271) on the top (Fig. 1D and 2B) or right (Fig. 4A) panel of the figures. To complement Fig. 2C-F, we have generated new stacked violin plots showing the expression level of three markers by all 9 stromal clusters (Fig. R2B). As we believe that including these three markers in the figures does not provide a better strategy to improve the analyses, we decided to leave the original figures unchanged in this respect.

Figure R2. (A) Modified Fig. 1D, 2B and 4A with PTPRC (CD45), GYPA (CD235a) and NGFR (CD271) expression. (B) Stacked violin plots of PTPRC, GYPA and NGFR expressed by stromal clusters to complement Fig. 2C-F.

With regard to cell exclusion based on CD45, as shown in the modified Figure corresponding to Fig 1A in the manuscript (Fig R2A), CD45 gene expression is observed also in the endothelial cluster, basal cluster, and neuronal cluster (Fig. R2A). These clusters represent non-hematopoietic clusters that we would like to keep in our dataset for further analysis, such as cell-cell interaction. Therefore, we choose to not restrict the analysis to solely CD45 nonexpressing cells.

With regard to CD235a (GYPA), expression of CD235a is not detected in any of the nonhematopoietic clusters. Thus, CD235a-expressing cell exclusion is not necessary.

For CD271, according to our previous results (own unpublished data, belonging to a dataset of which only significantly expressed genes were reported in Li et al.8), protein expression of CD271 is not necessarily reflected by gene expression. In the other words, stromal cells with CD271 protein expression do not always have high mRNA expression. A significant fraction of stromal cells would be excluded if we restrict the analyses only to those cells that show high CD271 gene expression, which would not reflect the real cellular composition of human bone marrow stroma. In order to not risk losing stromal cells, we therefore kept our previous analyses which included stromal cells with various CD271 expression levels.

With regard to using CD71 as an exclusion marker, please see also the comments to reviewer 1. Briefly, according to our data, CD71 (TFRC)-expressing erythroid precursors could still be found after excluding CD45 and CD235a positive cells (Figure 1-figure supplement 1B and R3). As furthermore shown in Figure 1-figure supplement 1G and R2, CD71 expression in the stromal clusters is negligible. Therefore, we believe that this justifies the use of CD71 as an additional marker to exclude erythroid cells. We have amended the discussion to address this issue (page 19, lines 7-8).

Figure R3. FACS plots illustrating the expression of (A) CD71 (TFRC) vs CD271 in CD45- CD235a- cells and (B) FSC-A vs CD81 in CD45-CD235a-CD271+CD71+ cells following exclusion of doublets and dead cells.

• Despite a distinct neuronal cluster (39), there does not seem to be a distinctive marker for these cells. Is this true?

Yes, the reviewer is correct that there is no significantly-expressed distinctive marker for neuronal cells. Multiple markers indicating the presence of different cell types were identified in cluster 39 (Supplementary File 4). Among them, several neuronal markers (NEUROD1, CHGB, ELAVL2, ELAVL3, ELAVL4, STMN2, INSM1, ZIC2, NNAT) were found to be enriched in this cluster (Supplementary File 4 and Fig. 1D) with higher fold changes compared to other identified genes. However, the expression of these genes was not statistically significant, which is mainly due to the heterogeneity of the cluster and thus does not allow us to draw any firm conclusions.

Several genes including MALAT1, HNRNPH1, AC010970.1, and AD000090.1 were identified to be statistically highly expressed by cluster 39 (Supplementary File 4). The expression of these genes is not restricted to any specific cell type. It is therefore impossible to annotate the cluster based on this and our data thus indicated that cluster 39 is a heterogeneous population containing multiple cell types. Based on the expression of neuronal markers, we nevertheless chose to annotate Cluster 39 as “neuronal” as the prominent expression of neuronal markers indicated the presence of neurons in this cluster. To be more accurate, the annotation of cluster 39 has been changed to ‘neuronal cell-containing cluster’ to correctly reflect the presence of non-neuronal gene expressing cells as well (page 29, lines 3-8).

• Since based on 2C and 2D, the authors are unable to distinguish adipo- from osteogenic cells, would the authors use the same molecules to distinguish different populations of 2C-D, or would they use other markers, if so which and why.

We agree with the reviewer that at the first glance adipo-primed (cluster 5, now annotated as “highly adipocytic gene-expressing progenitors”, HAGEPs), balanced progenitors (cluster 16), and pre-osteoblasts (cluster 38) shared a similar expression pattern according to the violin plots in Fig. 2C and 2D. However, as illustrated in the heatmap (Fig. 2B), the expression patterns of adipo-primed (HAGEP) and balanced progenitors were quite different in terms of their expression of adipogenic and osteogenic markers. Both adipogenic and osteogenic marker expression was detected in HAGEPs, balanced progenitors, and preosteoblasts. Thus, as violin plots are summarizing the overall expression levels of a certain marker in a certain cluster, these plots tend to make it more difficult to detect differential expression patterns between different clusters. In this case, the heatmap shown in Fig. 2B is a good complement to the violin plots as it is demonstrating the different expression patterns of every cell in the different stromal clusters.

Additionally, cluster 5 showed the expression of a group of stress-related transcription factors (FOS, FOSB, JUNB, EGR1) (Fig. 2B and Figure 2-figure supplement 1C), some of which had been shown to mark bone marrow adipogenic progenitors1. The expression of the abovementioned stress-related transcription factors (putative adipogenic progenitor markers) was generally lower in cluster 38 compared to cluster 5, further demonstrating that clusters were different.

Furthermore, there was a gradual upregulation of more mature osteogenic markers such as RUNX1, CDH11, EBF1, and EBF3 from cluster 5 to cluster 16 and finally cluster 38. As shown in Fig. 2D, the expression of these markers was higher in cluster 38 compared to cluster 5. Therefore, cluster 38 was annotated as pre-osteoblasts.

Most of the stromal clusters form a continuum (Fig. 2A), which correlates very well with the gradual transition of different cellular states during stromal cell development. It is highly unlikely that abrupt and dramatic gene expression changes would occur during the cellular state transition of cells of the same lineage. Therefore, it is not surprising to find the differences in gene expression profiles between stromal clusters share a certain level of similarities.

In summary, we rely on several factors to distinguish different stromal clusters, which include canonical adipo-, osteo- and chondrogenic markers, stress markers, heatmap, violin plots, and the gradual up-regulation of certain lineage-specific markers.

To directly answer the reviewer’s question, we believe that we are able to distinguish different stromal clusters based on our data.

• In de Jong et al., an inflammatory MSC population (iMSC) is defined. Since the Schneider group showed that inflammatory S100A8 and A9 are expressed by inflamed MSC, is it possible that the some of the designated pre-fibroblasts actually correspond to these S100A8/A9-expressing iMSC?

We thank the reviewer for raising this interesting question.

First of all, we would like to point out that scRNAseq was performed using viably frozen bone marrow aspirates in de Jong’s study while freshly isolated bone marrows were used in our study. There might be discrepancies between frozen and fresh bone marrow samples in terms of cellular composition including stromal composition and, importantly, processinginduced stress-related gene expression profiles.

To investigate if designated pre-fibroblasts actually correspond to iMSCs as suggested by the reviewer, we have re-examined the expression of some of the key iMSC genes as reported by de Jong et al 17. As shown in Fig. R6, the markers that can distinguish iMSC from other MSC clusters in de Jong et al. study were not exclusively expressed by pre-fibroblasts, but also by other stromal cell types including HAGEPs, balanced progenitors, and pre-osteoblasts.

In the study by R. Schneider’s group18, significant upregulation of S100A8/S100A9 was observed in stromal cells from patients with myelofibrosis. Furthermore, base-line expression of S100A8/A9 was also observed in the fibroblast clusters in the control group, which correlates very well with our data of S100A8/9 expression in pre-fibroblasts in normal donors (Fig. 2F). Our data thus indicate – in line with Schneider’s findings - that there is a baseline level expression of S100A8/9 in fibroblasts in hematologically normal samples and that the expression of S100A8/9 is not restricted to inflamed MSC.

In summary, the gene expression profiles observed in our study do not indicate the presence of iMSC in the healthy bone marrow.

• Figure 3A: Do human adipo-primed cells (cluster 5) indeed differentiate into osteogenic cells (clusters 6, 38, and 39). This would be highly unexpected. Can the authors substantiate this "reliable outcome of the RNA velocity analysis"?

Please refer to our previous responses regarding this topic. Briefly, as shown in Fig. 2B and D, both osteogenic and adipogenic genes are expressed in cluster 5, indicating the multi-potent potentials of this cluster. Although the cluster was initially annotated as adipo-primed progenitors, this was not intended to exclude the osteogenic differentiation potential of these progenitors. Nevertheless, this annotation did not correctly reflect the differentiation potential and might thus have caused confusion, for which we apologize. In order to more correctly describe the characteristics of these cells, cluster 5 has now been reannotated as ‘highly adipocytic gene-expressing progenitors (HAGEPs)’.

In general, the outcome of the RNA velocity analysis needs to be corroborated by in-vivo differentiation experiments. But we believe that functional verification, which would be extensive, is out of the scope of the current study and we will address these questions in future studies.

• How statistically certain are the authors, that the populations in Figure 4B as defined by flow cytometry, correspond to MSSC, adipo-primed cells, osteoprogenitors, etc., as defined by scRNAseq?

To address this question, we sorted the A1-A4 populations and performed RT- PCR to examine the CD81 expression level in each cluster. As shown in Figure 4-figure supplement 1B, CD81 expression levels were higher in A1 and A2 compared with A3 and A4, which is consistent with the scRNAseq data that showed the highest CD81 expression in MSSCs compared to other clusters (Supplementary File 4).

The phenotypes defined in this study allowed us to isolate different stromal cell types which demonstrated significant functional differences as described in the manuscript (page 19, lines 17-25; page 20, lines 1-11). These results, in combination with the quantitative real-time PCR results (Figure 4-figure supplement 1B), demonstrated that the A1-A4 subsets in FACS are functionally distinct populations and are likely to be – at least in large parts – identical or equivalent to the transcriptionally identified clusters in group A stromal cells. However, at this point, we do not have performed the required experiments (scRNAseq of sorted cells) that would provide sufficient proof to confirm this statement statistically.

• The immunohistochemistry results shown do not allow distinct conclusions as the colors give unequivocal mix-colors, and surface expression cannot be distinguished from intracellular expression. Please use a 3D (confocal) method for such statements.

We thank the reviewer for the suggestion and we have performed additional confocal microscopy analysis of human bone marrow biopsies as suggested by the reviewer. Representative confocal images are now presented in the middle and right panel of Fig. 6E. We also include a separate file (Supplemental confocal image file). Here, confocal scans of all maker combinations are shown as ortho views in addition to detailed intensity profile analyses of the cells of interest clearly distinguishing surface staining from intracellular staining.

Confocal analysis of bone marrow biopsies confirmed our findings presented in the manuscript. As observed in the scanning images, CD271-expressing cells were negative for CD45 and were located in perivascular, endosteal, and peri-adipocytic regions. CD271/CD81double positive cells could be found either in the peri-adipocytic regions or perivascular regions while CD271/NCAM1 double-positive cells were exclusively situated at the bone-lining endosteal regions. The results of the confocal analysis have been added to the revised manuscript (page 21, lines 15-17).

• Figure 5A: as all cells seem to interact with all other cells, this figure does not convey relevant information about BM regions using for instance CXCL12 or SPP1. Please reanalyze to show specificity of the interactions of the single clusters. Also, since it is unlikely the CellPhoneDB2-predicted interactions are restricted to hematopoietic responders, please also describe the possible interactions between non-hematopoietic cells.

Fig. 5A was used to demonstrate the complexity of the interactions between hematopoietic cells and stromal cells.

To gain a more detailed understanding of the interactions, we also performed an analysis with the top-listed ligand-receptor pairs as shown in Fig. 5B-C and Figure 5-figure supplement 1B. Here, each dot represents the interaction of a specific ligand-receptor pair listed on the x-axis between the two individual clusters indicated in the y-axis, which we believe shows what the reviewer is asking for.

The specificity of the interactions between single clusters were shown in Fig. 5B-C and Figure 5-figure supplement 1B. The CXCL12- and SPP1-mediated interactions between MSSC/OC and hematopoietic clusters clearly suggested stromal cell type-specific interactions.

Regarding non-hematopoietic cells, both inter- and intra-stromal interactions were identified to be operative between different stromal subsets as well as within the same stromal cell population as shown in Figure 5-figure supplement 3B. In addition, we have also analyzed the interaction pattern between endothelial cells and hematopoietic cells as shown in Fig. 7A, and thus we believe that we have sufficiently described these interactions as requested by the reviewer.

Author Response

Reviewer #2 (Public Review):

This study identifies the neural circuits inhibited by activation of opioid receptors using complex experimental approaches such as electrophysiology, pharmacology, and optogenetics and combined them with retrograde and anterograde tracings. The authors characterize two key regions of the brainstem, the preBötzinger Complex, and the Kolliker-Fuse, and how these neuronal populations interact. Understanding the interactions of these circuits substantially increases our understanding of the neural circuits sensitive to opioid drugs which are critical to understand how opioids act on breathing and potentially design new therapies.

Major strengths.

This study maps the excitatory projections from the Kolliker-Fuse to the preBötzinger Complex and rostral ventral respiratory group and shows that these projections are inhibited by opioid drugs. These Kolliker-Fuse neurons express FoxP2, but not the calcitonin gene-related peptide, which distinguishes them from parabrachial neurons. In addition, the preBötzinger Complex is also hyperpolarized by opioid drugs. The experiments performed by the authors are challenging, complex, and the most appropriate types of approaches to understanding pre- and post-synaptic mechanisms, which cannot be studied in vivo. These experiments also used complex tracing methods using adenoassociated virus and cre-lox recombinase approaches.

Limitations.

(1) The roles of the mechanisms identified in this study have not been established in models recording opioid-induced respiratory depression or respiratory activity. This study does not record, modulate, or assess respiratory activity in-vitro or in-vivo, without or with opioid drugs such as fentanyl or morphine.

(2) Experiments are performed in-vitro which do not mimic the effects of opioids observed in-vivo or in freely-moving animals. However, identification of pre- and post- synaptic mechanisms, as well as projections, cannot be performed in-vivo, so the authors use the right approaches for their experiments.

We agree with both of these points. We hope this study lays the groundwork for future studies assessing the impact of these projections on respiratory activity in vitro and in vivo.

(3) The type of neurons projecting from KP to preBötzinger Complex or ventral respiratory group have not been identified. Although some of these cells are glutamatergic, optogenetic experiments could have been performed in other cre-expressing cell populations, such as neurokinin-1 receptors.

There are indeed many different cell populations that could be interrogated. In addition to the optogenetic identification of glutamatergic projections, we identified immunohistochemically that at least some opioid receptor-expressing, medullary-projecting KF neurons express FoxP2, and not CGRP. Further dissection of other cell populations, such as Lmx1b and Phox2b, are excellent future directions.

Reviewer #3 (Public Review):

This manuscript reveals opioid suppression of breathing could occur via multiple mechanisms and at multiple sites in the pontomedullary respiratory network. The authors show that opioids inhibit an excitatory pontomedullary respiratory circuit via three mechanisms: 1) postsynaptic MOR-mediated hyperpolarization of KF neurons that project to the ventrolateral medulla, 2) presynaptic MOR mediated inhibition of glutamate release from dorsolateral pontine terminals onto excitatory preBötC and rVRG neurons, and 3) postsynaptic MOR-mediated hyperpolarization of the preBötC and rVRG neurons that receive pontine glutamatergic input.

This manuscript describes in detail a useful method for dissecting the relationship between the dorsolateral pons and the rostral medulla, which will be useful for various researchers. It's also great to see how many different methods have been applied to improve the accuracy of the results.

1. Relationship between the dorsolateral pons and rostral ventrolateral medulla.

The method of this paper is a good paper to show a very precise relationship between the presence of opioid receptors and the dorsolateral pons and rostral ventrolateral medulla, and for opioid receptors, based on the expression of Oprm1, the use of genetically modified mice with anterograde or retrograde viruses with additional fluorescent colors showed both anterograde and retrograde projections, revealing a relationship between the dorsolateral pons and rostral ventrolateral medulla.

For example, to visualize dorsal pontine neurons expressing Oprm1, Oprm1Cre/Cre mice were crossed with Ai9tdTomato Cre reporter mice to generate Ai9tdT/+ oprm1Cre/+ mice (Oprm1Cre/tdT mice) expressing tdTomato on neurons that also express MOR at any point during development, and the retrograde virus encoding Cre-dependent expression of GFP (retrograde AAV-hSIN-DIO-eGFP was injected into the respiratory center of Oprm1Cre/+ mice and into the ventral respiratory neuron group, showing that KF neurons expressing Oprm1 project to the respiration-related nucleus of the ventrolateral medulla.

However, although the authors have also corrected it, the virus may spread to other places as well as where they thought it would be injected, and it is important to note that it is injected accordingly to mark the injection site with an anterograde virus encoding a different fluorescent color mCherry, and the extent of the injection is quantified, which is excellent as a control experiment.

In addition, the respiratory center seems to be related not only to preBötC but also to pFRG recently, so if the relation with it is described, it is important from the viewpoint of the effect on the respiratory center and the effect on the rhythm.

Our injections centered in preBotC, rVRG or BötC did not spread extensively to slices containing 7N/pFRG (Figure 2C and Figure 2-supplement 1D, Bregma -6.0 to -6.4, shaded region labeled 7N).

Author Response:

eLife assessment

This manuscript analyzes large-scale Neuropixels recordings from visual areas and hippocampus of mice passively viewing repeated clips of a movie and reports that neurons respond with elevated firing activities to specific, continuous sequences of movie frames. The important results support a role of rodent hippocampal neurons in general episode encoding and advance understanding of visual information processing across different brain regions. The strength of evidence for the primary conclusion is solid, but some technical limitations of the study were identified that merit further analyses.

We thank the editors and reviews for the assessment and reviews. We have provided clarifications and updated the manuscripts to address the seeming technical limitations that are perhaps due to some misunderstanding, please see below. We provide additional results that isolate the contribution of pupil diameter, sharpwave ripple and theta power to show that movie tuning cannot be explained by these nonspecific effects. Nor are these mere time cells or some other internally generated patterns due to many differences highlighted below.

Reviewer #1 (Public Review):

Taking advantage of a publicly available dataset, neuronal responses in both the visual and hippocampal areas to passive presentation of a movie are analyzed in this manuscript. Since the visual responses have been described in a number of previous studies (e.g., see Refs. 11-13), the value of this manuscript lies mostly on the hippocampal responses, especially in the context of how hippocampal neurons encode episodic memories. Previous human studies show that hippocampal neurons display selective responses to short (5 s) video clips (e.g. see Gelbard-Sagiv et al, Science 322: 96-101, 2008). The hippocampal responses in head-fixed mice to a longer (30 s) movie as studied in this manuscript could potentially offer important evidence that the rodent hippocampus encodes visual episodes.

We have now included citations to Gelbard-Sagiv et al. Science 2008 paper and many other references too, thank you for pointing that out. There are major differences between that study and ours.

• The movies used in previous study contained very familiar, famous people and famous events, and the experiment was about the patient’s ability to recall those famous movie episodes. In our case the mice had seen this movie clip only twice before.

• They did not look at the fine structure of neural responses below half a second whereas we looked at the mega-scale representations from 30ms to 30s.

• The movie clips in that study were in full color with audio, we used an isoluminant, black-and-white, silent movie clip.

• Their movie clips contained humans and was observed by humans, whereas our study mice observed a movie clip with humans and no mice or other animals.

The analysis strategy is mostly well designed and executed. A number of factors and controls, including baseline firing, locomotion, frame-to-frame visual content variation, are carefully considered. The inclusion of neuronal responses to scrambled movie frames in the analysis is a powerful method to reveal the modulation of a key element in episodic events, temporal continuity, on the hippocampal activity. The properties of movie fields are comprehensively characterized in the manuscript.

Thank you.

Although the hippocampal movie fields appear to be weaker than the visual ones (Fig. 2g, Ext. Fig. 6b), the existence of consistent hippocampal responses to movie frames is supported by the data shown. Interestingly, in my opinion, a strong piece of evidence for this is a "negative" result presented in Ext. Fig. 13c, which shows higher than chance-level correlations in hippocampal responses to same scrambled frames between even and odd trials (and higher than correlations with neighboring scrambled frames). The conclusion that hippocampal movie fields depend on continuous movie frames, rather than a pure visual response to visual contents in individual frames, is supported to some degree by their changed properties after the frame scrambling (Fig. 4).

Yes, hippocampal selectivity is not entirely abolished with scrambled movie, as we show in several figures (Fig 4d,g and Extended Data Fig. 16), but it is greatly reduced, far more than in the afferent visual cortices. The fraction of tuned cells for scrambled movies dropped to 4.5% in hippocampus, which is close to the chance level of 3%. In contrast, in visual areas selectivity was still above 80%.

Significant overlap between even and odd trials is to be expected for the tuned cells. Without a significant overlap, i.e. a stable representation, they will not be tuned. Despite this, the correlation between even and odd trials for the (only 4.5% of) tuned cells in the hippocampus was more than 2-fold smaller than (more than 80% of) cells in visual cortices. This strongly supports our hypothesis that unlike visual cortices, hippocampal subfields depended very strongly on the continuity of visual information. We will clarify this in the main text.

However, there are two potential issues that could complicate this main conclusion.

One issue is related to the effect of behavioral variation or brain state. First, although the authors show that the movie fields are still present during low-speed stationary periods, there is a large drop in the movie tuning score (Z), especially in the hippocampal areas, as shown in Ext. Fig. 3b (compared to Ext. Fig. 2d). This result suggests a potentially significant enhancement by active behavior.

There seems to be some misunderstanding here. There was no major reduction in movie tuning during immobility or active running. As we wrote in the manuscript, the drop in selectivity during purely immobile epochs is because of reduction in the amount of data, not reduction in selectivity per se. Specifically, as the amount data reduces, the statistical strength of tuning (z-scored sparsity) reduces. For example, if we split the total of 60 trials worth of data into two parts, the amount of data reduces to about half in each part, leading to a seeming reduction in selectivity in both halves. Extended figure 2B shows nearly identical tuning in all brain regions during immobility and equivalent subsamples chosen randomly from the entire data, including mobility and immobility. We will include additional data in the revised manuscript to demonstrate this more clearly. Please see below for more details.

Second, a general, hard-to-tackle concern is that neuronal responses could be greatly affected by changes in arousal or brain state (including drowsy or occasional brief slow-wave sleep state) in head-fixed animals without a task. Without the analysis of pupil size or local field potentials (LFPs), the arousal states during the experiment are difficult to know.

In the revised manuscript we will that the behavioral state effects cannot explain movie tuning. Specifically:

• We compare sessions in which the mouse was mostly immobile versus sessions in which the mouse was mostly running. Movie tuned cells were found in both these cases (Extended Data Fig. 7).

• b. We detect and remove all data around sharp-wave ripples (SWR). Movie tuning was unchanged in the remaining data.

• c. As a further control, we quantified arousal by two standard metrics. First within a session, we split the data into two groups, segments with high theta power and segments with low theta power. Significant movie tuning persisted in both.

• d. Finally, pupil dilation is another common method to estimate arousal, so data within a session were split into two parts: those with pupil dilation versus constriction. Movie tuning remained significant in both parts. See the new Extended Data Fig. 7.

Many example movie fields in the presented raw data (e.g., Fig. 1c, Ext. Fig. 4) are broad with low-quality tuning, which could be due to broad changes in brain states. This concern is especially important for hippocampal responses, since the hippocampus can enter an offline mode indicated by the occurrence of LFP sharp-wave ripples (SWRs) while animals simply stay immobile. It is believed that the ripple-associated hippocampal activity is driven mainly by internal processing, not a direct response to external input (e.g., Foster and Wilson, Nature 440: 680, 2006). The "actual" hippocampal movie fields during a true active hippocampal network state, after the removal of SWR time periods, could have different quantifications that impact the main conclusion in the manuscript.

We included the broadly tuned hippocampal neurons to demonstrate the movie-field broadening compared to those in visual areas. We will include more examples with sharp movie fields in the hippocampal regions (Main figure 1a-d right column, 2d and h, Extended Data Fig 5 and 8). Further, as stated above, we detected sharp-wave ripples and removed one second of data around SWR. Move tuning was unchanged in the remaining data. Thus, movie tuning is not generated internally via SWR (Extended Data Fig. 6). See also Extended Data 7 and 8 and the response above.

Another issue is related to the relative contribution of direct visual response versus the response to temporal continuity in movie fields. First, the data in Ext. Fig. 8 show that rapid frame-to-frame changes in visual contents contribute largely to hippocampal movie fields (similarly to visual movie fields).

There seems to be some misunderstanding here. That figure showed that the frame-toframe changes in the visual content had the highest effect on visual areas MSUA and much weaker in hippocampus (Extended Data Fig. 8, as per previous version). For example, the depth of modulation (max – min) / (max + min) for MSUA was 21% and 24% for V1 but below 6% for hippocampal regions. Similarly, the MSUA was more strongly (negatively) correlated with F2F correlation for visual areas (r=0.48 to 0.56) than hippocampal (0.07 to 0.3). Similarly, comparing the number of peaks or their median widths, visual regions showed stronger correlation with F2F, and largest depth of modulation than hippocampal regions, barring handful exceptions (like CA3 correlation between F2F and median peak duration). This strongly supports our claim that visual regions generated far greater response of the frame-to-frame changes in the movie than hippocampal regions.

Interestingly, the data show that movie-field responses are correlated across all brain areas including the hippocampal ones.

The changes in multiunit activity are strongly correlated only between visual areas and some of the hippocampal region pairs. The correlation is much weaker for hippocampal areas, or hippocampal-visual area pairs. This will be quantified explicitly in the revised text Extended Data Fig. 11 with an additional correlation matrix. Further, in Fig 3c we compared the MSUA responses with normalization between brain regions. Amongst the 21 possible brain region pairs, 5 were uncorrelated, 7 were significantly negatively correlated and 9 were significantly correlated.

This could be due to heightened behavioral arousal caused by the changing frames as mentioned above, or due to enhanced neuronal responses to visual transients, which supports a component of direct visual response in hippocampal movie fields.

As shown in Extended data 7 and 8 and described above, the effect of arousal as quantified by theta power of pupil diameter cannot explain the results in hippocampal areas and the correlations in multiunit responses are unrelated across many brain areas.

Second, the data in Ext. Fig. 13c show a significant correlation in hippocampal responses to same scrambled frames between even and odd trials, which also suggests a significant component of direct visual response.

This is plausible. The fraction of hippocampal cells which were significantly tuned for the scrambled presentation (4.5%) was close to chance level (3%), and this small subset of cells was used to compute the population overlap between even and odd trials in Ext Fig. 13 (old numbering). As described above, this significant but small amount of tuning could generate significant population overlap, which is to be expected by construction.

Is there a significant component purely due to the temporal continuity of movie frames in hippocampal movie fields? To support that this is indeed the case, the authors have presented data that hippocampal movie fields largely disappear after movie frames are scrambled. However, this could be caused by the movie-field detection method (it is unclear whether single-frame field could be detected).

As described in the methods section, the movie-field detection algorithm had a resolution of 3.3ms resolution, which ensured that we could detect single frame fields. As reported, we did find such short movie fields in several cells in the visual areas. The sparsity metric used is agnostic to the ordering of the responses, and hence single frame field, and the resultant significant movie-tuning, if present, can be detected by our methods.

Another concern in the analysis is that movie-fields are not analyzed on re-arranged neural responses to scrambled movie frames. The raw data in Fig. 4e seem quite convincing. Unfortunately, the quantifications of movie fields in this case are not compared to those with the original movie.

We saw very few (3.6-4.9%) cells with significant movie tuning for scrambled presentation in the hippocampus. Hence, we did not quantify this earlier. This is now provided in new Extended Data Fig. 16. The amount of movie tuning for the scrambled presentation taken as-is, or after rearranging the frames is below 5% for all hippocampal brain regions.

Reviewer #2 (Public Review):

[…] The authors have concluded that the neurons in the thalamo-cortical visual areas and the hippocampus commonly encode continuous visual stimuli with their firing fields spanning the mega-scale, but they respond to different aspects of the visual stimuli (i.e., visual contents of the image versus a sequence of the images). The conclusion of the study is fairly supported by the data, but some remaining concerns should be addressed.

1) Care should be taken in interpreting the results since the animal's behavior was not controlled during the physiological recording.

This was done intentionally since plenty of research shows that task demand (e.g., Aronov and Tank, Nature 2017) can not only modulate hippocampal responses but also dramatically alter them. We have now provided additional figures (Extended Data Fig. 6 and 7) where we quantified the effects of the behavioral states (sharp wave ripples, theta power and pupil diameter), as well as the effect of locomotion (Extended Data Fig. 4). Movie tuning remained unaffected with these manipulations. Thus, movie tuning cannot be attributed to behavioral effects.

It has been reported that some hippocampal neuronal activities are modulated by locomotion, which may still contribute to some of the results in the current study. Although the authors claimed that the animal's locomotion did not influence the movie-tuning by showing the unaltered proportion of movie-tuned cells with stationary epochs only, the effects of locomotion should be tested in a more specific way (e.g., comparing changes in the strength of movie-tuning under certain locomotion conditions at the single-cell level).

Single cell analysis of the effect of locomotion and visual stimulation is underway, and beyond the scope of the current work. As detailed in the (Extended Data Fig. 4), we have ensured that in spite of the removal of running or stationary epochs, as well as removal of sharp wave ripple events (Extended Data Fig. 6) movie tuning persists. Further, we will provide examples of strongly tuned cells from sessions with predominantly running or predominantly stationary behavior (Extended Data Fig. 7).

2) The mega-scale spanning of movie-fields needs to be further examined with a more controlled stimulus for reasonable comparison with the traditional place fields. This is because the movie used in the current study consists of a fast-changing first half and a slow-changing second half, and such varying and ununified composition of the movie might have largely affected the formation of movie-fields. According to Fig. 3, the mega-scale spanning appears to be driven by the changes in frame-to-frame correlation within the movie. That is, visual stimuli changing quickly induced several short fields while persisting stimuli with fewer changes elongated the fields.

Please note that a strong correlation between the speed at which the movie scene changed across frames was correlated with movie-field width in the visual areas, but that correlation was much weaker in the hippocampal areas (see above). Please see Extended Data Fig. 11 and the quantification of correlation between frame-to-frame changes in the movie and the properties of movie fields.

The presentation of persisting visual input for a long time is thought to be similar to staying in one place for a long time, and the hippocampal activities have been reported to manifest in different ways between running and standing still (i.e., theta-modulated vs. sharp wave ripple-based). Therefore, it should be further examined whether the broad movie-fields are broadly tuned to the continuous visual inputs or caused by other brain states.

As shown in Extended Data Fig. 6, movie field properties are largely unchanged when SWR are removed from the data, or when the effect of pupil diameter or theta power were factored for (Extended Data Fig.7).

3) The population activities of the hippocampal movie-tuned cells in Fig. 3a-b look like those of time cells, tiling the movie playback period. It needs to be clarified whether the hippocampal cells are actively coding the visual inputs or just filling the duration.

Tiling patterns would be observed when the maximal are sorted in any data, even for random numbers. This alone does not make them time cells. The following observations suggest that movie fields cannot be explained as being time cells.

• a. Time cells mostly cluster at the beginning of a running epoch (Pastalkova et al. Science 2008, MacDonald et al. Neuron 2011) and they taper off towards the end. Such large clustering is not visible in these tiling plots for movie tuned cells.

• b. Time fields become wider as the temporal duration progresses (Pastalkova et al. Science 2008, MacDonald et al. Neuron 2011) as the encoded temporal duration increases. This is not evident in any movie fields.

• c. Widths of movie fields in visual areas, and to a smaller extent in the hippocampal areas, were clearly modulated by the visual content, like the change from one frame to the next (F2F correlation, Extended Data Fig. 11).

• d. Tiling pattern of movie fields was found in visual areas too, with qualitatively similar pattern as hippocampus. Clearly, visual area responses are not time cells, as shown by the scrambled stimulus experiment. Here, neural selectivity could be recovered by rearranging them based on the visual content of the continuous movie, and not the passage of time.

The scrambled condition in which the sequence of the images was randomly permutated made the hippocampal neurons totally lose their selective responses, failing to reconstruct the neural responses to the original sequence by rearrangement of the scrambled sequence. This result indirectly addressed that the substantial portion of the hippocampal cells did not just fill the duration but represented the contents and temporal order of the images. However, it should be directly confirmed whether the tiling pattern disappeared with the population activities in the scrambled condition (as shown in Extended Data Fig. 11, but data were not shown for the hippocampus).

As stated above for the continuous movie, tiling pattern alone does not mean those are time cells. Further, tuning, and tiling pattern remained intact with scrambled movie in the visual cortices but not in hippocampus.

Reviewer #3 (Public Review):

[…] The paper is conceptually novel since it specifically aims to remove any behavioral or task engagement whatsoever in the head-fixed mice, a setup typically used as an open-loop control condition in virtual reality-based navigational or decision making tasks (e.g. Harvey et al., 2012). Because the study specifically addresses this aspect of encoding (i.e. exploring effects of pure visual content rather than something task-related), and because of the widespread use of video-based virtual reality paradigms in different sub-fields, the paper should be of interest to those studying visual processing as well as those studying visual and spatial coding in the hippocampal system. However, the task-free approach of the experiments (including closely controlling for movement-related effects) presents a Catch-22, since there is no way that the animal subjects can report actually recognizing or remembering any of the visual content we are to believe they do.

Our claim is that these are movie scene evoked responses. We make no claims about the animal’s ability to recognize or remember the movie content. That would require entirely different set of experiments. Meanwhile, we have shown that these results are not an artifact of brain states such as sharp wave ripples, theta power or pupil diameter (Extended Data Fig. 6 and 7) or running behavior (Extended Data Fig. 4). Please see above for a detailed response.

We must rely on above-chance-level decoding of movie segments, and the requirement that the movie is played in order rather than scrambled, to indicate that the hippocampal system encodes episodic content of the movie. So the study represents an interesting conceptual advance, and the analyses appear solid and support the conclusion, but there are methodological limitations.

It is important to emphasize that these responses could constitute episodic responses but does not prove episodic memory, just as place cell responses constitute spatial responses but that does not prove spatial memory. The link between place cells and place memory is not entirely clear. For example, mice lacking NMDA receptors have intact place cells, but are impaired in spatial memory task (McHugh et al. Cell 1996), whereas spatial tuning was virtually destroyed in mice lacking GluR1 receptors, but they could still do various spatial memory tasks (Resnik et al. J. Neuro 2012). The experiments about episodic memory would require an entirely different set of experiments that involve task demand and behavioral response, which in turn would modify hippocampal responses substantially, as shown by many studies. Our hypothesis here, is that just like place cells, these episodic responses without task demand would play a role, to be determined, in episodic memory. We will emphasize this point in the main text (Ln 432-436 in the revised manuscript).

Major concerns:

1) A lot hinges on hinges on the cells having a z-scored sparsity >2, the cutoff for a cell to be counted as significantly modulated by the movie. What is the justification of this criterion?

The z-scored sparsity (z>2) corresponds to p<0.03. This would mean that 3% of the results could appear by chance. Hence, z>2 is a standard method used in many publications. Another advantage of z-scored sparsity is that it is relatively insensitive to the number of spikes generated by a neuron (i.e. the mean firing rate of the neuron and the duration of the experiment). In contrast, sparsity is strongly dependent on the number of spikes which makes it difficult to compare across neurons, brain regions and conditions (See Supplement S5 Acharya et al. Cell 2016). To further address this point, we compared our z-scored sparsity measure with 2 other commonly used metrics to quantify neural selectivity, depth of modulation and mutual information (Extended Data Fig. 3). Comparable movie tuning was obtained from all 3 metrics, upon z-scoring in an identical fashion.

It should be stated in the Results. Relatedly, it appears the formula used for calculating sparseness in the present study is not the same as that used to calculate lifetime sparseness in de Vries et al. 2020 quoted in the results (see the formula in the Methods of the de Vries 2020 paper immediately under the sentence: "Lifetime sparseness was computed using the definition in Vinje and Gallant").

The definition of sparsity we used is used commonly by most hippocampal scientists (Treves and Rolls 1991, Skaggs et al. 1996, Ravassard et al. 2013). Lifetime sparseness equation used by de Vries et al. 2020, differs from us by just one constant factor (1-1/N) where N=900 is the number of frames in the movie. This constant factor equals (1- 1/900)=0.999. Hence, there is no difference between the sparsity obtained by these two methods. Further, z-scored sparsity is entirely unaffected by such constant factors. We will clarify this in the methods of the revised manuscript.

To rule out systematic differences between studies beyond differences in neural sampling (single units vs. calcium imaging), it would be nice to see whether calculating lifetime sparseness per de Vries et al. changed the fraction "movie" cells in the visual and hippocampal systems.

As stated above, the two definitions of sparsity are virtually identical and we obtained similar results using two other commonly used metrics, which are detailed in Extended Data Fig. 3.

2) In Figures 1, 2 and the supplementary figures-the sparseness scores should be reported along with the raw data for each cell, so the readers can be apprised of what types of firing selectivity are associated with which sparseness scores-as would be shown for metrics like gridness or Raleigh vector lengths for head direction cells. It would be helpful to include this wherever there are plots showing spike rasters arranged by frame number & the trial-averaged mean rate.

As shown in several papers (Aghajan et al Nature Neuroscience 2015, Acharya et al., Cell 2016) raw sparsity (or information content) are strongly dependent on the number of spikes of a neuron. This makes the raw values of these numbers impossible to compare across cells, brain regions and conditions. (Please see Supplement S5 from Acharya et al., Cell 2016 for details). Including the data of sparsity would thus cause undue confusion. Hence, we provide z-scored sparsity. This metric is comparable across cells and brain regions, and now provided above each example cell in Figure 1 and Extended Data Fig. 2.

3) The examples shown on the right in Figures 1b and c are not especially compelling examples of movie-specific tuning; it would be helpful in making the case for "movie" cells if cleaner / more robust cells are shown (like the examples on the left in 1b and c).

We did not put the most strongly tuned hippocampal neurons in the main figures so that these cells are representative of the ensemble and not the best possible ones, so as to include examples with broad tuning responses. We have clarified in the legend that these cells are some of the best tuned cells. Although not the cleanest looking, the z-scored sparsity mentioned above the panels now indicates how strongly they are modulated compared to chance levels. Additional examples, including those with sharply tuned responses are shown in Extended Data Fig. 5 and 8.

4) The scrambled movie condition is an essential control which, along with the stability checks in Supplementary Figure 7, provide the most persuasive evidence that the movie fields reflect more than a passive readout of visual images on a screen. However, in reference to Figure 4c, can the authors offer an explanation as to why V1 is substantially less affected by the movie scrambling than it's main input (LGN) and the cortical areas immediately downstream of it? This seems to defy the interpretation that "movie coding" follows the visual processing hierarchy.

This is an important point, one that we find very surprising as well. Perhaps this is related to other surprising observations in our manuscript, such as more neurons appeared to be tuned to the movie than the classic stimuli. A direct comparison between movie responses versus fixed images is not possible at this point due to several additional differences such as the duration of image presentations and their temporal history. The latency required to rearrange the scrambled responses (60ms for LGN, 74ms for V1, 91ms for AM/PM) supports the anatomical hierarchy. The pattern of movie tuning properties was also broadly consistent between V1 and AM/PM (Fig 2). However, all metrics of movie selectivity (Fig 2) to the continuous movie showed a consistent pattern that was the exact opposite pattern of the simple anatomical hierarchy: V1 had stronger movie tuning, higher number of movie fields per cell, narrower movie-field widths, larger mega-scale structure, and better decoding than LGN. V1 was also more robust to the scrambled sequence than LGN. One possible explanation is that there are other sources of inputs to V1, beyond LGN, that contribute significantly to movie tuning. This is an important insight and we will modify the discussion to highlight this.

Relatedly, the hippocampal data do not quite fit with visual hierarchical ordering either, with CA3 being less sensitive to scrambling than DG. Since the data (especially in V1) seem to defy hierarchical visual processing, why not drop that interpretation? It is not particularly convincing as is.

The anatomical organization is well established and an important factor. Even when observations do not fit the anatomical hierarchy, it provides important insights about the mechanisms. All properties of movie tuning (Fig 2) –the strength of tuning, number of movie peaks, their width and decoding accuracy firmly put visual areas upstream of hippocampal regions. But, just like visual cortex there are consistent patterns that do not support a simple feed-forward anatomical hierarchy. We have pointed out these patterns so that future work can build upon it.

5) In the Discussion, the authors argue that the mice encode episodic content from the movie clip as a human or monkey would. This is supported by the (crucial) data from the scrambled movie condition, but is nevertheless difficult to prove empirically since the animals cannot give a behavioral report of recognition and, without some kind of reinforcement, why should a segment from a movie mean anything to a head-fixed, passively viewing mouse?

We emphasize once again that our claim is about the nature of encoding of the movie across these neurons. We make no claims about whether this forms a memory or whether the mouse is able to recognize the content or remember it. Despite decades of research, similar claims are difficult to prove for place cells, with plenty of counter examples (See the points above). The important point here is that despite any cognitive component, we see remarkably tuned responses in these brain areas. Their role in cognition would take a lot more effort and is beyond the scope of the current work.

Would the authors also argue that hippocampal cells would exhibit "song" fields if segments of a radio song-equally arbitrary for a mouse-were presented repeatedly? (reminiscent of the study by Aronov et al. 2017, but if sound were presented outside the context of a task). How can one distinguish between mere sequence coding vs. encoding of episodically meaningful content? One or a few sentences on this should be added in the Discussion.

Aronov et al 2017, found the encoding of an audio sweep in hippocampus when the animals were doing a task (release the lever at a specific frequency to obtain a reward). However, without a task demand they found that hippocampal neurons did not encode the audio sequence beyond chance levels. This is at odds with our findings with the movie where we see strong tuning despite any task demand or reward. These results are consistent with but go far beyond our recent findings that hippocampal (CA1) neurons can encode the position and direction of motion of a revolving bar of light (Purandare et al. Nature 2022). Please see Ln 414-420 for related discussion.

These responses are unlikely to be mere sequence responses since the scrambled sequence was also fixed sequence that was presented many times and it elicited reliable responses in visual areas, but not in hippocampus. Hence, we hypothesize that hippocampal areas encode temporally related information, i.e. episodic content. We will modify the discussion to address these points.

Author Response:

We thank the eLife editorial board and the reviewers for the assessment of our article. We look forward to thoroughly addressing their comments and concerns. We would like to correct one factual error in the consensus public review:

“Importantly, the authors do not present evidence that value itself is stably encoded across days, despite the paper's title. The more conservative in its claims in the Discussion seems more appropriate: "these results demonstrate a lack of regional specialization in value coding and the stability of cue and lick [(not value)] codes in PFC."

The imaging sessions in which we identify value coding cells were in fact performed on separate days: Experimental Days 6 and 7 (see Figure 1b), which is evidence of the stability of value coding across consecutive days. Days 6 and 7 correspond to the third day of Odor Set 1 and the third day of Odor Set 2, respectively, which is why we referred to them both as “Day 3” in the manuscript, and this may have led to the confusion about the temporal relationship between these sessions. We will clarify this terminology in the revised manuscript.

Author Response

Reviewer #1 (Public Review):

In this well-written manuscript, Afshar et al demonstrated the significant transcriptional and proteomic differences between cultured human umbilical vein endothelial cells (HUVECs) and those freshly isolated from the cords. They showed that TGFbeta and BMP signaling target genes were enriched in cord cells compared to those in culture. Extracellular matrix (ECM) and cell cycle-related genes were also different between the two conditions. Because master regulators of EC shear stress response genes, KLF2 and KLF4, were downregulated in culture, the authors sought to restore the in vivo transcriptional profile with the application of shear stress in an orbital shaker and dextran-containing media for various time periods. They showed that after 48 hours of shear stress the transcriptional profile of sheared cells correlated with in vivo transcriptional profile more significantly than static cultures. They also showed, using single cell RNAseq, that EC-smooth muscle cell cocultures resulted in changes in TGFbeta and NOTCH signaling pathways and rescued 9% of the in vivo transcriptional signatures.

This is an important study that was elegantly executed. The authors should also be commended for making their data public; thereby, creating a valuable resource for vascular biologists.

We much appreciate the comments and thank the reviewer for the time and effort evaluating the study.

Reviewer #2 (Public Review):

The authors profiled the transcriptome and proteome of human umbilical vein endothelial cells freshly isolated from in vivo and compared that with the same cells exposed to in vitro culture under different conditions, including static culture, flow, and co-culture with smooth muscle cells. The experiments were properly designed and performed. The authors also provided a reasonable and sound interpretation of their findings. This study provides valuable insights into how the culturing conditions impact on gene expression, encouraging the field to select their in vitro work setting appropriately. Overall, the manuscript is well-written and easy to follow.

Several notable strengths include:

1. Parallel transcriptome- and proteome-wide profiling of endothelial cells enabling the unbiased interrogation of gene expression and a genome-wide view of the impact of in vitro culture on endothelial transcriptome.

2. The innovative experimental design and comparisons were done with genetically identical ECs (from the same donors) in vivo and in vitro.

3. The analyses were robust and provided novel information on flow-dependent and cell context-dependent gene regulation, with the native freshly isolated cells as a baseline.

4. The donor samples used in this study were diverse including Asian, White, Black, Latino, and American Indian samples which reduce racial background bias.

Some points that can strengthen the study:

A clear description of experimental and analytical details (e.g. how the comparisons were made) and more in-depth interpretation and discussion of the results, e.g. the complete genes that are rescued by flow and co-culture and potential synergy of these factors.

We thank the reviewer for highlighting the strengths and appreciate the comments on experimental and analytical details which have been now addressed in this revised manuscript. Specifically, we have expanded the discussion and included synergy and additional comments on the rescued genes. A clear description of experimental and analytical details (e.g. how the comparisons were made) and more in-depth interpretation and discussion of the results, e.g. the complete genes that are rescued by flow and co-culture and potential synergy of these factors are now included.

Reviewer #3 (Public Review):

Afshar et al. performed RNA-seq and LC-MS of in vivo and in vitro HUVECs to identify the role of culture conditions on gene expression. Given the widespread use of HUVECs to study EC biology, these findings are interesting and can help design better in vitro experiments. There have been previous papers that compared in vivo and in vitro HUVECs, however, the depth of sequencing and analysis in this manuscript identifies some novel effects which should be accounted for in future in vitro experiments using ECs.

Strengths:

1. Major findings of distinct pathways affected by cell culture are novel and interesting. The authors identify major effects on TGFb and ECM gene expression. They also corroborate previous findings of flow response pathways, namely KLF2/4 and Notch pathway regulation.

2. Use of multiple genomic methods to profile effects of culture conditions. The LC-MS data showed a significant correlation with RNA-seq, however, the data were not as strong so not used for subsequent analyses.

3. Use of scRNA-seq to show the dynamic effects of co-culture and shear stress on ECs is very novel. However, the heterogeneity in the EC populations is not discussed in this manuscript.

We would like to thank the reviewer for the in-depth analysis of our study and for highlighting the novelty and strength of the data. Note that we included comments in relation to EC heterogeneity as part of the limitations of this study (in the Discussion).

Weaknesses:

1. The physiological relevance of these changes in gene expression is not demonstrated in the manuscript. The authors claim the significance of their data is to improve in vitro culture to better represent in vivo biology. Is this the case with orbital shear stress? Do they rescue some functional effects in ECs with long-term shear stress? An angiogenesis, barrier function, or migration assay for HUVECs exposed to different conditions would help answer this question. A similar assay for cells after EC-VSMC co-culture would validate the importance of these stimuli.

The reviewer is correct, our manuscript did not expand into physiological read outs, we have now clearly acknowledged this as part of the limitations of the study. Notably, there is already extensive literature on the effects of different types of flow on several physiological parameters. For example, others have shown that laminar shear stress (by orbital or other means) reduces proliferation and migration (PMID: 31831023; PMID: 22012789, PMID: 12857765, PMID: 21312062, PMID: 15886673; PMID: 17323381), reduces inflammation (PMID: 34747636; PMID: 32951280), and improves barrier function (PMID: 20543206; PMID: 32457386 ; PMID: 12577139, PMID: 27246807; PMID: 31500313 ).

From the onset, our objective was to bring granularity to transcriptional changes associated with the transition from in vivo to in vitro. Further, it was our goal to identify the cohorts of transcripts that could and those that could not be rescued by altering culture conditions. Because we had transcriptional information from the identical samples at a time that they were in the vessel, we have been able to fulfill our goal. We feel this is important, and currently missing data, that will be of value to many investigators.

1. One explanation for the increased expression of ECM genes in vivo is that these cells are contaminated with VSMCs/fibroblasts. This could be very likely given that cells were not sorted or purified upon isolation. Expression of other VSMC or fibroblast-specific markers (i.e. CNN1, MYH11, SMTN, DCN, FBLN1) would help determine if there is some level of non-EC contamination.

We thank the reviewer for this comment and prompted by this, we have included a new figure (Supplemental Figure 1 and new panels in Supplemental Figure 5) that directly address this concern.

Amongst the several pieces of data, we included scRNAseq from cells that were immediately obtained from umbilical vein – three independent experiments sequenced together and showed in one UMAP (Supplemental Figure 1C). As can be appreciated, the very large majority of cells are endothelial and the only other cell types present were blood cells (erythrocytes and CD45+ cells). No smooth muscle cells or fibroblasts were detected. These three examples are indeed representative of a large number of scRNAseq datasets (35 from cords and cultures for this and other projects). Furthermore, our cultures are also routinely evaluated by FACS (one example has been provided in Supplemental Figure 1E). We do not find, as illustrated in that example, cells that are not positive for CD31 and VE-Cadherin.

We hope this information reveals the rigor of our studies and convinces the reviewer that the transcriptional changes observed are from endothelial cells.

1. The use of scRNA-seq in Figure 4 is interesting. There appear to be 2 distinct EC populations in the co-cultured ECs. What are the marker genes for the 2 populations?

Indeed, we and others (Kalluri et al., 2019) have noticed two distinct populations in the in vivo and also in cultured ECs, as pointed by the reviewer. Evaluation as to these two subpopulations reflect two transcriptionally distinct groups or different states of cyclic expression patterns, requires more thorough analysis and lineage tracing studies and distinct from the focus of this manuscript. Nonetheless, we have made a point in the revised manuscript to highlight these possibilities.

Reference: Kalluri, AS, Vellarikkal, SK, Edelman, ER, Nguyen, L, Subramanian, A, Ellinor PT, Regev, A, Kathiresan, S, Gupta, RM. Single Cell Analysis of the Normal Mouse Aorta Reveals Functionally Distinct Endothelial Cell Populations. Circulation, 2019. 140:147-163.

1. The modest shifts in gene expression with shear stress and co-culture could be attributed to the batch effect. The authors describe 1 batch correction method (ComBat) in the bulk RNA-seq, but no mention of batch correction was noted in the scRNA-seq methods. The authors should ensure that batch effect correction in all data is adequate, and these results should be added to the manuscript.

We thank the reviewer for this comment. Indeed, batch effects are a particularly important consideration when samples are prepared separately and/or sequenced at distinct times, note this was not the case in this study.

For the scRNA-seq analysis, we removed the low-quality cells, but did not use batch-effect correction methods because the samples were prepared and run at the same time. Meaning, isolation was performed in parallel, generation of cDNA libraries was done concurrently, and sequencing was run in the same gel. The quality of the data (and lack of batch effect) was subsequently verified when the two mono-culture biological replicates were evaluated by Seurat and were found to overlap on the UMAP (Figure 4), the same applies to the two co-culture biological replicates. These results clearly indicate that there’s no batch effect (as the samples were not process in distinct batches) among these samples.

1. Table 1 shows ATAC-seq was done, however, no data from these experiments are provided in the manuscript.

As mentioned (reviewer 2), we had performed ATACseq but decided to remove from the manuscript for several reasons and apologize for missing reference to Table 1. We have now corrected this error.

1. Shear stress was achieved with an orbital shaker, which the accompanying citation states introduces significant heterogeneity in the ECs. This is based on the location of the culture dish. Was this heterogeneity seen in the scRNA-seq data?

Correct. We only use the 2/3 peripheral area of the plates and discard the central aspect of the plate. We have added clarifying language to the Methods > Shear stress application to reflect this: “Orbital shear stress (130 rpm) was applied to confluent cell cultures by using an orbital shaker positioned inside the incubator as previously discussed (32). The shear stress within the cell culture well corresponds to arterial magnitudes (11.5 dynes/cm2) of shear stress. To reduce issues associated with uniformity of shear stress, the endothelial cell monolayers in 6-well plates were lysed after removing center region using cell scraper (BD Falcon #35-3085) and washing with 1X HBSS (Corning #21-022-CV). The 1.8cm blade was circumferentially used in the center of the 6-well plate to remove the center of the monolayer that did not see the higher shear stress.”

1. It would be important to know whether the authors reproduce the findings from other papers that CD34 expression is reduced in cultured HUVECs:

Muller AM, Cronen C, Muller KM, Kirkpatrick CJ: Comparative analysis of the reactivity of human umbilical vein endothelial cells in organ and monolayer culture. Pathobiology 1999;67:99-107. Delia D, Lampugnani MG, Resnati M, Dejana E, Aiello A, Fontanella E, Soligo D, Pierotti MA, Greaves MF: Cd34 expression is regulated reciprocally with adhesion molecules in vascular endothelial cells in vitro. Blood 1993;81:1001-1008.

Thank you for this suggestion. Supplemental Excel 4 allows the reader to review single genes that are modulated by condition and in fact, consistent with all previous literature, CD34 expression is one of the most significantly decreased genes in cultured HUVECs (0.9, p=1E-5).

Author Response

Reviewer #1 (Public Review):

1) I was confused about the nature of the short-term plasticity mechanism being modeled. In the Introduction, the contrast drawn is between synaptic rewiring and various plasticity mechanisms at existing synapses, including long-term potentiation/depression, and shorter-term facilitation and depression. And the synaptic modulation mechanism introduced is modeled on STDP (which is a natural fit for an associative/Hebbian rule, especially given that short-term plasticity mechanisms are more often non-Hebbian).

Indeed, because of its associative nature, the modulation mechanism was envisioned to be STDP-like, i.e. on faster time scales than the complete rewiring of the network (via backpropagation) but slower time scales than things like STSP which, as the reviewer points out, are usually not considered associative. One thing we do want to highlight is that backpropagation and the modulation mechanism are certainly not independent of one another. During training, the network’s weights that are being adjusted by backpropagation are experiencing modulations, and said modulations certainly factor into the gradient calculation.

We have edited the abstract and introduction to try to make the distinction of what we are trying to model clearer.

1) cont: On the other hand, in the network models the weights being altered by backpropagation are changes in strength (since the network layers are all-to-all), corresponding more closely to LTP/LTD. And in general, standard supervised artificial neural network training more closely resembles LTP/LTD than changing which neurons are connected to which (and even if there is rewiring, these networks primarily rely on persistent weight changes at existing synapses).

Although we did not highlight this particular biological mechanism because we wanted to keep the updates as general as possible, one could view the early versus late LTP. We have added an additional discussion of how the associative modulation mechanisms and backpropagation might biologically map into this mechanism in the discussion section.

1) cont: Moreover, given the timescales of typical systems neuroscience tasks with input coming in on the 100s of ms timescale, the need for multiple repetitions to induce long-term plasticity, and the transient nature/short decay times of the synaptic modulations in the SM matrix, the SM matrix seems to be changing on a timescale faster than LTP/LTD and closer to STP mechanisms like facilitation/depression. So it was not clear to me what mechanism this was supposed to correspond to.

We note that although the structure of the tasks certainly resembles known neuroscience experiments that happen on shorter time scales (and with the introduction of the 19 new NeuroGym tasks, even more so), we did not have a particular time scale for task effects in mind. So each piece of “evidence” in the integration tasks may indeed occur over significantly slower time scales and could abstractly represent multiple repetitions in order to induce (say) early phase LTP.

Given that the separation between the two plasticity mechanisms may be clearer for STSP, and indeed many of the tasks we investigate may more naturally be mapped to tasks that occur on time scales more relevant to STSP, we have introduced a second modulation rule that is only dependent upon the presynaptic firing rates. See our response to the Essential Revisions above for additional details on these new results.

2) A number of studies have explored using short-term plasticity mechanisms to store information over time and have found that these mechanisms are useful for general information integration over time. While many of these are briefly cited, I think they need to be further discussed and the current work situated in the context of these prior studies. In particular, it was not clear to me when and how the authors' assumptions differed from those in previous studies, which specific conclusions were novel to this study, and which conclusions are true for this specific mechanism as opposed to being generally true when using STP mechanisms for integration tasks.

We have added additional works to the related works sections and expanded the introduction to try to better convey the differences with our work and previous studies. Briefly, mostly our assumptions differed from previous studies in that we considered a network that relied only on synaptic modulations to do computations, rather than a network with both recurrence and synaptic modulations. This allowed us to isolate the computational power and behavior of computing using synaptic modulations alone.

It is hard to say which of the conclusions are generally true when using STP mechanisms for integration tasks without a comprehensive comparison of the various models of STP on the same tasks we investigated here. That being said, we believe we have presented in this work conclusions that are not present in other works (as far as we are aware) including: (1) a demonstration of the strength of computing with synaptic connection on a large variety of sequential tasks, (2) an investigation into the dynamics of such computations how they might manifest in neuronal recordings, and (3) a brief look at how these different dynamics might be computational beneficial in neuroscience-relevant areas. We also note that one reason for the simplicity of our mechanism is that we believe it captures many effects of synaptic modulations (e.g. gradual increase/decrease of synaptic strength that eventually saturates) with a relatively simple expression, and so we believe other STP mechanisms would yield qualitatively similar results. We have edited the text to try to clarify when conclusions are novel to this study and when we are referencing results from other works.

Reviewer #2 (Public Review):

On the other hand, the general principle appears (perhaps naively) very general: any stimulus-dependent, sufficiently long-lived change in neuronal/synaptic properties is a potential memory buffer. For instance, one might wonder whether some non-associative form of synaptic plasticity (unlike the Hebbian-like form studied in the paper), such as short-term synaptic plasticity which depends only on the pre-synaptic activity (and is better motivated experimentally), would be equally effective. Or, for that matter, one might wonder whether just neuronal adaptation, in the hidden layer, for instance, would be sufficient. In this sense, a weakness of this work is that there is little attempt at understanding when and how the proposed mechanism fails.

We have tried to address if the simplicity of the tasks considered in this work may be a reason for the MPN’s success by training it on 19 additional neuroscience tasks (see response to Essential Revisions above). Across all these additional tasks, we found the MPN performs comparable to its RNN counterparts.

To address whether associativity is necessary in our setup we have introduced a version of the MPN that has modulation updates that are only presynaptic dependent. We call this the “MPNpre” and have added several results across the paper addressing its computational abilities (again, additional details are provided above in Essential Revisions). We find the MPNpre has dynamics that are qualitatively the same as its MPN counterpart and has very comparable computational capabilities.

Certainly, some of the tasks we consider may also be solvable by introducing other forms of computation such as neuronal adaptation. Indeed, we believe the ability of the brain to solve tasks in so many different ways is one of the things that makes it so difficult to study. Our work here has attempted to highlight one particular way of doing computations (via synapse dynamics) and compared it to one particular other form (recurrent connections). Extending this work to even more forms of computation, including neuronal dynamics, would be very interesting and further help distinguish these different computational methods from one another.

Reviewer #3 (Public Review):

Because the MPN is essentially a low-pass filter of the activity, and the activity is the input - it seems that integration is almost automatically satisfied by the dynamics. Are these networks able to perform non-integration tasks? Decision-making (which involves saddle points), for instance, is often studied with RNNs.

We have tested the MPN on 19 additional supervised learning tasks found in the NeuroGym package (Molano-Mazon et. al., 2022), which consists of several decision-making-based tasks and added these results to the main text (see response to Essential Revisions above, and also Figs. 7i & 7j). Across all tasks we investigated, we found the MPN performs at comparable levels to its RNN counterparts.

Manuel Molano-Mazon, Joao Barbosa, Jordi Pastor-Ciurana, Marta Fradera, Ru-Yuan Zhang, Jeremy Forest, Jorge del Pozo Lerida, Li Ji-An, Christopher J Cueva, Jaime de la Rocha, et al. “NeuroGym: An open resource for developing and sharing neuroscience tasks”. (2022).

The current work has some resemblance to reservoir computing models. Because the M matrix decays to zero eventually, this is reminiscent of the fading memory property of reservoir models. Specifically, the dynamic variables encode a decaying memory of the input, and - given large enough networks - almost any function of the input can be simply read out. Within this context, there were works that studied how introducing different time scales changes performance (e.g., Schrauwen et al 2007).

Thank you for pointing out this resemblance and work. In our setup, the fact that lamba is the same for the entire network means all elements of M decrease uniformly (though the learned modulation updates may allow for the growth of M to be non-uniform). One modification that we think would be very interesting to explore is the effects on the dynamics of non-uniform learning rates or decays across synapses. In this setting, the M matrix could have significantly different time scales and may even further resemble reservoir computing setups. We have added a sentence to the discussion section discussing this possibility.

Another point is the interaction of the proposed plasticity rule with hidden-unit dynamics. What will happen for RNNs with these plasticity rules? I see why introducing short-term plasticity in a "clean" setting can help understand it, but it would be nice to see that nothing breaks when moving to a complete setting. Here, too, there are existing works that tackle this issue (e.g., Orhan & Ma, Ballintyn et al, Rodriguez et al).

Thank you for pointing out these additional works, they are indeed very relevant and we have added them all to the text where relevant.

Here we believe we have shown that either recurrent connections or synaptic dynamics alone can be used to solve a wide variety of neuroscience tasks. We don’t believe a hybrid setting with both synaptic dynamics and recurrence (e.g. a Vanilla RNN with synaptic dynamics) would “break” any part of this setup. Since each of the computational mechanisms could be learned to be suppressed the network could simply solve the task by relying on only one of the two mechanisms. For example, it could use a strictly non-synaptic solution by driving eta (the learning rate of the modulations) to zero or it could use a non-recurrent solution by driving the influence of recurrent connections to be very small. Orhan & Ma mention they have a hard time training a Vanilla RNN with Hebbian modulations on the recurrent weights for any modulation effect that goes back more than one time step, but unlike our work they rely on a fixed modulation strength.

Indeed, we think how networks with multiple computational mechanisms will solve tasks is a very interesting question to be further investigated, and a hybrid solution may be likely. We believe our work is valuable in that it illuminates one end of the spectrum that is relatively unexplored: how such tasks could be solved using just synaptic dynamics. However, what type of solution a complete setup ultimately lands on is likely largely dependent upon both the initialization and the training procedure, so we felt exploring the dynamics of such networks was outside the scope of this work.

One point regarding biological plausibility - although the model is abstract, the fact that the MPN increases without bounds are hard to reconcile with physical processes.

Note although the MPN expression does not have explicit bounds, in practice the exponential decay eventually does balance with the SM matrix updates, and so we observe a saturation in its size (Fig. 4c, except for the case of lamba=1.0, which is not considered elsewhere in the text). However, we explicitly added modulation bounds to the M matrix update expression and did not find it significantly changed the results (see comments on Essential Revisions above for details).

Author Response

Reviewer #2 (Public Review):

Here I will mainly comment on the biology of adipocytes, which is my specialty.

In this manuscript, it has been very convincingly shown that O-GlcNAc acts as an important regulator of MSC differentiation in mice, and given previous studies in which O-GlcNAc is regulated by aging and nutritional status, it makes sense that this PTM determines differentiation and BM niche.

The point that O-GlcNAc regulates adipocyte differentiation is convincing, but there are already previous studies using 3T3-L1 (e.g., Biochemical and Biophysical Research Communications 417 (2012) 1158-1163), and a more step-by-step demonstration of the molecular mechanism would make this an excellent paper that can be extended to adipocyte research in general, not just BM.

While O-GlcNAc has been demonstrated in regulating many aspects of metabolic physiology, our understanding of its role in adipogenesis has been limited so far. As the reviewer pointed out, there was an in vitro report on its inhibition of adipogenesis in 3T3-L1 cells (Ji et al., 2012). Two recent publications from Dr. Xiaoyong Yang’s group revealed the profound role of mature white adipocytes OGT in regulating lipolysis and obesity (Li et al., 2018; Yang et al., 2020). To my knowledge, our manuscript is the first attempt to address the regulation of adipogenesis by O-GlcNAc in vivo. While using the BMSCs as a non-conventional model, we speculate our molecular mechanisms (i.e., O-GlcNAc inhibition of C/EBPβ) could be conserved in peripheral adipose organs, including white and brown adipose tissues. Future experiments are warranted in the lab to extend the current knowledge to these adipocyte progenitors. Nonetheless, I would also like to point out that, due to the broad actions of OGT and the current lack of adipocyte progenitor specific Cre animal tools, such efforts might be futile as results can be confounded by defects in other organs/cells.

It is somewhat unclear whether or not the authors' in vitro experiments using 10T1/2 cells accurately reflect what is happening in vivo in knockout mice. The PDGFRa+VCAM1+ population of adipocyte progenitors shown by the authors is upregulated by about 30% by knockout of Ogt (Figure 4C). How significant is this difference? Rather, might the expression of Pparg, which indicates lineage commitment, be the underlying mechanism? In any case, this manuscript is highly impactful in the sense that the differentiation of adipocytes forming the BM niche can be controlled using tissue-specific knockouts of the Ogt gene.

We agree with the reviewer that the role of OGT in BMSC fate determination and adipogenesis might be multifaceted. The 30% increase in PDGFRa+VCAM1+ BM adipose progenitors cannot fully explain the massive adipogenesis observed in OgtΔOsx animals (Fig. 4A). Indeed, we provided in vitro evidence that genetic deletion or chemical inhibition of OGT activates adipogenesis (Fig. 4D-I). Mechanistically, we found the O-GlcNAcylation of C/EBPβ protein (but not PPARγ) is responsible in the inhibition, which leads to reduced expression of adipogenic genes, including Pparg (Fig. 4H).

Author Response

Reviewer #1 (Public Review):

The paper states that they observed a combined total of 77,017 single-nucleotide variants (SNVs) and 12,031 insertion/deletions (In/Dels) across all tissue, age, and intervention groups. Collectively, these data represent the largest collection of somatic mtDNA mutations obtained in a single study to date. However, A study with more somatic mtDNA mutations by the LostArc method (PMID 32943091) revealed 35 million deletions (~ 470,000 unique spans) in skeletal muscle from 22 individuals with and 19 individuals without pathogenic variants in POLG. Thus, the authors should reword this part to say that this study represents the largest collections of mouse mtDNA point mutations detected, but not the largest amount of mutations (deletions exceed this number).

Thank you for pointing this out. When we wrote that sentence, we were more referring to small polymerase-based errors, as opposed to larger structural variants that likely arise from a different mechanism. However, the distinction between these two event classes is poorly defined. We have amended our statement and have added a citation to Lujan et al. Our statement now reads “We observed a combined total of 77,017 single-nucleotide variants (SNVs) and 12,031 small insertion/deletions (In/Dels) (≲15bp in size) across all tissue, age, and intervention groups. Collectively, these data represent the largest collection of somatic mtDNA point mutations obtained in a single study to date and is second only to Lujan et al. in terms overall In/Del counts (Lujan et al., 2012).” (Lines 252-256)

What is the theoretical limit of pt mutations in the mitochondrial genome, assuming only one pt mutation per genome? Doesn't 77000 detected independent pt mutations approach that limit? Can the authors estimate how many molecules contained two or more pt mutations? Did the analysis reveal any un-mutated regions implying an essential function? For example, on p.9 can the authors provide an explanation of why OriL and other G/C-rich regions were not uniformly covered as compared to the rest of the genome?

This is an interesting question and one we’ve given some thought to. In fact, this basic question was the inspiration for our recent Nucleic Acids Research paper (PMC8565317) where we asked how mutations were distributed in the genome. The short answer is that we likely exceed the limit for only dG site mutations (and only for G>A mutations, at that), but not the other reference sites. The reason is that there are only 2013 dG sites and the mutation spectrum is heavily skewed toward G>X (there are 47,680 dG site mutations, 42,924 of which are G>A). In comparison, we observe only 4,421 A>X, 9,277 T>X, and 15,632 C>X mutations, but with 5,629, 4,681, and 3,976 dA, dT, and dC genomic sites, respectively. Assuming the mutations are uniformly distributed along the genome (which they are not; see our NAR paper), then random binomial sampling would require a fair amount more mutations in order to reach saturation for the other genomic sites. The uneven distribution increases this number further.

With regard to the second question, we can’t actually do this estimation with this data set. The reason is because the ~77,000 mutations aren’t found in a single sample, but are distributed across may independent or semi-independent (i.e. different organs within a mouse), which means that most, if not all, of the mutations are necessarily on different mtDNA molecules.

With regard to the OriL and G/C rich regions, these presumably have some sort of secondary structure that prevents the sequencer from obtaining any useful information. However, this is all speculative and we don’t know why. Interestingly, human mtDNA doesn’t show this dip at the OriL, despite a similar function and location in the mtDNA.

Given that mitochondrial disease usually doesn't present until >60% of the genomes are affected, the very low level of detected pt mutations observed in the mouse (and presumably similar to human) would mean that they are well below a physiological level. Thus, these low-level pt mutations are well tolerated. Can the authors estimate a theoretical age of the mouse (well beyond their life span) where over 50% of the genomes carry at least one pt mutation?

The reviewer brings up a frequent noted point in mitochondrial biology that is very much worth addressing in this manuscript. The often-cited statistic that mitochondrial disease doesn’t present until ~60% of genomes are affected is, while true, only pertinent to overt mitochondrial diseases, such as LHON, MERRF, etc, where all or nearly all cells in an individual are affected by the mutation. However, the impact of mtDNA mutations is not only contingent on how many cells have the mutation, but also the fraction of mtDNA molecules within a cell that harbor the variant. Because the deleterious effects of a mtDNA mutation act at the level of individual cells, it is important to know both how many cells harbor a mutation as well as what the heteroplasmic level is within the cell before making claims on their pathological impact.

To date, nearly all studies on mtDNA mutations rely on bulk DNA analysis from thousands to millions of cells, which necessarily decouples variant phasing information between any two reads, resulting in a loss of important biological information such as the heteroplasmic level within any given cell. As such, with bulk sequencing it is impossible to tell the difference between a homoplasmic mutation in a small subset of cells and heteroplasmic mutation in all cells. In the first case, the cells harboring this mutation would be negatively impacted, whereas in the second example, it is unlikely. One can imagine a scenario where every cell contains a different homoplasmic pathogenic mutation which would negatively affect cellular function for every cell. In this case, mutations would be highly prevalent (100% of cells), yet individually rare. However, bulk sequencing would give the appearance that no mutation comes close to exceeding the phenotypic threshold. We highlight this issue in a recent review (Sanchez-Contreras and Kennedy, 2022; PMC8896747).

The point that the review brings up is extremely important, so we have added a section in the discussion related to heteroplasmy versus clones.

Also, the problem with this low level of pt mutations is that they are not physiological, the effect of the drug treatment causing a reduction in ROS-mediated transversions would not be expected to have a detectable effect on mitochondria. The improvement on mitochondrial seen by others is most likely independent of the mutations in the genome. There needs to be a cause and effect here and I don't see one.

It is important to note that we do not make the claim (no do we want to imply) that the reduction of mutations is the reason behind the improvements in mitochondrial function by these interventions. Instead, we believe that loss of ROS-linked mutations is a consequence of the mechanism by which these interventions work. We do hypothesize that the reduction in ROS-linked mutations suggests that “there is tissue specificity in how cells repair and/or destroy oxidatively damaged mitochondria and/or mtDNA resulting in a steady-state of ROS-linked mutations.” (Lines 551-553) and that “We propose that rather than the incidence and impact of ROS damage on mtDNA being minimal, recognition and removal of ROS-linked mutations are maintained at a steady state during aging.” (Lines 572-574).

In addition, as noted above, how “low level” these mutations are and their impact on cellular function is not easily determined in bulk sequencing studies, so a strong link between cause and effect is not an answerable relationship with this data set.

There's no mention in this paper and methodology about how point mutations in nuclear-encoded mtDNA (NUMTs) are excluded from the reads and I'm worried that these errors are being read as rare errors in the mtDNA genome. While NUMTs have been documented for decades, a recent report in Science (PMID: 36198798) documents how frequently and fluidly NUMTs occur. Can the authors provide a clear explanation of how mutations in NUMTs are excluded?

The reviewer is absolutely correct to call attention to this important aspect of mitochondrial biology. We don’t believe NUMTs are an important confounder in our data set for several reasons.

1) We used isogenic inbred C57Blk6/J which, frequently, were litter mates (siblings). Therefore, any mutations from NUMTS that are there would be expected to be uniform across samples, especially between tissues from a single sample animal. Unknown and variations of NUMTS would certainly be a potentially strong confounder in an outbred population, but the use of one isogenic inbred line for this study likely eliminates this confounder.

2) We used the mm10 reference genome which is based on the C57Blk6/J strain so any NUMTS derived variants present in our mtDNA data should preferentially align against the NUMT. Therefore, we perform a BLAST step of all reads containing at least one variant against the mm10. BLAST is much more sensitive to sequence variation compared to bwa but is far slower, so it is impractical to run as the initial aligner. We then reassign the read based to whatever genomic location has the lower e-score. The result is typically around a dozen reads are removed, demonstrating that NUMTS are not likely a major source of false mutations.

3) Because NUMTS are inherited, then any variants would be found across all the tissues and animals we used in this study. As part of our processing, we mark and remove variants shared between multiple individual samples.

We have made edits to the Methods section (Lines 198-206) to more explicitly highlight the filtering steps and the logic behind them. In addition, we have added a paragraph in the discussion that addresses NUMTs (Starting on line 642).

Reviewer #2 (Public Review):

A common problem in mutation analysis is that DNA damage (present in one strand) is difficult to separate from real mutations (present in both strands). One of the approaches to solve this problem based on independent tagging of the two strands by different unique molecular identifiers was developed by the authors about 10 years ago. This study summarizes the application of this method to a wide range of mouse tissues, ages, and drug treatment regimes. Much of the results confirm previous conclusions from this laboratory. This involves overall mutational levels of somatic mtDNA mutations (~10-6-10-5), their accumulation with age, the prevalence of GA/CT transitions, and their clonality. Although these results were not new, it is important that these were confirmed in a single study with high confidence in a huge number of independent mutations.

We thank the reviewer for the comment and really hope this data set will be of significant use to other researchers given its breadth of sample types and large number of mutations.

What really sets this study apart from other studies is the detection of a large proportion of transversion mutations, primarily of the C>A/G>T and C>G/G>C types. Transversions are traditionally considered 'persona non grata' in mtDNA mutational spectra and are typically associated with errors of mutational analysis (which they in fact are). The presence of these mutations in both strands of the duplex makes a good case that these mutations are real, rather than converted damage. However, because this is such a novel discovery and because regular controls do not work (I mean, for example, that these mutations never clonally expand. If there is a clonal expansion, then the mutation is real, only real mutation can expand. But in the case of non-expandable C>A/G>T and C>G/G>C this control does not help to validate these mutations), it would be nice to provide extra assurances that this is not some kind of artifact that somehow slipped through the ds sequencing procedure. I would recommend including in the supplement the data on the abundance of single-stranded base changes as detected by ds sequencing (i.e., changes confirmed in one and not in the other strand of a given molecule). An unusually high presence of such single-stranded changes of the C>A/G>T and C>G/G>C type would be a red flag for me. If ratios of single and double-stranded mutations were similar for transitions and transversions - that would reassure me and hopefully the reader.

Furthermore, a similar excess of C>A/G>T and C>G/G>C has been observed in a recent paper by Abascal 2021 (cited in the manuscript). In that paper, a UMI- free, but otherwise very similar ds sequencing approach in nuclear DNA (BotSeqS) was demonstrated to suffer from an artifact causing (among other effects) an excess of C>A/G>T and C>G/G>C transversions. This artifact is related to end repair and nick-translation of DNA fragments during library preparation. Because BotSeqS is very similar to ds sequencing, we expect that same artifact may be taking place in the study under review. We recommend running checks similar to those undertaken by Abascal et al (which include, at the very minimum, checking the distribution of the C>A/G>T and C>G/G>C transversions within the reads (artifacts tend to be concentrated towards the ends of the reads).

The reviewer is absolutely correct to bring up this extremely important point. We have addressed these concerns in two ways that are addressed on Lines 332-361. 1) by performing an analysis of the single-stranded consensus data, which is a measure of PCR artifacts that frequently arise as a function of DNA damage, across all the tissues of the aged cohort. We noted no differences between tissues, which indicates that the amount of ROS-induced PCR artifacts is no different between the tissues. Thus, it would require a different rate at which ROS artifacts lead to false “Duplex consensus” variants that is tissue specific. The analysis is presented in Figure 3-figure supplement 2. 2) we have included an experiment in which we show that treatment of post-fragmented DNA with FPG, a glycosylase that targets Fapy-dG and 8-oxo-dG, does not differ from untreated control DNA. Because Duplex-Seq requires that both strands of a parent DNA molecule be present to form a final Duplex Consensus Sequence, the scission of one strand by the lyase activity of FPG would prevent the formation of this final consensus and prevent this sort of error from “bleeding through”. This analyses can now be found in a Figure 3-figure supplement 3.

Of note, even if transversions detected in this study prove to be artifacts of the Abascal type (likely) they still may reflect real ss damage in mtDNA (not instrumental artifacts, like sequencing errors or in vitro DNA damage). This is supported by the strong variation in the levels of transversions across tissues and as a result of the ameliorating drug intervention. Artifacts, in contrast, would be expected to be at a constant level. This logic, however, does not differentiate between real ds mutations and ss damage. So UMI-based ds sequencing evidence remains the only (though very strong) independent proof. So, in my view, whereas the jury may be still out on whether the observed transversions are true ds mutations or some kind of single-stranded damage, this is a critically important observation. The evidence of ss damage greatly varied between tissues and detected with such precision on a single molecule level is a very important finding as well.

Out of caution, I would recommend mentioning the above-stated uncertainty and noting that more research is needed to fully confirm that C>A/G>T and C>G/G>C changes detected in this study are indeed double-stranded mutations.

We agree. Together with comments from Reviewer #1 regarding NUMTs (Comment #5), we have added a paragraph in the Discussion about potential alternative explanations for our observations.

Author Response

Reviewer #1 (Public Review):

In this manuscript, May et al use H2B overexpression driven by Keratin14 Cre-mediated excision of a loxPstop cassette to quantify bulk chromatin dynamics in the live epidermis. They observe heterogeneity of H2B distribution within the basal stem cell layer and a change in distribution when the stem cells delaminate into the suprabasal layers. They further show that these chromatin rearrangements precede cell fate commitment, as detected by adding another Cre-mediated transgene on top (tetO-Cre mediated Keratin10 reporter). Finally, they generate an MST stem-loop transgene for the keratin 10 transcript and observe transcriptional bursting.

We would like to clarify for the reviewer that the H2B system used is a transgenic allele of histone-2B-GFP that is driven directly by the Keratin-14 promoter (Kanda et al., 1998; Tumbar et al., 2004). This system does not rely on any Cre-mediated excision of the LoxP-stop cassette, and these mice do not carry Cre alleles. We will touch on this point below when addressing the comment on Cre expression in cells and the raised question on whether it influences the quantifications of chromatin compaction.

The manuscript uses elegant in vivo imaging approaches to describe a set of observations that are logically based on a panel of studies that have used genetic approaches to dissect the role of heterochromatin and histone/DNA modifications in epidermal state transitions. In addition, the MST stem-loop analysis is a nice technical advance, confirming transcriptional bursting as a general phenomenon of how transcription is regulated in cells (see work from Daniel Larsson, Jonathan Chubb, Arjun Raj, and others).

We thank the reviewer for their recognition of our contribution to the transcription field. To deepen the connection between our data and previous characterizations of transcriptional dynamics in other systems, we have added new analyses of K10MS2 transcriptional bursting on a finer temporal scale (Fig 5G-K). We find pervasive “transcriptional bursting,” consistent with findings in vitro and in other model organisms, and a surprising variation of burst durations. We believe these additional analyses significantly strengthen our conclusions and the relevance of our study to the overall transcription field.

The value of the study in my view is recapitulating these known phenomena in a live tissue setting with high-quality imaging and careful quantification. Overall, the analyses appear thorough, although the overall changes appear relatively minor, which is perhaps to be expected from imaging bulk H2B distribution as a proxy for chromatin states.

There is one major technical concern that might impact the interpretation of the data. The authors combine Cre lines for their key conclusions (Krt10 reporter and SRF KO) and analyze single cells that thus express very high levels of Cre. Knowing that Cre will target non-loxP sites and is genotoxic, it is possible that the effect of chromatin is due to high levels of Cre expression in single cells rather than specific effects due to cell state transitions. I would encourage the authors to carefully quantify the dose-dependent effects of the Cre protein (independent of the LoxP sites) on chromatin organization. Along these lines, is the phenotype of the SRF KO similar in the presence of two Cre alleles versus just one?

Thank you for these kind words. This is an important potential caveat to consider. We believe that Cre activity does not significantly affect the chromatin compaction profiles for several reasons. First, we interrogated Cre activity. The quantifications in Figure 1A-E and Figure 2B-C are from mice containing K14H2B-GFP allele alone and do not carry any Cre allele. When these data were compared to those from mice that had been treated with a high dose of tamoxifen to induce Cre-mediated recombination in the vast majority of cells, the chromatin compaction profiles were not significantly different (Supp Fig 3C). We have added this comparison to Supplemental Figure 3 and addressed this point in the text (page 9). To further determine whether Cremediated recombination affects our measurement of chromatin compaction, we also analyzed adjacent basal cells with and without Cre activity in the same animal. K14H2BGFP; K14CreER; tdTomato mice were induced with a low dose of tamoxifen such that roughly 65% of epidermal cells underwent Cre recombination as demonstrated by expression of the tdTomato fluorescent reporter (Gallini et al., 2022). They also received a punch biopsy performed on the unimaged ear. Three days post injury and six days after Cre induction, the chromatin compaction profiles of cells positive and negative for Cre-mediated recombination were also not significantly different (Rebuttal Figure 1). Together, these direct comparisons between cells exposed to Cre activity and cells not exposed to Cre activity indicate that Cre activity at levels comparable to those used in our experiments has no measurable effect on our measurements of chromatin compaction.

Rebuttal Figure 1: Effect of Cre expression on chromatin compaction profiles

The second issue is the conclusion of "chromatin spinning". Concluding that chromatin is spinning would in my view require that the authors demonstrate that the nuclear envelope is not moving or is moving less than the chromatin. To support this conclusion the authors should do double imaging for example with LINC complex proteins, an ER/outer nuclear membrane marker, or equivalent.

This is an excellent point. While we expect that the entire nucleus is spinning based on observations others have made in in vitro fibroblasts systems, we describe our observation as “chromatin spinning” instead of “nuclear spinning” because the K14H2B-GFP allele only allows us to directly visualize chromatin itself (Kumar et al., 2014; Zhu et al., 2018).

Unfortunately, LINC complex proteins and nuclear membrane proteins have not been fluorescently tagged in mice, which prevents us from visualizing their dynamics in vivo. To establish these new tools and perform experiments would take more than a year, making it therefore beyond the scope of this current paper. Additionally, their relatively uniform distribution across the nuclear membrane would not allow us to visualize potential spinning of these components. We have made efforts towards the reviewer’s question by asking whether other compartments within the cell also spin in delaminating cells. To do this, we leveraged a mouse line developed by Claudio Franco’s lab (Barbacena et al., 2019), which fluorescently labels both the chromatin (H2B-GFP) and the Golgi (GTS-mCherry). As expected, this model showed a perinuclear and polarized Golgi in skin fibroblasts (Rebuttal Figure 2). However, this tool is incompatible with our questions in epidermal cells for a few reasons. First, the system is toxic to epithelial cells in vivo, resulting in apoptosis, nuclear fragmentation, and binucleate cells. Second, the Golgi is not discretely polarized (or even perinuclear) in epithelial cells (Rebuttal Figure 2). As such, although we observe chromatin spinning in delaminating basal cells, we are uncertain as to whether the whole nucleus or any other cellular compartments are spinning in these cells.

Rebuttal Figure 2: Interrogation of intracellular spinning

Given the above reasoning and efforts, we have altered the text and specified that we only have the capacity to visualize chromatin through the H2B-GFP allele and that we hypothesize the entire nucleus is spinning (page 11).

Reviewer #2 (Public Review):

In this work entitled "Live imaging reveals chromatin compaction transitions and dynamic transcriptional bursting during stem cell differentiation in vivo" the authors use a combination of genetic and imaging tools to characterize dynamic changes in chromatin compaction of cells undergoing epidermal stem cell differentiation and to relate chromatin compaction to transcriptional regulation in vivo. They track this phenomenon by imaging the epithelium at the ear of live mice, thus in a physiological context. By following individual nuclei expressing H2B-GFP along time ranges of hours and up to 3 days, they develop a strategy to quantify the profile of chromatin compaction across different epidermal layers based on normalized intensity profiles of H2B-GFP. They observe that cells belonging to the basal stem cell layer display a considerable level of internuclear variability in chromatin compaction that is cell-cycle independent. Instead, intercellular variability in chromatin compaction appears more related to the differentiation status of the cells as it is stable in the hours range but dynamic in the days range. The authors show that differentiated nuclei in the spinous layer exhibit higher chromatin compaction. They also identified a subset of cells in the basal stem layer with an intermediate profile of chromatin compaction and with the dynamic expression of the early differentiation marker keratin 10. Lastly, they show that the expression of keratin-10 precedes the chromatin compaction establishing relevant temporal relationships in the process of epidermal differentiation.

This work includes a number of challenging approaches and techniques since it is carried out in living mice. Also, it provides nice tools and methods to study chromatin structure in vivo during multiple days and within a differentiation physiological system. On the other hand, the results are descriptive and, in some respect, expected in line with previous observations.

Thank you very much for this great summary, kind words, and the recommendations listed below. We will address each of them specifically. We have also deepened the analysis of transcriptional dynamics in ways that are more comparable with how other groups have studied transcription and included those results in Figure 5.

References

Kanda, T., Sullivan, K.F., and Wahl, G.M. (1998). Histone–GFP fusion protein enables sensitive analysis of chromosome dynamics in living mammalian cells. Current Biology 8, 377–385. 10.1016/S09609822(98)70156-3.

Tumbar, T., Guasch, G., Greco, V., Blanpain, C., Lowry, W.E., Rendl, M., and Fuchs, E. (2004). Defining the epithelial stem cell niche in skin. Science 303, 359–363. 10.1126/science.1092436.

Kumar, A., Maitra, A., Sumit, M., Ramaswamy, S., and Shivashankar, G.V. (2014). Actomyosin contractility rotates the cell nucleus. Sci Rep 4, 3781. 10.1038/srep03781.

Zhu, R., Liu, C., and Gundersen, G.G. (2018). Nuclear positioning in migrating fibroblasts. Seminars in Cell & Developmental Biology 82, 41–50. 10.1016/j.semcdb.2017.11.006.

Sara Gallini, Nur-Taz Rahman, Karl Annusver, David G. Gonzalez, Sangwon Yun, Catherine Matte-Martone, Tianchi Xin, Elizabeth Lathrop, Kathleen C. Suozzi, Maria Kasper, Valentina Greco . Injury suppresses Ras cell competitive advantage through enhanced wild-type cell proliferation.<br /> bioRxiv 2022.01.05.475078; doi: https://doi.org/10.1101/2022.01.05.475078

Pedro Barbacena, Marie Ouarné, Jody J Haigh, Francisca F Vasconcelos, Anna Pezzarossa, Claudio A Franco. GNrep mouse: A reporter mouse for front-rear cell polarity. Genesis 2019 Jun. DOI: 10.1002/dvg.23299

Cristiana M Pineda, Sangbum Park, Kailin R Mesa, Markus Wolfel, David G Gonzalez, Ann M Haberman, Panteleimon Rompolas, Valentina Greco. Intravital imaging of hair follicle regeneration in the mouse. Nature Protocols 2015 July. DOI: 10.1038/nprot.2015.070

Author Response

Reviewer #1 (Public Review):

Reviewer 1 confirmed the view that your paper provides new insight into YTHDC1 function in regulating SC activation/proliferation but added that some of the data could be improved to fully support the conclusions. Specifically:

The title "Nuclear m6A Reader YTHDC1 Promotes Muscle Stem Cell Activation/Proliferation by Regulating mRNA Splicing and Nuclear Export" seems a bit overstated. Their data are not sufficient to show YTHDC1 regulating nuclear export. From figure 6 we could see some mRNAs export was inhibited upon YTHDC1 loss but intron retention also occurs on these mRNAs, for example, Dnajc14. Since intron retention could lead to mRNA nuclear retention, the mRNA export inhibition may be caused by splicing deficiency. From the data they provided we could not draw the conclusion that YTHDC1 directly affects mRNA export. I think they could not emphasize this point in the title.

Thanks for the suggestion. It is true that in our initial submission, we had more data to support YTHDC1 regulation of mRNA splicing but not enough on nuclear export. It will take substantial amount of time and efforts to have thorough dissection on both mechanisms. Nevertheless, we argue that our data does provide evidence on YTHDC1 regulation of nuclear export. For example, in Figures 6 C, H, and M, only ~20% of the target mRNAs (such as Dnaj14) showed alteration in both splicing and export upon YTHDC1 loss while the majority of the export targets showed no splicing deficiency. For example, Btbd7 and Tiparp in Figure 6 N showed no intron retention. In addition, we have now performed Co-IP experiments to validate the interaction between YTHDC1 and THOC7 (new result added in Figure 7L), which provides extra evidence to support YTHDC1 function in regulating mRNA nuclear export. We thus would like to keep the original title in order to reflect the multifaceted function of YTHDC1 in muscle stem cells.

The mechanism of YTHDC1 promoting muscle stem cell activation/proliferation is not solidified. The authors could strengthen their evidence through bioinformatics analysis or give more discussion. Besides, the previous work done by Zhao and colleagues (Zhao et al,. Nature 542, 475-478 (2017).) reported another m6A reader Ythdf2 promotes m6A-dependent maternal mRNA clearance to facilitate zebrafish maternal-to-zygotic transition. Does YTHDC1 regulate mRNA clearance during SC activation/proliferation? The authors should explore this possibility by deep-seq data analysis and give some discussion.

Thanks for the critical comment. For the first concern, we think YTHDC1 promotes muscle stem cell activation/proliferation through the multi-level gene regulatory capabilities of YTHDC1 on both transcriptional and post-transcriptional processes and the myriads of targets regulated by YTHDC1. In addition, with the newly added data, we believe that YTHDC1’s function is largely dependent on its synergism with hnRNPG (Figure 7 K). We have added the discussion in lines 421-427 of the revised text. For the second question, our data showed that YTHDC1 predominantly localizes in the nucleus of SCs and myoblasts (Figure 1 F&G), thus it may not have a role in regulating mRNA clearance in the cytoplasm like YTHDF2. Nevertheless, there are a few existing reports1, 2 suggesting its possible role in mRNA degradation and stability which may arise from its transient shuttling to cytoplasm of cells. We have now added this point in lines 469-472 of the revised text.

Reviewer #2 (Public Review):

Reviewer 2 was similarly positive stating that several tour-de-force techniques were used to examine m6A and the biological consequence in satellite cells and that there was a large amount of data supporting the conclusions with only a few minor weaknesses.

General points: The main body is lengthy, and some content can be reduced or condensed. For example, RNA-seq was used to determine gene expression in WT and cKO cells, but the purpose of this is not well justified given that YTHDC1 mainly functions to regulate splicing and nuclear expert of mRNA rather than controlling their expression levels. Does the RNA-seq data suggest that YTHDC1 may also regulate gene expression independent of m6A reader function?

Thanks for the comment. We have now revised the entire text to condense the content. Nevertheless, we must point out that the purpose of the RNA-seq is to provide extra evidence for the proliferation defect of the YTHDC1 KO cells but not to search for the underlying mechanism. We have now revised in lines 159-160 to clarify this.

Reference:

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2. Zhang, Z., Wang, Q., Zhao, X., Shao, L., Liu, G., Zheng, X., Xie, L., Zhang, Y., Sun, C. & Xu, R. YTHDC1 mitigates ischemic stroke by promoting Akt phosphorylation through destabilizing PTEN mRNA. Cell Death Dis 11, 977 (2020).
3. He, P.C. & He, C. m(6) A RNA methylation: from mechanisms to therapeutic potential. EMBO J 40, e105977 (2021).
4. Widagdo, J., Anggono, V. & Wong, J.J. The multifaceted effects of YTHDC1-mediated nuclear m(6)A recognition. Trends Genet 38, 325-332 (2022).
5. Sheng, Y., Wei, J., Yu, F., Xu, H., Yu, C., Wu, Q., Liu, Y., Li, L., Cui, X.L., Gu, X., Shen, B., Li, W., Huang, Y., Bhaduri-Mcintosh, S., He, C. & Qian, Z. A Critical Role of Nuclear m6A Reader YTHDC1 in Leukemogenesis by Regulating MCM Complex-Mediated DNA Replication. Blood (2021).
6. Cheng, Y., Xie, W., Pickering, B.F., Chu, K.L., Savino, A.M., Yang, X., Luo, H., Nguyen, D.T., Mo, S., Barin, E., Velleca, A., Rohwetter, T.M., Patel, D.J., Jaffrey, S.R. & Kharas, M.G. N(6)-Methyladenosine on mRNA facilitates a phase-separated nuclear body that suppresses myeloid leukemic differentiation. Cancer Cell 39, 958-972 e958 (2021).
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Author Response

Reviewer #1 (Public Review):

Laurent et al. generate genotyping data from 259 individuals from Cabo Verde to investigate the histories and patterns of admixture in the set of islands that make up Cabo Verde. The authors had previously studied admixture in an earlier study but in a smaller set of individuals from two cities on one island (from Santiago) in Cabo Verde. Here, the authors sample from all the islands of Cabo Verde to study admixture in these islands and reveal that there is a varied picture of admixture in that the demographic histories are distinct amongst this set of islands.

I found the article interesting and clearly written, and I like that it highlights that admixture is a dynamic process that has manifested differently in distinct geographical regions, which will be of broad interest. It also highlights how genetic ancestry patterns are correlated with the populations that were in power/enslaved during colonial times and proposes that certain social practices (e.g. legally enforced segregation) might have affected the distribution/length of runs of homozygosity.

We thank the reviewer for this positive and encouraging appreciation of our work.

My main suggestion is that the authors provide a set of hypotheses regarding admixture that may explain their observations, and it would be nice to see if at least one of these has some support using simulations. Could the authors run simulations under their proposed demographic model for populations in Cabo Verde vs what we would expect in a pseudo-panmictic population with two sources of admixture? The authors probably already have simulations they could use. And then see how pre/post admixture founding events change patterns of ancestry.

As suggested by the reviewer, in the revised version of the manuscript, we conducted the same MetHis-ABC scenario-choice and posterior parameter inference considering the 225 Cabo Verde-born individuals as a single random-mating population, in addition to our main results considering each island of birth separately. Most interestingly, we find that our ABC inferences fail to accurately reconstruct the detailed admixture history of Cabo Verde when considered as a whole instead of per each island of birth separately. This is due to admixture histories substantially differing across islands of birth of individuals, also consistent with the significantly differentiated genetic patterns within Cabo Verde obtained from ADMIXTURE, local-ancestry inferences, ROH, and isolation-by-distance analyses. These results are now implemented throughout the revised version of the manuscript and in supplementary figures and tables. See in particular Results L758-769, and Appendix1-figures and tables, Figure7-figure supplement 1-3, and Appendix 5-table 10.

Reviewer #2 (Public Review):

In this article, the authors leveraged patterns on the empirical genomic data and the power of simulations and statistical inferences and aimed to address a few biologically and culturally relevant questions about Cabo Verde population's admixture history during the TAST era. Specifically, the authors provided evidence on which specific African and European populations contributed to the population per island if the genetic admixture history parallels language evolution, and the best-fitting admixture scenario that answers questions on when and which continental populations admixed on which island, and how that influenced the island population dynamics since then.

Strengths

1) This study sets a great example of studying population history through the lens of genetics and linguistics, jointly. Historically most of the genetic studies of population history either ignored the sociocultural aspects of the evidence or poorly (or wrongly) correlated that with genetic inference. This study identified components in language that are informative about cultural mixture (strictly African-origin words versus shared European-African words), and carefully examined the statistical correlation between genetic and linguistic variation that occurred through admixture, providing a complete picture of genetic and sociocultural transformation in the Cabo Verde islands during TAST.

We thank the reviewer for this very enthusiastic and encouraging comment on our work.

2) The statistical analyses are carefully designed and rigorously done. I especially appreciate the careful goodness-of-fit checking and parameter error rates estimation in the ABC part, making the inference results more convincing.

Again, we thank the reviewer for this positive comment.

Weaknesses

1) Most of the methods in the main analyses here were previously developed (eg. MDS, MetHis, RF/NN-ABC). However, when being introduced and applied here, the authors didn't reinstate the necessary background (strength and weakness, limitations and usage) of these methods to make them justifiable over other methods. For example, why ADS-MDS is used here to examine the genetic relationship between Cabo Verde populations and other worldwide populations, rather than classic PCA and F-statistics?

As mentioned in the answer to the general comments, we extensively modified our manuscript in both Results and Material and Methods, to clarify and justify our reasoning for each one of the analyses conducted, and to discuss pros and cons of the methods used. We warmly thank the reviewers for this request, as we believe it allowed us to strongly improve the accessibility of our work in particular for the less specialized audience, as well as equally crucially improve replicability of our work for specialists. See in particular Results L185-193, L245-250, L368-371, L380-386, L495-511, L567-571, L606-621, and the corresponding Material and Methods sections.

For the particular example of PCA raised by the reviewer: see Results L185-193.

For that of F-statistics, see Results L368-386. Note that we added the F-stat analysis suggested by the reviewer to the revised version of our manuscript (see detailed answers below), Figure 3-figure supplement 2.

We believe that these changes strongly strengthen our manuscript and enlarged its potential readership, and we thank, again, the reviewer for this request.

2) The senior author of this paper has an earlier published article (Verdu et al. 2017 Current Biology) on the same population, using a similar set of methods and drew similar conclusions on the source of genetic and linguistic variation in Cabo Verde. Although additional samples on island levels are added here and additional analyses on admixture history were performed, half of the main messages from this paper don't seem to provide new knowledge than what we already learned from the 2017 paper.

We substantially modified the text of the revised version of the manuscript to address the concern raised by the reviewer in numerous locations of the Abstract, Introduction and Results and Discussion sections, thus hoping to highlight better what we think is the profound novelty brought by this study. In particular, see Introduction L128-153.

3) Furthermore, there are a few essential factors that could confound different aspects of the major analyses in this article that I believe should be taken into account and discussed. Such factors include the demographic history of source populations prior to admixture, different scenarios of the recipient population size changes, differences in recombination rates across the genome and between African and European populations, etc.

We thank the reviewer for these comments which allowed us to improve the clarity of our manuscript and rise very interesting discussion points that we had overlooked. As indicated in part in the general answer to reviewers above:

1) We clarified our methods’ design and discussed extensively its limitations with respect to ancestral populations’ sizes mis-specifications. Indeed, ancestral source population sizes are not modelized in our MetHis-ABC approach. Instead, we consider that the observed proxy source populations from Africa and Europe are at the drift-mutation equilibrium and are large since the initial and recent founding of Cabo Verde in the 1460’s, and thus use observed genetic variation patterns in these populations to build virtual gamete reservoirs for the admixture history of Cabo Verde with the MetHis-ABC framework. Therefore, while we cannot evaluate explicitly the influence of ancestral source population sizes differences on our inferences in Cabo Verde, as we now state in the revised version of our manuscript: “we nevertheless implicitly take the real demographic histories of these source populations into account in our simulations, as we use observed genetic patterns themselves the product of this demographic history to create the virtual source populations at the root of the admixture history of each Cabo Verdean island.”. We then discuss the outcome of such an approach which mimics satisfactorily the real data for ABC inference. See in particular the revised versions of the Material and Methods L1454-1491 novel section “Simulating the admixed population from source-populations for 60,000 independent SNPs with MetHis”, and Results L637-649.

2) Concerning the possibilities for population-size changes in the admixed population in our simulations and ABC inferences, we clarified our Material and Methods and explanations of our Results to better show that we readily consider various possible scenarios (for each island separately). Indeed, with our MetHis simulation design, given values of model-parameters correspond either to a constant, a linearly increasing, or a hyperbolic increase in reproductive size in the admixed population over time. We further clarified our Results and Discussion pointing out that we find, a posteriori, indeed, different demographic regimes among islands.

Nevertheless, reviewers are right that we did not test the possibility for bottlenecks. We thus substantially expanded the Results and Discussion sections in multiple locations to highlight this limitation and the challenges involved in overcoming it in future work. See in particular Material and Methods L1386-1404 section “Hyperbolic increase, linear increase, or constant reproductive population size in the admixed population”, Results L739-742, and Discussion L934-941, and Perspectives.

3) Finally, concerning recombination rate, we considered only independent SNPs in our simulation and inference process, as is now clarified in multiple locations throughout the text. Otherwise, we further discuss matters of recombination concern regarding specifically our ROH analyses, as suggested in the detailed reviewer’s comments. In brief, we note that in Figure 8 Pemberton 2012 (AJHG 91:275-292) shows that occurrence of long ROH at the same genomic location across individuals is correlated with low recombination rates, although the effect is relatively weak unless in extreme recombination cold spots. Unless there were many extreme recombination cold spots that were different among the islands or ancestral populations, we anticipate fine-scale recombination rate differences not to matter very much for total ROH levels in these data. Similarly, we do not expect large genome-wide differences in mutation rate, and therefore we don’t anticipate minor local variation in mutation rates to make a systematic difference in total ROH levels. We now refer to these important points in the revised version of our Results L414-415.

Overall, the paper is of interest to the field of human evolutionary genetics - that not only does it tell the story of a historically important population, but also the methodology behind this paper sets a great example for future research to study genetic and sociocultural transformations under the same framework.

We would like to thank the reviewer for this very encouraging conclusion and for the detailed revision of our work which, we believe, helped us to substantially improve our manuscript.

Author Response

Reviewer #1 (Public Review):

1) The heat shock effect in the drosophila lines was not understood in the study. Why did some lines show phenotypes only at 29C but not 22C? The study showed data that ubiquilin 2 expression was not impacted by 29C, then what caused the phenotypic differences? In addition, the method section did not describe clearly whether a temperature sensitive promoter was used in the flies.

The heat inducibility of the UBQLN2 transgenes is likely attributed to heat shock elements in the UAS promoter as noted in on page 6, line 4-14. The heat inducibility of dUbqln is interesting and may reflect transcriptional and/or posttranscriptional mechanisms. While it is possible that increased UBQLN2 contributes to the severe phenotypes in UBQLN24XALS flies reared at 29C; this is not seen for UBQLN2WT and UBQLN2P497H flies. Instead, we postulate that heat stress synergizes with the misfolded UBQLN24XALS protein to disrupt proteostasis and/or endolysosomal function. This clarification has been added to paragraph 2 of the Discussion (page 16, line 15-25) section of the revised MS: “The reason for enhanced toxicity of UBQLN24XALS is unclear; however, its enhanced aggregation potential may overwhelm cellular proteostasis machinery and/or accelerate disease mechanisms that are slow to manifest in neurons harboring ALS point mutations. This is consistent with the fact that UBQLN24XALS toxicity in flies was unmasked by HS, which is a well-known inducer of proteotoxicity.” We have also explicitly state the HS inducibility of the UAS-Gal4 in the revised Materials and methods (page 20, line 24-25).

2) The study showed data on male and female flies separately in some but not all experiments. In addition, the manuscript largely avoided discussing whether there was a sex difference in those experiments.

We showed separate male and female eye phenotypes in Figure 1 to clearly demonstrate that UBQLN24XALS toxicity is not sex dependent. Subtle sex differences were seen in the longevity and climbing assays and were reported in figures 4A and 4D. In Figure 4D, Unc-5 silencing extended the lifespan of Elav>Gal4 female control flies but not Elav>Gal4 male control flies. In Figure 4A, an Unc-5 KK RNAi line rescued climbing of D42>UBQLN24XALS male flies, but not female flies (a second Unc-5 RNAi line rescued both males and females). The reasons for sex differences in these specific experiments is unclear.

3) Some data appear to be peripheral with no significant contribution to the main findings. Moreover, some data were introduced but were not explained. For instance, the RNA-Seq analysis (Fig 2) did not contribute much to the study. The rescue effect of UBA* (F594A mutant) in Fig 1-Supplemental 1B was interesting but was not elaborated or followed up. FUS flies in Fig 6-Supplement 2 were abrupted introduced with little discussion.

We understand the reviewer’s point or the reviewer’s point is well taken. Appreciating the reviewer’s comment, we moved both figures to the supplementary data.

RNA-Seq (Fig. 2)

Although not essential, the RNA-Seq adds experimental rigor to the study by providing strong molecular correlates to eye degeneration phenotypes across different UBQLN2 genotypes. It shows the unique toxicity of UBQLN24XALS and reinforces phenotypic similarity between UBQLN2WT and UBQLN2P497H flies, which likely reflects non-specific toxicity of overexpressed UBQLN2 proteins. We have carried out additional data analyses requested by the reviewer and moved the RNA-Seq data to Figure 1-figure supplement 2.

UBA mutant (Figure1-figure supplement 1)

Both aggregation and toxicity of UBQLN24XALS were abolished by an inactivating F594A mutation in the UBA domain. While this implicates Ub binding in the biochemical mechanism of UBQLN2 toxicity, we have not followed up on the finding in either fly or iMN models and have chosen to remove the data (Figure1-figure supplement 1) from the revised MS.

Lack of genetic interaction between FUS and Unc-5 (Figure 3-figure supplement 1).

This data was included to show that shUnc-5 is not a general suppressor of eye toxicity in Drosophila. This contrasts with lilliputian, whose mutation rescues toxicity phenotypes elicited by FUS, TDP-43, and UBQLN2. We believe that the FUS control data enhances experimental rigor and have retained the data in the revised MS, with some additional clarification on page 10, line 5-8.

4) The main quadrupole (4XALS) mutation used in the study was not found in patients. The relevance of the findings needs to be thoroughly justified.

The use of combinatorial mutants—either in the same gene or same pathway—can sometimes be used to enhance neurodegenerative phenotypes in cellular and rodent models for neurodegenerative diseases, most notably, Alzheimer’s Disease. In the case of the 4XALS mutant, we reasoned that its enhanced aggregation might drive stronger phenotypes than those elicited by UBQLN2 clinical alleles, whose toxicity is barely discernible in flies (relative to overexpressed UBQLN2WT) or in iMNs. We have clarified the rationale for testing the 4XALS mutant and articulated its potential strengths and weaknesses in Results (page 5, line 14-page 6, line 2) and Discussion (page 16, line 15-25) sections.

5) ALS and FTD are age-related neurodegenerative diseases, whereas the involvement of axon guidance genes in indicative of disruptions during the developmental stage. The manuscript did not discuss this potential caveat.

We have inserted the following sentence in the discussion to note this caveat: “Consistent with this notion, UNC5B has been linked to neurodegeneration in the 6-OHDA model of Parkinson’s Disease (PD) and UNC5C has been nominated as a risk allele in late-onset Alzheimer’s Disease. Defining the contributions of pathologic UNC5 signaling to the development or progression of ALS-dementia awaits further study.” on Page 20, line 2-6. We have added a similar sentence to the Limitations paragraph at the end of the Discussion: “Third, it is possible that axon guidance genes are only relevant to UBQLN2 toxicity in the context of the developing nervous system”.

Author Response

Reviewer #1 (Public Review):

This work describes a new method, Proteinfer, which uses dilated neural networks to predict protein function, using EC terms and GO terms. The software is fast and the server-side performance is fast and reliable. The method is very clearly described. However, it is hard to judge the accuracy of this method based on the current manuscript, and some more work is needed to do so.

I would like to address the following statement by the authors: (p3, left column): "We focus on Swiss Prot to ensure that our models learn from human-curated labels, rather than labels generated by electronic annotation".

There is a subtle but important point to be made here: while SwissProt (SP) entries are human-curated, they might still have their function annotated ("labeled") electronically only. The SP entry comprises the sequence, source organism, paper(s) (if any), annotations, cross-references, etc. A validated entry does not mean that the annotation was necessarily validated manually: but rather that there is a paper backing the veracity of the sequence itself, and that it is not an automatic generation from a genome project.

Example: 009L_FRG3G is a reviewed entry, and has four function annotations, all generated by BLAST, with an IEA (inferred by electronic annotation) evidence code. Most GO annotations in SwissProt are generated that way: a reviewed Swissprot entry, unlike what the authors imply, does not guarantee that the function annotation was made by non-electronic means. If the authors would like to use non-electronic annotations for functional labels, they should use those that are annotated with the GO experimental evidence codes (or, at the very least, not exclusively annotated with IEA). Therefore, most of the annotations in the authors' gold standard protein annotations are simply generated by BLAST and not reviewed by a person. Essentially the authors are comparing predictions with predictions, or at least not taking care not to do so. This is an important point that the authors need to address since there is no apparent gold standard they are using.

The above statement is relevant to GO. But since EC is mapped 1:1 to GO molecular function ontology (as a subset, there are many terms in GO MFO that are not enzymes of course), the authors can easily apply this to EC-based entries as well.

This may explain why, in Figure S8(b), BLAST retains such a high and even plateau of the precision-recall curve: BLAST hits are used throughout as gold-standard, and therefore BLAST performs so well. This is in contrast, say to CAFA assessments which use as a gold standard only those proteins which have experimental GO evidence codes, and therefore BLAST performs much poorer upon assessment.

We thank the reviewer for this point. We regret if we gave the impression that our training data derives exclusively, or even primarily, from direct experiments on the amino acid sequences in question. We had attempted to address this point in the discussion with this section:

"On the other hand, many entries come from experts applying existing computational methods, including BLAST and HMM-based approaches, to identify protein function. Therefore, the data may be enriched for sequences with functions that are easily ascribable using these techniques which could limit the ability to estimate the added value of using an alternative alignment-free tool. An idealised dataset would involved training only on those sequences that have themselves been experimentally characterized, but at present too little data exists than would be needed for a fully supervised deep-learning approach."

We have now added a sentence in the early sentence of of the manuscript reinforcing this point:

"Despite its curated nature, SwissProt contains many proteins annotated only on the basis of electronic tools."

We have also removed the phrase "rather than labels generated by a computational annotation pipeline" because we acknowledge that this could be read to imply that computational approaches are not used at all for SwissProt which would not be correct.

While we agree that SwissProt contains many entries inferred via electronic means, we nevertheless think its curated nature makes an important difference. Curators as far as possible reconcile all known data for a protein, often looking for the presence of key residues in the active sites. There are proteins where electronic annotation would suggest functions in direct contradiction to experimental data, which are avoided due to this curation process. As one example, UniProt entry Q76NQ1 contains a rhomboid-like domain typically found in rhomboid proteases (IPR022764) and therefore inputting it into InterProScan results in a prediction of peptidase activity (GO:0004252). However this is in fact an inactive protein, as discovered by experiment, and so is not annotated with this activity in SwissProt. ProteInfer successfully avoids predicting peptidase activity as a result of this curated training data. (For transparency, ProteInfer is by no means perfect on this point: there are also cases in which UniProt curators have annotated single proteins as inactive but ProteInfer has not learnt this relationship, due to similar sequences which remain active).

We had also attempted to address this point by comparing with phenotypes seen in a specific high-throughput experimental assay ("Comparison to experimental data" section).

We have now added a new analysis in which we assess the recall of GO terms while excluding IEA annotation codes. We find that at the threshold that maximises F1 score in the full analysis, our approach is able to recall 60-75% (depending on ontology) of annotations. Inferring precision is challenging due to the fact that only a very small proportion of the possible function*gene combinations have in fact been tested, making it difficult to distinguish a true negative from a false negative.

"We also tested how well our trained model was able to recall the subset of GO term annotations which are not associated with the "inferred from electronic annotation" (IEA) evidence code, indicating either experimental work or more intensely-curated evidence. We found that at the threshold that maximised F1 score for overall prediction, 75% of molecular function annotations could be successfully recalled, 61% of cellular component annotations, and 60% of biological process annotations."

Pooling GO DAGs together: It is unclear how the authors generate performance data over GO as a whole. GO is really 3 disjoint DAGs (molecular function ontology or MFO, Biological Process or BPO, Cellular component or CCO). Any assessment of performance should be over each DAG separately, to make biological sense. Pooling together the three GO DAGs which describe completely different aspects of the function is not informative. Interestingly enough, in the browser applications, the GO DAG results are distinctly separated into the respective DAGs.

Thank you for this suggestion. To answer the question of how we were previously generating performance data: this was simply by treating all terms equivalently, regardless of their ontology.

We agree that it would be helpful to the reader to split out results by ontology type, especially given clear differences in performance.

We now provide PR-curve graphs split by ontology type.

We have also added the following text:

"The same trends for the relative performance of different approaches were seen for each of the direct-acyclic graphs that make up the GO ontology (biological process, cellular component and molecular function), but there were substantial differences in absolute performance (Fig S10). Performance was highest for molecular function (max F1: 0.94), followed by biological process (max F1:0.86) and then cellular component (max F1:0.84)."

Figure 3 and lack of baseline methods: the text refers to Figures 3A and 3B, but I could only see one figure with no panels. Is there an error here? It is not possible at this point to talk about the results in this figure as described. It looks like Figure 3A is missing, with Fmax scores. In any case, Figure 3(b?) has precision-recall curves showing the performance of predictions is the highest on Isomerases and lowest in hydrolases. It is hard to tell the Fmax values, but they seem reasonably high. However, there is no comparison with a baseline method such as BLAST or Naive, and those should be inserted. It is important to compare Proteinfer with these baseline methods to answer the following questions: (1) Does Proteinfer perform better than the go-to method of choice for most biologists? (2) does it perform better than what is expected given the frequency of these terms in the dataset? For an explanation of the Naive method which answers the latter question, see: ( https://www.nature.com/articles/nmeth.2340 )

We apologise for the errors in figure referencing in the text here. This emerged in part from the two versions of text required to support an interactive and legacy PDF version. We had provided baseline comparisons with BLAST in Fig. 5 of the interactive version (correctly referenced in the interactive version) and in Fig. S7 of the PDF version (incorrectly referenced as Fig 3B).

We have now moved the key panel of Fig S7 to the main-text of the PDF version (new Fig 3B), as suggested also by the editor, and updated the figure referencing appropriately. We have also added a Naive frequency-count based baseline. This baseline would not appear in Fig 3B due to axis truncation, but is shown in a supplemental figure, new Fig S9. We thank the reviewer and the editor for raising these points.

Reviewer #2 (Public Review):

In this paper, Sanderson et al. describe a convolutional neural network that predicts protein domains directly from amino acid sequences. They train this model with manually curated sequences from the Swiss-Prot database to predict Enzyme Commission (EC) numbers and Gene Ontology (GO) terms. This paper builds on previous work by this group, where they trained a separate neural network to recognize each known protein domain. Here, they train one convolutional neural network to identify enzymatic functions or GO terms. They discuss how this change can deal with protein domains that frequently co-occur and more efficiently handle proteins of different lengths. The tool, ProteInfer, adds a useful new tool for computational analysis of proteins that complements existing methods like BLAST and Pfam.

The authors make three claims:

1) "ProteInfer models reproduce curator decisions for a variety of functional properties across sequences distant from the training data"

This claim is well supported by the data presented in the paper. The authors compare the precision-recall curves of four model variations. The authors focus their training on the maximum F1 statistic of the precision-recall curve. Using precision-recall curves is appropriate for this kind of problem.

2) "Attribution analysis shows that the predictions are driven by relevant regions of each protein sequence".

This claim is very well supported by the data and particularly well illustrated by Figure 4. The examples on the interactive website are also very nice. This section is a substantial innovation of this method. It shows the value of scanning for multiple functions at the same time and the value of being able to scan proteins of any length.

3) "ProteInfer models create a generalised mapping between sequence space and the space of protein functions, which is useful for tasks other than those for which the models were trained."

This claim is also well supported. The print version of the figure is really clear, and the interactive version is even better. It is a clever use of UMAP representations to look at the abstract last layer of the network. It was very nice how each sub-functional class clustered.

The interactive website was very easy to use with a good user interface. I expect will be accessible to experimental and computational biologists.

The manuscript has many strengths. The main text is clearly written, with high-level descriptions of the modeling. I initially printed and read the static PDF version of the paper. The interactive form is much more fun to read because of the ability to analyze my favorite proteins and zoom in on their figures (e.g. Figure 8). The new Figure 1 motivates the work nicely. The website has an excellent interactive graphic showing how the number of layers in the network and the kernel size change how data is pooled across residues. I will use this tool in my teaching.

We are grateful for these comments. We are excited that the reviewer hopes to use this figure for teaching, which is exactly the sort of impact we hoped for this interactive manuscript. We agree that the interactive manuscript is by far the most compelling version of this work.

The manuscript has only minor weaknesses. It was not clear if the interactive model on the website was the Single CNN model or the Ensemble CNN model.

We thank the reviewer for pointing out the ambiguity here. The model shown on the website is a Single CNN model, and is chosen with hyperparameters that achieve good performance whilst being readily downloadable to the user's machine for this demonstration without use of excessive bandwidth. We have added additional sentences to address this better in the manuscript.

" When the user loads the tool, lightweight EC (5MB) and GO model (7MB) prediction models are downloaded and all predictions are then performed locally, with query sequences never leaving the user's computer. We selected the hyperparameters for these lightweight models by performing a tuning study in which we filtered results by the size of the model's parameters and then selected the best performing models. This approach uses a single neural network, rather than an ensemble. Inference in the browser for a 1500 amino-acid sequence takes < 1.5 seconds for both models "

Overall, ProteInfer will be a very useful resource for a broad user base. The analysis of the 171 new proteins in Figure 7 was particularly compelling and serves as a great example of the utility and power of ProteInfer. It completes leading tools in a very valuable way. I anticipate adding it to my standard analysis workflows. The data and code are publicly available.

Reviewer #3 (Public Review):

In this work, the authors employ a deep convolutional neural network approach to map protein sequence to function. The rationales are that (i) once trained, the neural network would offer fast predictions for new sequences, facilitating exploration and discovery without the need for extensive computational resources, (ii) that the embedding of protein sequences in a fixed-dimensional space would allow potential analyses and interpretation of sequence-function relationships across proteins, and (iii) predicting protein function in a way that is different from alignment-based approaches could lead to new insights or superior performance, at least in certain regimes, thereby complementing existing approaches. I believe the authors demonstrate i and iii convincingly, whereas ii was left open-ended.

A strength of the work is showing that the trained CNNs perform generally on par with existing alignment based-methods such as BLASTp, with a precision-recall tradeoff that differs from BLASTp. Because the method is more precise at lower recall values, whereas BLASTp has higher recall at lower precision values, it is indeed a good complement to BLASTp, as demonstrated by the top performance of the ensemble approach containing both methods.

Another strength of the work is its emphasis on usability and interpretability, as demonstrated in the graphical interface, use of class activation mapping for sub-sequence attribution, and the analysis of hierarchical functional clustering when projecting the high-dimensional embedding into UMAP projections.

We thank the reviewer for highlighting these points.

However, a main weakness is the premise that this approach is new. For example, the authors claim that existing deep learning "models cannot infer functional annotation for full-length protein sequences." However, as the proposed method is a straightforward deep neural network implementation, there have been other very similar approaches published for protein function prediction. For example, Cai, Wang, and Deng, Frontiers in Bioengineering and Biotechnology (2020), the latter also being a CNN approach. As such, it is difficult to assess how this approach differs from or builds on previous work.

We agree that there has been a great deal of exciting work looking at the application of deep learning to protein sequences. Our core code has been publicly available on GitHub since April 2019 , and our preprint has now been available for more than a year. We regret the time taken to release a manuscript and for it to reach review: this was in part due to the SARS-CoV-2 pandemic, which the first author was heavily involved in the scientific response to. Nevertheless, we believe that our work has a number of important features that distinguish it from much other work in this space.

● We train across the entire GO ontology. In the paper referenced by the reviewer, training is with 491 BP terms, 321 MF terms, and 240 CC terms. In contrast, we train with a vocabulary of 32,102 GO labels, and the majority of these are predicted at least once in our test set. ● We use a dilated convolutional approach. In the referenced paper the network used is instead of fixed dimensions. Such an approach means there is an upper limit on how large a protein can be input into the model, and also means that this maximum length defines the computational resources used for every protein, including much smaller ones. In contrast, our dilated network scales to any size of protein, but when used with smaller input sequences it performs only the calculations needed for this size of sequence.

● We use class-activation mapping to determine regions of a protein responsible for predictions, and therefore potentially involved in specific functions.

● We provide a TensorFlow.JS implementation of our approach that allows lightweight models to be tested without any downloads

● We provide a command-line tool that provides easy access to full models.

We have made some changes to bring out these points more clearly in the text:

"Since natural protein sequences can vary in length by at least three orders of magnitude, this pooling is advantageous because it allows our model to accommodate sequences of arbitrary length without imposing restrictive modeling assumptions or computational burdens that scale with sequence length. In contrast, many previous approaches operate on fixed sequence lengths: these techniques are unable to make predictions for proteins larger than this sequence length, and use unnecessary resources when employed on smaller proteins."

We have added a table that sets out the vocabulary sizes used in our work (5,134 for EC and 32,109 for GO):

"Gene Ontology (GO) terms describe important protein functional properties, with 32,109 such terms in Swiss-Pr ot (Table S6) that cov er the molecular functions of proteins (e.g. DNA-binding, amylase activity), the biological processes they are involved in (e.g. DNA replication, meiosis), and the cellular components to which they localise (e.g. mitochondrion, cytosol)."

A second weakness is that it was not clear what new insights the UMAP projections of the sequence embedding could offer. For example, the authors mention that "a generalized mapping between sequence space and the space of protein functions...is useful for tasks other than those for which the models were trained." However, such tasks were not explicitly explained. The hierarchical clustering of enzymatic proteins shown in Fig. 5 and the clustering of non-enzymatic proteins in Fig. 6 are consistent with the expectation of separability in the high-dimensional embedding space that would be necessary for good CNN performance (although the sub-groups are sometimes not well-separated. For example, only the second level and leaf level are well-separated in the enzyme classification UMAP hierarchy). Therefore, the value-added of the UMAP representation should be something like using these plots to gain insight into a family or sub-family of enzymes.

We thank the reviewer for highlighting this point. There are two types of embedding which we discuss in the paper. The first is the high-dimensional representation of the protein that the neural network constructs as part of the prediction process. This is the embedding we feel is most useful for downstream applications, and we discuss a specific example of training the EC-number network to recognise membrane proteins (a property on which it was not trained): "To quantitatively measure whether these embeddings capture the function of non-enzyme proteins, we trained a simple random forest classification model that used these embeddings to predict whether a protein was annotated with the intrinsic component of membrane GO term. We trained on a small set of non-enzymes containing 518 membrane proteins, and evaluated on the rest of the examples. This simple model achieved a precision of 97% and recall of 60% for an F1 score of 0.74. Model training and data-labelling took around 15 seconds. This demonstrates the power of embeddings to simplify other studies with limited labeled data, as has been observed in recent work (43, 72)."

As the reviewer points out, there is a second embedding created by compressing this high-dimensional down to two dimensions using UMAP. This embedding can also be useful for understanding the properties seen by the network, for example the GO term s highlighted in Fig. 7 , but in general it will contain less information than the higher-dimensional embedding.

The clear presentation, ease of use, and computationally accessible downstream analytics of this work make it of broad utility to the field.

Author Response

Reviewer #1 (Public Review):

The manuscript by Kschonsak et al. describes the rational structure-based design of novel hybrid inhibitors targeting human Nav1.7 channel. CryoEM structure of arylsulfonamide (GNE-3565) - VSD4 NaV1.7-NaVPas channel complex confirmed binding pose observed in x-ray structure GX-936 - VSD4 Nav1.7-NavAb channel. Remarkably, cryoEM structure of acylsulfonamide (GDC-0310) - VSD4 NaV1.7-NaVPas channel complex revealed a novel binding pocket between the S3 and S4 helices, with the S3 segment adopting a distinct conformation compared to the arylsulfonamide (GNE-3565) - VSD4 NaV1.7-NaVPas channel complex. Creatively, the authors designed a novel class of hybrid inhibitors that simultaneously occupy both the aryl- and acylsulfonamide binding pockets. This study underscores the power of structure-guided drug design to target transmembrane proteins and will be useful to develop safer and more effective therapeutics.

We thank this Reviewer for the very positive feedback and for highlighting the importance of our work in utilizing structure-based drug design to target key membrane targets.

Reviewer #2 (Public Review):

In this manuscript, the authors identify a critical unmet need for the (structure-based) drug design of human Nav channels, which are of clinical interest. They cleverly rationalized a hybrid strategy for developing target-specific small molecule inhibitors, which integrate binding mechanisms of two drug candidates that act orthogonally on the VSD4 of Nav 1.7. Thus, the authors illustrate a promising outlook on pharmaceutical intervention on Nav channels.

Overall, the cryo-EM structures of the ligand-bound Nav channels are convincing, with a clear indication of the site-specific, distinct density of the small molecules. At the moment, it is difficult to tell how innovative the pipeline is compared to conventional cryo-EM structure determination.

We thank this Reviewer for this positive comments and for the very helpful suggestions. We are addressing the concerns regarding our cryoEM pipeline.

Reviewer #3 (Public Review):

This is an excellent manuscript, describing a few lines of discoveries:

1. Establishment of a structural biological pipeline for iterative structural determination of an engineered Nav1.7;

2. Illumination of the novel compound binding mode;

3. Structure-based development of the hybrid compounds, which led to the novel Nav1.7 inhibitor;

The cryo-EM study on the engineered Nav1.7 consistently reveals the map at the mid to low 2 Å range, which is unprecedented and impressive, thus, demonstrating the high value of this workflow. The further strength of this study is that the authors were able to develop a new compound by combining structural information gained from the two Nav1.7 structures complexed to two different compounds with different binding modes. Overall, the depth and quality of this study are excellent.

We thank this Reviewer for highlighting the importance of this manuscript and specifically recognizing our accomplishments in enabling iterative high-resolution structure for this target which allowed us to perform SBDD and design a new series of hybrid compounds. We are also grateful for indicating the excellence of our studies.

Author Response

Reviewer #1 (Public Review):

In this manuscript, McQuate et al. use serial block face SEM to provide a high resolution, 3D analysis of mitochondrial structure in hair cells and surrounding supporting cells of the zebrafish lateral line. They first demonstrate that hair cells have a higher mitochondrial volume as compared to supporting cells, which likely reflects the high metabolic load of these sensory cells. Their deeper analysis of mitochondrial morphology in hair cells reveals that the base of the hair cell - near the presynapse is dominated by a large, networked mitochondrion, while the apex of the cell is dominated by many small mitochondria. By examining hair cells at different stages of development, the authors show that specialized features of hair cell mitochondria are gradually established over the course of development. Finally, by examining hair cells in mutants that lack mechanosensation or presynaptic calcium responses, McQuate et al. reveal that cellular activity contributes to the development of appropriate mitochondrial morphology and localization within hair cells. This dataset, which will be made publicly available, is an immense resource to the community and will facilitate the generation of novel hypotheses about hair cell mitochondrial function in health and disease.

Strengths:

1. The painstaking acquisition and analysis of hair cell EM data in a genetically tractable system that is easily accessible for in vivo functional experiments to address hypotheses that emerge from this work.

2. The use of multiple datasets and analysis methods to cross-validate results.

3. The thoughtful, careful analysis of the data highlights the richness of the dataset.

4. The use of both wild-type and mutant animals substantially adds to the manuscript, providing significantly more insight than wild-type data alone.

Weaknesses:

1. The manuscript could more strongly highlight the utility of this dataset and facilitate its future use by providing a summary table that lists each sample together with salient details.

2. The authors examine an opa-1 mutant with altered mitochondrial fission (which consequently has changes in mitochondrial morphology and organization) to suggest that aberrant mitochondrial architecture negatively impacts mitochondrial function. However, mitochondrial fusion is thought to be critical for mitochondrial health beyond just altered architecture. Because fusion has other roles, it is difficult to use this manipulation to conclude that it is simply disruptions in mitochondrial architecture that alters function.

3. Although the work of acquiring and reconstructing EM data is labor-intensive, ideally, multiple fish would be examined for each genotype. Readers should take into consideration that one of the mutant datasets is derived from just one animal.

We thank Reviewer 1 for pointing out the “painstaking acquisition” that went into this study, the “thoughtful, careful analysis,” and the “richness of the dataset.” We believe we have addressed the aforementioned weaknesses.

Reviewer #2 (Public Review):

Sensory hair cells have high metabolic demands and rely on mitochondria to provide energy as well as regulate homeostatic levels of intracellular calcium. Using high-resolution serial block face SEM, the authors examined the influences of both developmental age and hair cell activity on hair cell mitochondrial morphology. They show that hair cell mitochondria develop a regionally specific architecture, with the highest volume mitochondria localized to the basolateral presynaptic region of hair cells. Data obtained from mutants lacking either mechanotransduction or presynaptic calcium influx provide evidence that hair cell activity shapes regional mitochondrial morphology. These observed specializations in mitochondrial morphology may play an important role in mitochondrial function, as mutants showing disrupted hair cell mitochondrial architecture showed depolarized mitochondrial potentials and impaired evoked mitochondrial calcium influx.

This work provides novel and intriguing evidence that mechanotransduction and presynaptic calcium influx play important roles in shaping subcellular mitochondrial morphology in sensory hair cells. Yet there was a lack of consistency in the analysis and presentation of the data which made it difficult to contextualize and interpret the results. This study would be greatly strengthened by i) consistent definitions for hair cell maturation, ii) comparable data analysis of cav1.3a mutant and cdh23 mutant mitochondrial morphologies, and iii) more detailed descriptions and interpretations of the UMAP analysis.

We thank Reviewer #2 for thinking the work is “novel and intriguing”. We have addressed the weaknesses raised.

Reviewer #3 (Public Review):

McQuate et al have succeeded in reconstructing 3D images of mitochondria and discovered unique structural features of mitochondria in zebrafish hair cells. Compared to the other cell types, such as central and peripheral support cells, Hair cells have many elongated and connected mitochondria and they seem to be involved in hair cell and ribbon synapses development. These findings will contribute to understanding the mechanisms for mitochondrial network regulation.

Using the SBFSEM technique, the authors provide clear 3D images of hair cells and the technique improves the resolution of the image to understand the structural parameters of not only mitochondria but also ribbon synapses compared to typical fluorescent imaging. These results are very attractive and have the high potential to broadly apply to 3D imaging of any type of organelles, cells, and tissues. On the other hand, however, the authors provide the data from a small sample size, and the functional experiments to make a conclusion are lacking. Some missing representative images and the nonunified methods of grouping for the analysis make the reviewer concerned.

We thank the Reviewer for thinking the results are “very attractive and have the high potential to broadly apply to 3D imaging of any type or organelles, cell, and tissues.” We agree. We have addressed the weaknesses raised

Author Response

Reviewer #1 (Public Review):

The article from Dumoux et al. shows the use of plasma-based focused ion beams for volume imaging on cryo-preserved samples. This exciting application can potentially increase the throughput and quality of the data acquired through serial FIB-SEM tomography on cryo-preserved and unstained biological samples. The article is well-written, and it is easy to follow. I like the structure and the experimental description, but I miss some points in the analyses, without which the conclusions are not adequately supported.

The authors state the following: "the application of serial FIB/SEM imaging of non-stained cryogenic biological samples is limited due to low contrast, curtaining, and charging artefacts. We address these challenges using a cryogenic plasma FIB/SEM (cryo-pFIB/SEM)".

Reading the article, I do not find that the challenges are addressed; it appears that some of these are evaluated when the samples are prepared using plasma-based beams. To support the fact that charging, contrast, and curtaining are addressed, a comparison should be made with the current state of the art, or it is otherwise impossible to determine whether these systems bring any advantage.

Charging is an issue that is not described in detail, nor has it been adequately analysed. The effect of using plasma beams is independent of the presented algorithm for charging suppression, which is purely image processing based, although very interesting. Given that the focus of the work is on introducing the benefit of using plasma ion beams (from the title) and given that a great deal of data is presented on the effect of the multiple ion sources, one would expect to have comparable images acquired after the surfaces have been prepared with the different beams. This should also be compared against the current state-of-the-art (gallium) to provide a baseline for different beams' benefits. I realise that this requires access to another microscope and that this also imposes controls on the detector responses on each instrument to have a normalised analysis. Still, it also provides the opportunity to quantify the benefits of each instrumentation.

We have provided a response to the charging comments outlined here in the main rebuttal above. The SEM we used in this study was selected based on its optimal performance at low electron voltages due to its immersion field. The low kV capability is particularly of interest in the case of charging (cross over energy). There is the possibility the interaction of the sample surface with chemically inert or reactive ion species could change the surface potential (either positively or negatively). The Vero cells imaged during a serial pFIB/SEM using nitrogen plasma still exhibit charging as well as the argon plasma we canonically used, suggesting that charging is ion beam independent.

Regarding Gallium, this would require prolonged access to another very bespoke microscope for a like-for-like comparison, and indeed there are studies (e.g. Schertel et al. 2013 and Scher et al, 2021) that show SEM data of cryogenic sample surfaces milled with gallium. Therefore, we consider such a study outside of the scope of this manuscript.

The curtaining scores. This is a good way to explain the problem, though a few aspects need to be validated. For example, curtains appear over time when milling, and it would be useful to understand how different sources behave over time in FIB/SEM tomography sessions. The score is currently done from individual windows milled, which gives a good indication of the performance. However, it would make sense to check that the behaviour remains identical in an imaging setting and with the moving milling windows (or lines). This will show the counteracting effect to the redeposition and etching effect reported when imaging with the E-beam the milled face.

Please see our response in the main rebuttal points.

No detail about the milling resolution has been reported. Since different currents and beams have different cross-sections, it is expected to affect the z-resolution achievable during an imaging session. It would be useful to have a description of the beam cross-sections at the various conditions used and how or whether these interfere with the preparation.

Please see our response in the main rebuttal points.

Contrast. No analysis of plasma FIBs' benefits on image contrast compared to the current state of the art has been provided. Measuring contrast is complex, especially when this value can change in response to the detector settings. Still, attempts can be made to quantify it through the FRC and through the analysis of the image MTF (amplitude and fall off), given that membranes are the only most prominent and visible features in cryoFIB/SEM images of biological samples.

We agree that measuring contrast is complex, and therefore the following parameters as stated on page 6, line 6 to 7 were kept consistent throughout data collection: voltage, current, line integration, exposure, detectors voltage offset and gain. We also decided to keep constant or vary the working distance (focus) in Figure 4 and compared the FRC as well as the contrast. As discussed above, a like-for-like comparison with the state of the art (gallium) is not currently possible, making this experiment/analysis outside the scope of this manuscript.

Figure S4 points out that electrons that hit the sample at normal incidence give better signal/contrast or imaging quality than when the sample is imaged at a tilt. This fact is expected to significantly affect large areas as the collection efficiency will vary across the sample, particularly as regions get further away from the optimal location. The dynamic focusing option available on all SEM will compensate for the focal change but not the collection efficiency. Even though this is a fact, the authors show a loss of resolution, which is not explained by the tilt itself. In particular, the generation of secondary electrons is known to increase with the increased tilt, and to consider that the curtains (that are the prominent feature on the surface) are running along the tilt direction, it would be expected to see no contrast difference between the background and the edge of each curtain as the generation of secondary electrons will increase with tilt for both the edges and the background. Therefore, the contrast should be invariant, at least on the curtains.

Looking at the images presented in the figure, they appear astigmatic and not properly focused when imaged at a tilt. As evidence of this claim, the cellular features do not measure the same, and the sharpness of the edge of the curtains is gone when tilted. This experience comes from improper astigmatism correction, which in turn, in scanning systems, leads to the impossibility of focusing. The tilt correction provides not only dynamic focusing but also corrects for the anisotropy in the sampling due to the tilt. If all imaging is set up correctly, the two images should show the imaged features with the exact sizes regardless of the resolution (which, in the presented case, is sufficient), and the sharpness of the curtain edges should be invariant regardless of the tilt, at least while or where in focus. Only at that point, the comparison will be fair.

Please see our response in the main rebuttal points.

Finally, the resolution measurements presented in the last supplementary figures have no impact or relation to the use of plasma FIB/SEM. It is an effect related to the imaging conditions used in the SEM regardless of the ion beam nature. The distribution of the resolution within images appears predominantly linked to local charging and the local sample composition (from fig8). Given the focus is aimed at introducing or presenting the use of the plasma-based beams the results should be presented in that optic in mind with a comparison between beams.

This figure is to present the absence of degradation in image quality over the dataset. As the stage is moving during the imaging at 90 it would be possible for the focus to be lost throughout a longer data acquisition session. However, this figure demonstrates that the focus is well adjusted throughout the data acquisition. We also considered potential beam damage accumulation which does not seem to be detectable with our method.

Reviewer #2 (Public Review):

The authors present a manuscript highlighting recent advancements in cryo-focused ion beam/scanning electron microscopy (cryo-FIB) using plasma ion sources as an alternative to positively-charged gallium sources for cryo-FIB milling and volumetric SEM (cryo-FIB/SEM) imaging. The authors benchmark several sources of plasma and determine argon gas is the most suitable source for reducing undesirable curtaining effects during milling. The authors demonstrate that milling with an argon source enables volumetric imaging of vitrified cells and tissue with sufficient contrast to gleam biological insight into the spatial localization of organelles and large macromolecular complexes in both vitrified human cells and in high-pressure frozen mouse brain tissue slices. The authors also show that altering the sample angle from 52 to 90 degrees relative to the SEM beam enhances the contrast and resolution of biological features imaged within the vitrified samples. Importantly, the authors also demonstrate that the resolution of SEM images after serial milling with argon and nitrogen plasma sources does not appear to significantly affect resolution, suggesting that resolution does not vary over an acquisition series. Finally, the authors test and apply a neural network-based approach for mitigating image artifacts caused by charging due to SEM imaging of biological features with high lipid content, such as lipid droplets in yeast, thereby increasing the clarity and interpretability of images of samples susceptible to charging.

Strengths and Weaknesses:

The authors do a fantastic job demonstrating the utility of plasma sources for increased contrast of biological features for cryo-FIB/SEM images. However, they do not specifically address the lingering question of whether or not it is possible to use this plasma source cryo-FIB/SEM volumetric imaging for the specific application of localizing features for downstream cryo-ET imaging and structural analyses. As a reader, I was left wondering whether this technique is ideally suited solely for volumetric imaging of cryogenic samples, or if it can be incorporated as a step in the cellular cryo-ET workflow for localization and perhaps structure determination. Another biorxiv paper (doi.org/10.1101/2022.08.01.502333) from the same group establishes a plasma cryo-FIB milling workflow to generate lamella of sufficient quality to elucidate sub-nanometer reconstructions of cellular ribosomes. However, I anticipate the real impact on the field will be from the synergistic benefits of combining both approaches of volumetric cryo-FIB/SEM imaging to localize regions of interest and cryo-ET imaging for high-resolution structural analyses.

Additional experiments were undertaken to demonstrate that serial cryo pFIB/SEM can be used in a variety of correlative imaging workflows, including follow-on cryoET. However, we have yet to carefully determine the consequences for downstream high spatial frequencies of such imaging modalities e.g., for sub volume averaging. The role of the SEM imaging, ion beam damage, etc has yet to be analysed or optimised in detail. This work is outside of the scope of this manuscript.

Another weakness is the lack of demonstration that the contrast gained from plasma cryo-FIB/SEM is sufficient to apply neural network-based approaches for automated segmentation of biological features. The ability to image vitrified samples with enhanced contrast is huge, but our interpretation of these reconstructions is still fundamentally limited in our ability to efficiently analyze subcellular architecture.

We have demonstrated that the segmentation of subcellular features such as mitochondria within a serial pFIB-SEM data set of heart tissue can be automated using SuRVos2 – a neural network based automated segmentation software. These comparisons are included in an additional figure (Figure 11).

Author Response

Reviewer #2 (Public Review):

Charme is a long non-coding RNA reported by the authors in their previous studies. Their previous work, mainly using skeletal muscles as a model, showed the functional relevance of Charme, and presented data demonstrating its nuclear role, primarily via modulating the sub-nuclear localization of Matrin 3 (MATR3). Their data from skeletal muscles suggested that loss of the intronic region of Charme affects the local 3D genome organization, affecting MATR3 occupancy and this gene expression. Loss of Charme in vivo leads to cardiac defects. In this manuscript, they characterize the cardiac developmental defects and present molecular data supporting how the loss of Charme affects the cardiac transcriptome repertoire. Specifically, by performing whole transcriptome analysis in E12.5 hearts, they identify gene expression changes affected in developing hearts due to loss of Charme. Based on their previous study in skeletal muscles, they assume that Charme regulates cardiac gene expression primarily via MATR3 also in developing cardiomyocytes. They provide CLIP-seq data for MATR3 (transcriptome-wide foot printing of MATR3) in wild-type E15.5 hearts and connect the binding of MATR3 to gene expression changes observed in Charme knockout hearts. I credit the authors for providing CLIP seq data from in vivo embryonic samples, which is technically demanding.

Major strengths:

Although, as previously indicated by the authors in Charme knockout mice, the major strength is the effect of Charme on cardiac development. While the phenotype might be subtle, the functional data indicate that the role of Charme is essential for cardiac development and function. The combinatorial analysis of MATR3 CLIP-seq and transcriptional changes in the absence of Charme suggests a role of Charme that could be dependent on MATR3.

We thank this reviewer for appreciating our methodological efforts and the importance of the MATR3 CLIP-seq data from in vivo embryonic samples.

Weakness:

(i) Nuclear lncRNAs often affect local gene expression by influencing the local chromatin.

Charme locus is in close proximity to MYBPC2, which is essential for cardiac function, sarcomerogenesis, and sarcomere maintenance. It is important to rule out that the cardiac-specific developmental defects due to Charme loss are not due to (a) the influence of Charme on MYBPC2 or, of that matter, other neighboring genes, (b) local chromatin changes or enhancer-promoter contacts of MYBPC2 and other immediate neighbors (both aspects in the developmental time window when Charme expression is prominent in the heart, ideally from E11 to E15.5)

Although the cis-activity represents a mechanism-of-action for several lncRNAs, our previous work does not reveal this kind of activity for pCharme. To add stronger evidence, we have now analysed the expression of pCharme neighbouring genes in cardiac muscle. Genes were selected by narrowing the analysis not only on the genes in “linear” proximity but also on eventual chromatin contacts, which may underlie possible candidates for in cis regulation. To this purpose, we made use of the analyses that in the meantime were in progress (to answer point iv) on available Hi-C datasets (Rosa- Garrido et al. 2017). Starting from a 1 Mb region around Charme locus, we found that most of the interactions with Charme occur in a region spanning from 240 kb upstream and 115 kb downstream of Charme for a total of 370 Kb (Rev#2_Capture Fig. 1A). This region includes 39 genes, 9 of them expressed in the neonatal heart but none showing significant deregulation (see Table S2). To note, this genomic region also included the MYBPC2 locus, for which we did not find a decreased expression in the heart from our RNA-seq data (Revised Figure 2-figure supplement 1C and Table S2). This trend was confirmed through RT-qPCR analyses of several genes from E15.5 extracts, which revealed no significant difference in their abundance upon Charme ablation (Rev#2_Capture fig. 1B).

Fig. 1. A) Contact map depicting Hi-C data of left ventricular mice heart retrived from GEO accession ID GSM2544836. Data related to 1 Mb region around Charme locus were visualized using Juicebox Web App (https://aidenlab.org/juicebox/). B) RT-qPCR quantification of Charme and its neighbouring genes in CharmeWT vs CharmeKO E15.5.5 hearts. Data were normalized to GAPDH mRNA and represent means ± SEM of WT and KO (n=3) pools. Data information: p < 0.05; p < 0.01, **p < 0.001 unpaired Student’s t test.

For a better understanding, we also checked possible “local” Charme activities in skeletal muscle cells, from previous datasets (Ballarino et al., 2018). We found that in murine C2C12 cells treated with two different gapmers against Charme, three of its neighbouring genes were expressed (Josd2, Emc10 and Pold1), but none showed significant alterations in their expression levels in response to Charme knock-down (Rev#2_Capture Fig. 2).

Taken together, these results would exclude the possibility of Charme in cis activity as responsible for the phenotype.

Fig. 2: Average expression from RNA-seq (FPKM) quantification of Charme neighbouring genes in C2C12 differentiated myotubes treated with Gap-scr vs Gap-Charme. Values for Gap-Charme represent the average values of gene expression after treatment with two different gapmers (GAP-2 and GAP-2/3).

(ii) The authors provide data indicating cardiac developmental defects in Charme knockouts. Detailed developmental phenotyping is missing, which is necessary to pinpoint the exact developmental milestones affected by Charme. This is critical when reporting the cell type/ organ-specific developmental function of a newly identified regulator.

We did our best to answer this concern.

Let us first emphasise that, since their generation, we have never observed any particular tissue alteration, morphological or physiological, when dissecting the CharmeKO animals other than the muscular ones. The high specificity of pCharme expression, as also shown here by ISH (Figure 1C-D, Figure 1-figure supplement 1A-B, Figure 3A), together with the minimal alteration applied to the locus for CRISPR-Cas-mediated KO (PolyA insertion), strongly excludes the presence of an alteration in other tissues and their involvement in the development of the phenotype.

Nevertheless, we now add more developmental details to the cardiac phenotype (see also Essential revision point 2).

1- First of all, gene expression analyses performed at 12.5E, 15.5E, 18.5E and neonatal (PN2) stages allowed us to identify, at the molecular level, the developmental time point when CharmeKO effects on the cardiac muscle can be found. Our new results clearly indicate that the pCharme-mediated regulation of morphogenic and cardiac differentiation genes is detectable from E15.5 fetal stage onward (Rev#2_Capture Fig. 3/Revised Figure 2E). Together with the analysis of pCharme targets and coherently with the altered cardiac maturation and performance, this evidence is also supported by the analysis of the myosins Myh6/Myh7 ratio, which diminution in CharmeKO hearts starts from E15.5 up to 69% of control levels at PN stages (Revised Figure 2F).

2- Hematoxylin-eosin staining of dorso-ventral cryosections from CharmeWT and CharmeKO hearts confirmed the fetal malformation at the E15.5 stage (Revised Figure 2G). Moreover, the hypotrabeculation phenotype of CharmeKO hearts, which was initially examined by immunofluorescence, now finds confirmation by the analysis of key trabecular markers (Irx3 and Sema3a), which expression significantly decreases upon pCharme ablation (Rev#1_Capture Fig. 3B/Revised Figure 2-figure supplement 1G).

3- Finally, the gene expression analysis on Ki-67, Birc5 and Ccna2 (Revised Figure 2-figure supplement 1E) definitively rules out the influence of pCharme ablation on cell-cycle genes and cardiomyocytes proliferation, thus allowing a more careful interpretation of the embryonic phenotype. Note that, coherently with the lncRNA implication at later stages of development, the expression of important cardiac regulators, such as Gata4, Nkx2-5 and Tbx5, is not altered by its ablation at any of the tested time points (Rev#2_Capture Fig.3), while pCharme absence mainly affects genes which are expressed downstream of these factors.

These new results have been included in the revised version of the manuscript and better discussed.

Fig. 3: RT-qPCR quantification Gata4, Nkx2-5 and Tbx5 in CharmeWT and CharmeKO cardiac extract at E12.5, E15.5 and E18.5 days of embryonal development. Data were normalized to GAPDH mRNA and represent means ± SEM of WT and KO (n=3) pools.

(iii) Along the same line, at the molecular level, the authors provide evidence indicating a change in the expression of genes involved in cardiogenesis and cardiac function. Based on changes in mRNA levels of the genes affected due to loss of Charme and based on immunofluorescence analysis of a handful of markers, they propose a role of Charme in cell cycle and maturation. Such claims could be toned down or warrant detailed experimental validation.

See above, response to Reviewer #2 (Public Review) weakness (ii).

(iv) Authors extrapolate the mechanistic finding in skeletal muscle they reported for Charme to the developing heart. While the data support this hypothesis, it falls short in extending the mechanistic understanding of Charme beyond the papers previously published by the authors. CLIP-seq data is a step in the right direction. MATR3 is a relatively abundant RBP, binding transcriptome-wide, mainly in the intronic region, based on currently available CLIP-seq data, as well as shown by the authors' own CLIP seq in cardiomyocytes. It is also shown to regulate pre-mRNA splicing/ alternative splicing along with PTB (PMID: 25599992) and 3D genome organization (PMID: 34716321). In addition, the authors propose a MATR3 depending molecular function for Charme primarily dependent on the intronic region of Charme and due to the binding of MATR3. Answering the following question would enable a better mechanistic understanding of how Charme controls cardiac development.

(i) what are the proximal genomic regions in the 3D space to Charme locus in embryonic cardiomyocytes? Authors can re-analysis published Hi-C data sets from embryonic cardiomyocytes or perform a 4-C experiment using Charme locus for this purpose.

See above, response to Reviewer #2 (Public Review) weakness (i).

(ii) does the loss of Charme affect the splicing landscape of MATR3 bound pre-mRNAs in E12.5 ventricles in general and those arising from the NCTC region specifically?

This is an intriguing issue, as also highlighted by new evidence showing that the reactivation of fetal-specific RNA-binding proteins, including MATR3, in the injured heart drives transcriptome-wide switches through the regulation of early steps of RNA transcription and processing (D'Antonio et al., 2022).

Using the rMATS software on our neonatal RNA-Seq datasets we then investigated the effect of pCharme depletion on splicing, with a focus on NCTC. As shown in the Rev#2_Capture Fig.4A, all classical splicing alterations were investigated, such as exon-skipping, alternative 5’ splice site, alternative 3’ splice site, mutually excluded exons and intron retention. Intriguingly, we did observe a slight alteration in the splicing patterns, in particular considering exon skipping events (62% corresponding to 381 genes). Among them, the majority corresponded to exon exclusion events (237 events = 209 genes) while a smaller fraction to exon inclusion (144 events = 133 genes). Moreover, by intersecting these genes with the MATR3-bound RNAs we found a slightly significant enrichment (p=0,038) for exon inclusion (Rev#2_Capture Fig.4B).

Regarding the NCTC locus, we demonstrate that in hearts pCharme acts through different target genes. Indeed, none of the NCTC-arising transcripts are bound by MATR3 (see Table S4) or substrate for alternative splicing regulation.

While these results are very interesting for deepening the investigation of pCharme/MATR3 interplay, their biological significance needs to be further investigated through one-by-one analysis of specific transcripts. As a prosecution of the project, Nanopore sequencing of these samples on a MinION platform is currently undergoing in the lab to obtain a better characterization of alternative splicing events in response to the lncRNA ablation during development.

Fig. 4: A) Left and middle panel: Pie Chart depicting the proportion of significantly altered (FDR < 0.05) splicing events detected by rMATS comparing neonatal CharmeWT and CharmeKO RNA-seq samples. All classical splicing alterations were investigated, such as exon-skipping, alternative 3’ splice site (A3SS), intron retention, alternative 5’ splice site (A5SS) and mutually excluded exons (MXE). Right panel. Volcano plot depicting significant exon skipping events in CharmeKO (FDR < 0.05, PSI<0 for excluded and included exons, FDR >= 0.05 for invariant exons). X-axis represent exon-inclusion ratio or Percentage Spliced In (PSI) while y-axis represent –log10 of p-value. B) Pie charts representing the fraction of transcripts with at least one significant excluded (left panel), invariant (middle panel) and included (right panel) exons that are bound by MATR3. P-values of MATR3 targets enrichment for each comparison is depicted below. Statistical significance was assessed with Fisher exact test.

(iii) MATR3 binds DNA, as also shown by authors in previous studies. Is the MATR3 genomic binding altered by Charme loss in cardiomyocytes globally, as well as on the loci differentially expressed in Charme knockout heart? Overlapping MATR3 genomic binding changes and transcriptome binding changes to differentially expressed genes in the absence of Charme would better clarify the MATR3-centric mechanisms proposed here. Further connecting that to 3D genome changes due to Charme loss could provide needed clarity to the mechanistic model proposed here.

Previous experience from our (Desideri et al., 2020) and other labs (Zeitz et al 2009 J Cell Biochem), indicate that Chromatin IP is not the most suitable approach for identifying MATR3 specific targets because of the broad distribution of MATR3 over the genome. Given the number of animals that would need to be sacrificed, we moved further to strengthen our MATR3 CLIP evidence by adding the i) CharmeKO MATR3 CLIP-seq control and the ii) combinatorial analysis of MATR3 CLIP-seq with the RNA-seq data.

We have better explained the reasoning within the text, which now reads “The known ability of MATR3 to interact with both DNA and RNA and the high retention of pCharme on the chromatin may predict the presence of chromatin and/or specific transcripts within these MATR3-enriched condensates. In skeletal muscle cells, we have previously observed on a genome-wide scale, a global reduction of MATR3 chromatin binding in the absence of pCharme (Desideri et al., 2020). Nevertheless, the broad distribution of the protein over the genome made the identification of specific targets through MATR3-ChIP challenging.” (lines 274-279).

Indeed, we found that MATR3 binding was significantly decreased on numerous peaks (434/626), while its increase was observed on a smaller fraction of regions (192/626) (Revised Figure 5C). As a control, we performed MATR3 motif enrichment analysis on the differentially bound regions revealing its proximity to the peak summit (+/- 50 nt) (Revised Figure 5-figure supplement 1D) close to the strongest enrichment of MATR3, further confirming a direct and highly specific binding of the protein to these sites. To better characterise the relationship between MATR3 and pCharme, we then intersected the newly identified regions with the MATR3-bound transcripts whose expression was altered by Charme depletion. While gain peaks were equally distributed across DEGs, loss peaks were significantly enriched in a subset of pCharme down-regulated DEGs (Revised Figure 5D), suggesting a crosstalk between the lncRNA and the protein in regulating the expression of this specific group of genes. Interestingly, these RNAs mainly distribute across the same GO categories as pCharme downregulated DEGs and include genes, such as Cacna1c, Notch3, Myo18B and Rbm20 involved in embryo development and validated as pCharme/Matr3 targets in primary cardiac cells (Revised Figure 5D, lower panel and 5E)

Author Response

Reviewer #2 (Public Review):

1) My main reservation is the presentation of the work. The writing style is conversational and expansive, which makes it challenging for the reader. Furthermore, long paragraphs shift from one topic to the next rather than using separate paragraphs with strong topic sentences to cover each topic. I suggested a few places to start new paragraphs, but many more paragraphs could be divided.

We have also made significant efforts to reduce the text of the manuscript in each section, with more compact phrasing (including the headlines for the different results sections), and more short paragraphs to make the paper more readable. This has resulted in an overall reduction in the total number of words in the manuscript from ~11.000 to 9.000 (including Abstract, Introduction, Results, Discussion, Materials and Methods, and Figure legends sections), equivalent to approximately four pages of typed text.

2) Most of the figures are also overly complicated. I did not attempt to edit one of them, but I am sure that findings will be much clearer with about half of the panels moved to supplemental materials, so the reader can concentrate on the most important data.

As recommended by the reviewer, we have significantly reduced the number of panels within the figures in the revised manuscript. Accordingly, the total number of panels in the modified figures compared to the original version is as follows: Figure 1 (7 vs 8); Figure 2 (8 vs 10); Figure 3 (7 vs 10); Figure 4 (7 vs 12); Figure 5 (6 vs 11); Figure 6 (4 vs 8).

The remaining panels, including quantitative data such as cable-to-patch ratios, or percentages of septated/multiseptated cells, among others, have been moved to existing and new supplementary figures. The total number of supplementary figures is now 9 versus 6 in the original version.

Author Response

Reviewer #1 (Public Review):

This study combines the biologging method with captive experiments and DNA metabarcoding to detail the hunting behavior of a bat species in the wild. Specifically, it shows that bats use two foraging strategies (echolocating small prey in the air and capturing large ground prey with passive listening) with different success rates and energetic gains. This result highlights that a species believed to be a specialist forager can, in fact, have mixed strategies depending on the condition and environment.

The detailed foraging behavior they show for such a small animal is impressive. A combination of several different methods, including captive experiments, is a major strength of the paper. I especially like the mastication sound analysis, although I don't know how new it is. However, I have a major concern about the presentation of this study. The manuscript is apparently written for a bat community, and it's hard to understand the significance of the results in the field of animal ecology.

Thank you for your helpful feedback. We agree that the framing of the ms was too narrow for the audience of eLife, and we have framed the introduction for a broader audience of animal ecology.

Reviewer #2 (Public Review):

This paper has huge potential for influencing the way we think about bats as foragers. But, I think that it can be improved.

Specifically, there is no clearly articulated hypothesis underlying the work. Second, there should be specific testable predictions arising from the hypothesis. This change, while relatively minor, will vastly improve the focus of the work, and hence its impact on the reader.

Thank you highlighting the need for clear hypotheses. We have added three specific hypotheses to guide the reader (line: 54-56) in the introduction. We have also reformatted the discussion section to address each hypothesis in succession using subheadings with clear take home messages (line: 223-224, 271-272, 293, 318)

Reviewer #3 (Public Review):

The study addresses a tough question in the study of wild bats: what and where they eat, using both acoustic bio-logging and DNA metabarcoding. As a result, it was found that greater mouse-eared bats made more frequent attack attempts against passively gleaning prey with lower predation success but higher prey profitability than aerial hawking with higher predation success. This is a precious study that reveals essential new insights into the foraging strategies of wild bats, whose foraging behavior has been challenging to measure. On the other hand, the detection of capture attempts, success or failure of predation, and whether it was by passively gleaning prey or aerial hawking were determined from the audio and triaxial accelerometer analysis, and all results of this study depend entirely on the veracity of this analysis. Also, although two different weights and a tag nearly 15% of its weight were used, it is essential for the results of this data that there be no effect on foraging behavior due to tag attachment. Since this is an excellent study design using state-of-the-art methods and very valuable results, readers should carefully consider the supplemental data as well.

Thank you for the kind words. We agree that it is critically important that the two foraging strategies are un-affected by tagging effects. In the revised ms, we have added tag weights, tag types and change in body weight during instrumentation as explanatory factors in out statistical models and found no effect of the tag weight on our results. We have also addressed this important issue in the method section (model 1: line 520-539, model 3: 568-590).

Author Response

Reviewer #1 (Public Review):

Zeng and colleagues investigated the neural underpinnings of visual-vestibular recalibration. Specifically, they measured changes in three monkeys' perception of unisensory heading cues as well as associated changes in neuronal responses to these cues in three different cortical areas following prolonged exposure to systematic visual-vestibular discrepancies. Behavioral responses in a motion direction discrimination task indicate unisensory perceptual shifts in opposite directions that account for the cross-modal discrepancy the monkeys were exposed to. Neuronal firing patterns, related to motion discrimination judgments by means of neurometric functions indicated analogous shifts in neuronal tuning in areas MSTd and PIVC. In contrast, in area VIP tuning for visual heading stimuli shifted in the same direction as tuning for vestibular stimuli and thus in contradiction to the observed perceptual shifts.

The shifts observed in MSTd and PIVC fit nicely with existing theories and results regarding cross-modal recalibration and substitute claims that activity in these areas might underlie perceptual decisions. The shift of visual tuning in VIP is surprising and will certainly spark further investigation.

Overall the results are really interesting, yet, the manuscript in its current form needs revisions along two dimensions, 1) data analysis and 2) writing.

We thank the reviewer for the positive comments and thoughtful suggestions, which have greatly helped us improve the data analysis and writing. Also, thank you for the thorough list of specific suggestions for improved writing and phrasing. This considerably helped us clarify these aspects in our manuscript.

Reviewer #2 (Public Review):

The manuscript by Zeng and colleagues aims to investigate how neural representations of sensory cues in two modalities (visual and vestibular) change when conflicts are introduced between the cues. The manuscript convincingly demonstrates that this recalibration process differs between areas MSTd (a multisensory region), where sensory responses recalibrated differently for visual and vestibular cues, following each modality's conflict, and area VIP ( a higher-level region), where responses follow the vestibular cue. More limited insights are present for area PIVC, where visual responses are limited.

The analyses generally support the conclusions of the authors, but I have two major suggestions to strengthen the statistical robustness of the manuscript:

1) The analysis about the lack of visual recalibration in area PIVC would have been more convincing if the authors had used Bayesian statistics instead of regular t tests. In this way it would have been possible to estimate if the lack of visual recalibration in this area, for those few neurons that show visual tuning, can be taken as evidence for the absence of an effect or not. In the absence of this additional analysis, it is in fact difficult to properly interpret the results about area PIVC. Is PIVC more in line with MSTd, in view of the lack of visual responses? Or is there actually no visual recalibration, in contrast to both MSTd and VIP?

In response to this comment, we calculated the Bayesian Pearson correlation for visual recalibration in area PIVC, with the alternative hypothesis (H1) of a correlation between neuronal shifts and perceptual shifts and the null hypothesis (H0) of no correlation: Pearson's r = 0.26, and BF10 = 0.49. Thus, the evidence neither supports H1 nor H0. The lack of support for or against visual recalibration in PIVC primarily reflects the lack of robust tuning to visual heading stimuli in PIVC. Accordingly, in the manuscript, we do not argue for or against the recalibration of visual heading tuning in PIVC. Rather, we highlight that neurons in PIVC respond strongly to vestibular signals, but not so to visual heading stimuli and that the vestibular responses undergo recalibration. We agree that the lack of evidence for (or against) visual recalibration in PIVC primarily reflects the lack of robust tuning to visual heading stimuli. We interpret the observed shifts in vestibular tuning in PIVC as lower-level, sensory, recalibration (similar to MSTd) based on the broader understanding that PIVC encodes lower-level vestibular signals, with transient time-courses, and impoverished visual tuning (Chen et al., 2016; Chen et al., 2021). Our results are in line with this interpretation, and there is no reason to suspect that PIVC reflects more complex multisensory recalibration (like VIP). Nonetheless, the data could also be in line with alternative interpretations. Therefore, in the revised manuscript we now more explicitly explain this argument and have added limitations thereof, and alternative interpretations to the Discussion (in subsection “Limitations and future directions”, paragraph 2).

2) For all statistical analyses, multi-level statistics would have been more appropriate than simple t-tests. In fact, since recordings come from few subjects, which in turn have relatively few recording sessions, there is a risk that the results are influenced by one subject and do not represent the full population. Admittedly, this is unlikely in view of the apparently large effect size and low p values. Nonetheless, a more appropriate statistical analysis would make the results more robust and convincing.

Thank you. We agree with this suggestion and have now: 1) added summary statistics for the individual monkeys, and 2) performed linear mixed model (LMM) analyses (please see our response to Essential Revisions Comment #1, for further details).

Once these issues are addressed, I believe that the manuscript would provide relevant evidence supporting the hypothesis that multisensory processing in the cortex is an area-specific phenomenon, and that effects observed in one area cannot be simply expected to operate elsewhere. This will therefore elucidate the mechanisms of multimodal plasticity.

Reviewer #3 (Public Review):

This study documents an empirical investigation of a fundamental brain process: adaptation to systematic cross-sensory discrepancies. The question is important, the experiment is carefully designed, and the results are striking. Following an unsupervised recalibration block, perceptual judgments of self-motion on the basis of visual and vestibular cues are systematically altered. These behavioral effects are mirrored by changes in the response properties of single neurons in areas MSTd and PIVC (provided that neurons in these areas exhibited selectivity for the sensory cue). Remarkably, neurons in downstream area VIP adjust their response properties in a very different manner, seemingly exclusively reflecting vestibular recalibration (which is opposite in direction to visual perceptual shifts). In the former two areas, the neural-behavior association follows the stimulus dynamics. In VIP, this association remains high beyond the life span of the stimulus. VIP typically exhibits strong choice signals. These decreased in strength after recalibration (an effect unique to area VIP). Together, these findings further dissociate VIP's functional role from that of MSTd and PIVC, without however, fully revealing what that role may be. These results offer a novel perspective on the neural basis of cross-sensory recalibration and will inspire future modeling studies of the neural basis of perception of self-motion.

We thank the reviewer for the supportive comments.

Author Response

Reviewer #1 (Public Review):

In this manuscript, Wei & Robles et al seek to estimate the heritability contribution of Neanderthal Informative Markers (NIM) relative to SNPs that arose in modern humans (MH). This is a question that has received a fair amount of attention in recent studies, but persistent statistical limitations have made some prior results difficult to interpret. Of particular concern is the possibility that heritability (h^2) attributed to Neanderthal markers might be tagging linked variants that arose in modern humans, resulting in overestimation of h^2 due to Neanderthal variants. Neanderthal variants also tend to be rare, and estimating the contribution of rare alleles to h^2 is challenging. In some previous studies, rare alleles have been excluded from h^2 estimates.

Wei & Robles et al develop and assess a method that estimates both total heritability and per-SNP heritability of NIMs, allowing them to test whether NIM contributions to variation in human traits are similar or substantially different than modern human SNPs. They find an overall depletion of heritability across the traits that they studied, and found no traits with enrichment of heritability due to NIMs. They also developed a 'fine-mapping' procedure that aims to find potential causal alleles and report several potentially interesting associations with putatively functional variants.

Strengths of this study include rigorous assessment of the statistical methods employed with simulations and careful design of the statistical approaches to overcome previous limitations due to LD and frequency differences between MH and NIM variants. I found the manuscript interesting and I think it makes a solid contribution to the literature that addresses limitations of some earlier studies.

My main questions for the authors concern potential limitations of their simulation approach. In particular, they describe varying genetic architectures corresponding to the enrichment of effects among rare alleles or common alleles. I agree with the authors that it is important to assess the impact of (unknown) architecture on the inference, but the models employed here are ad hoc and unlikely to correspond to any mechanistic evolutionary model. It is unclear to me whether the contributions of rare and common alleles (and how these correspond with levels of LD) in real data will be close enough to these simulated schemes to ensure good performance of the inference.

In particular, the common allele model employed makes 90% of effect variants have frequencies above 5% -- I am not aware of any evolutionary model that would result in this outcome, which would suggest that more recent mutations are depleted for effects on traits (of course, it is true that common alleles explain much more h^2 under neutral models than rare alleles, but this is driven largely by the effect of frequency on h^2, not the proportion of alleles that are effect alleles). Likewise, the rare allele model has the opposite pattern, with 90% of effect alleles having frequencies under 5%. Since most alleles have frequencies under 5% anyway (~58% of MH SNPs and ~73% of NIM SNPs) this only modestly boosts the prevalence of low frequency effect alleles relative to their proportion. Some selection models suggest that rare alleles should have much bigger effects and a substantially higher likelihood of being effect alleles than common alleles. I'm not sure this situation is well-captured by the simulations performed. With LD and MAF annotations being applied in relatively wide quintile bins, do the authors think their inference procedure will do a good job of capturing such rare allele effects? This seems particularly important to me in the context of this paper, since the claim is that Neanderthal alleles are depleted for overall h^2, but Neanderthal alleles are also disproportionately rare, meaning they could suffer a bigger penalty. This concern could be easily addressed by including some simulations with additional architectures to those considered in the manuscript.

We thank the reviewers for their thoughtful comments regarding rare alleles, and we agree that our RARE simulations only moderately boosted the enrichment of rare alleles in causal mutations. To address this, we added new simulations, ULTRA RARE, in which SNPs with MAF < 0.01 constitute 90% of the causal variants. Similar to our previous simulations, we use 100,000 and 10,000 causal variants to mimic highly polygenic and moderately polygenic phenotypes, and 0.5 and 0.2 for high and moderately heritable phenotypes. We similarly did three replicated simulations for each combination and partitioned the heritability with Ancestry only annotation, Ancestry+MAF annotation, Ancestry+LD annotation, and Ancestry+MAF+LD annotation. Our Ancestry+MAF+LD annotation remains calibrated in this setting (see Figure below). We believe this experiment strengthens our paper and have added it as Fig S2.

While we agree that these architectures are ad-hoc and are unlikely to correspond to realistic evolutionary scenarios, we have chosen these architectures to span the range of possible architecture so that the skew towards common or rare alleles that we have explored are extreme. The finding that our estimates are calibrated across the range that we have explored leads us to conclude that our inferences should be robust.

More broadly, we concur with the reviewer that our results (as well as others in the field) may need to be revisited as our view of the genetic architecture of complex traits evolves. The methods that we propose in this paper are general enough to explore such architectures in the future by choosing a sufficiently large set of annotations that match the characteristics across NIMs and MH SNPs. A practical limitation to this strategy is that the use of a large number of annotations can result in some annotations being assigned a small number of SNPs which would, in turn, reduce the precision of our estimates. This limitation is particularly relevant due to the smaller number of NIMs compared to MH SNPs (around 250K vs around 8M).

Reviewer #2 (Public Review):

The goal of the work described in this paper is to comprehensively describe the contribution of Neanderthal-informative mutations (NIMs) to complex traits in modern human populations. There are some known challenges in studying these variants, namely that they are often uncommon, and have unusually long haplotype structures. To overcome these, the authors customized a genotyping array to specifically assay putative Neanderthal haplotypes, and used a recent method of estimating heritability that can explicitly account for differences in MAF and LD.

This study is well thought-out, and the ability to specifically target the genotyping array to the variants in question and then use that information to properly control for population structure is a massive benefit. The methodology also allowed them to include rarer alleles that were generally excluded from previous studies. The simulations are thorough and convincingly show the importance of accounting for both MAF and LD in addition to ancestry. The fine-mapping done to disentangle effects between actual Neanderthal variants and Modern human ones on the same haplotype also seems reasonable. They also strike a good balance between highlighting potentially interesting examples of Neanderthal variants having an effect on phenotype without overinterpreting association-based findings.

The main weakness of the paper is in its description of the work, not the work itself. The paper currently places a lot of emphasis on comparing these results to prior studies, particularly on its disagreement with McArthur, et al. (2021), a study on introgressed variant heritability that was also done primarily in UK Biobank. While they do show that the method used in that study (LDSR) does not account for MAF and LD as effectively as this analysis, this work does not support the conclusion that this is a major problem with previous heritability studies. McArthur et al. in fact largely replicate these results that Neanderthal variants (and more generally regions with Neanderthal variants) are depleted of heritability, and agree with the interpretation that this is likely due to selection against Neanderthal alleles. I actually find this a reassuring point, given the differences between the variant sets and methods used by the two studies, but it isn't mentioned in the text. Where the two studies differ is in specifics, mainly which loci have some association with human phenotypes; McArthur et al. also identified a couple groups of traits that were exceptions to the general rule of depleted heritability. While this work shows that not accounting for MAF and LD can lead to underestimating NIM heritability, I don't follow the logic behind the claim that this could lead to a false positive in heritability enrichment (a false negative would be more likely, surely?). There are also more differences between this and previous heritability studies than just the method used to estimate heritability, and the comparisons done here do not sufficiently account for these. A more detailed discussion to reconcile how, despite its weaknesses, LDSR picks up similar broad patterns while disagreeing in specifics is merited.

We agree with the reviewer that our results are generally concordant with those of McArthur et al. 2021 and this concordance is reassuring given the differences across our studies. The differences across the studies, wherein McArthur et al. 2021 identify a few traits with elevated heritability while we do not, could arise due to reasons beyond the methodological differences such as differences in the sets of variants analyzed. We have partially explored this possibility in the revised manuscript by analyzing the set of introgressed variants identified by the Sprime method (which was used in McArthur et al. 2021) using our method: we continue to observe a pattern of depletion with no evidence for enrichment. We hypothesize that the reason why LDSR picks up similar overall patterns despite its limitations is indicative of the nature of selection on introgressed alleles (which, in turn, influences the dependence of effect size on allele frequency and LD). Investigating this hypothesis will require a detailed understanding of the LDSR results on parameters such as the MAF threshold on the regression SNPs and the LD reference SNPs and the choice of the LD reference panel.

Not accounting for MAF and LD can underestimate NIM heritability but can both underestimate and overestimate heritability at MH SNPs. Hence, tests that compare per-SNP heritability at NIMs to MH SNPs can therefore lead to false positives both in the direction of enrichment and depletion.

We have now written in the Discussion: “In spite of these differences in methods and NIMs analyzed, our observation of an overall pattern of depletion in the heritability of introgressed alleles is consistent with the findings of McArthur et al. The robustness of this pattern might provide insights into the nature of selection against introgressed alleles”

In general this work agrees with the growing consensus in the field that introgressed Neanderthal variants were selected against, such that those that still remain in human populations do not generally have large effects on phenotypes. There are exceptions to this, but for the most part observed phenotypic associations depend on the exact set of variants being considered, and, like those highlighted in this study, still lack more concrete validation. While this paper does not make a significant advance in this general understanding of introgressed regions in modern populations, it does increase our knowledge in how best to study them, and makes a good attempt at addressing issues that are often just mentioned as caveats in other studies. It includes a nice quantification of how important these variables are in interpreting heritability estimates, and will be useful for heritability studies going forward.

Author Responses

Reviewer #1 (Public Review):

The authors present a very detailed short report on a previously undocumented behaviour where flying squirrels are believed to have created grooves in various species of nuts to aid their secure storage in the crotch or forks of twigs. The behaviour is suggested to have evolved as an adaptive strategy in this population of flying squirrels because of the challenges for nut caching in a rainforest environment.

Thanks

Using detailed photographs, GPS locations, measurements and camera trap videos, the authors describe the behaviour in great depth providing a useful base for comparative and future studies. However, the weakest point of this study is that the authors did not detect any squirrels making the grooves and only monitored nuts once they were cached. Therefore more research needs to be done to ascertain who, how and where the grooves are produced in the first place.

Three new videos are attached to show that two squirrel species are rotate and carving the nuts to create the grooves. By the new videos, we can also observe that squirrels re-fixed the nuts between the twigs by carving the nuts. These direct observations can support the claim better. See Supplementary Media files 6-8.

This work will be of great interest to scholars of animal behaviour and cognition and draws attention to a novel behaviour that warrants further study in similar species.

Yes, it is. Thanks

Reviewer #2 (Public Review):

The authors describe observations of an innovative food caching behavior attributed to two species of flying squirrels and likened the behavior to architectural joints used by humans. The discovery of nuts stored in the crook of shrub branches, facilitated by indented rings seemingly carved by squirrels, possibly represents an interesting food handling innovation that may function to prevent spoilage in a damp tropical ecosystem.

Thanks!

I applaud the efforts to survey the area multiple times after the initial discovery, and the use of trail cameras to try capture evidence of animal associations. For what is in essence a natural history note, the authors did a great job of trying to gather a variety of supporting evidence. The videos capturing squirrels visiting and retrieving the cached nuts were compelling, and the shaking of the shrubs demonstrating the difficulty in dislodging the nuts helps build the case that the nuts are cached effectively.

Thanks!

The most glaring gap in the evidence is that there is no direct observation of the squirrels actually performing this nut carving behavior, only associating with the nuts after they have been cached.There must be more documentation provided to explicitly link the causality between squirrels and this caching innovation.

We have included three additional videos to demonstrate that squirrels of both species rotate and carve the nuts to create the grooves. These new videos also show that squirrels can fit the nuts between twigs by carving the nuts. We think that these direct observations clearly support our claim, but agree that it was oversight not to included them in the first draft. See Supplementary Media files 6-8.

The second major weakness is more to do with writing style and could be addressed with significant revisions to phrasing and development of ideas. This is namely to do with the claim that this is somehow an evolved behavior, without providing evidence that 1) it is indeed the squirrels performing this behavior, 2) that is confers some kind of fitness benefit, and 3) hard evidence that this caching method does indeed prevent decomposition/germination in comparison to the more traditional caching methods of these species. Given the limited geographic range of the observations, I wonder how much of this is actually attributable to learning and/or innovation by these individuals. These ideas are not developed fully, and sometimes the writing wanders among learning and evolution without exploring the deep links among the two concepts.

1) As above, three new videos establish that the squirrels do, in fact, carve the nuts. See Supplementary Media files 6-8.

2) We added more description to suggest how this behavior likely confers fitness benefit in the discussion. At this point, however, it is correct to say that we have no hard evidence to demonstrate this, and thus, we’ve attempted to ‘tighten up’ the discussion accordingly so that our arguments (and its limitations) are more understandable.

3) We revised the statistics about the proportion of nuts that were fresh during each of the surveys, and added some references about how long is required for the nuts to germinate in natural conditions. L163-172.

Third, the connection to architecture is attention-grabbing, but I'd like to see this fleshed out a bit more with more text description (and a visual here would help immensely).

We added more description about how the grooving, caching and checking processes were performed by squirrels and how the principles of this suspension are similar to the mortise-tenon joint as employed by humans. L186-202. As above, three new videos are attached.

Ultimately this work stands to potentially contribute a fascinating piece of evidence into the growing literature on animal cognition, spatial awareness, caching behavior, innovation, and adaptation, but currently, the claims are unsupported by the evidence presented.

Thank you for your comments about the potential importance of our work on this interesting system. In this version we try to focus more tightly on the aspects for which we have new information to interpret.

Reviewer #3 (Public Review):

The authors were trying to describe and document the grooving behaviour of nuts in two species of flying squirrels (Hylopetes Phayrei electilis and H. alboniger) as well as related such behaviour to tool use or that the squirrels are smart. To achieve these objectives, the authors conducted three field surveys. They also set out a camera later to capture animal species that interacted with these nuts. They found that these nuts with grooves are fixed between twigs and can be found in different small plant species. Both species of squirrels made grooves a nut. More shallow grooves are found in nuts that are fixed on alive than dead trees. Ellipsoid nuts have deeper grooves than oblate nuts. They concluded that these nut grooving behaviours are evolved or learned in those flying squirrel populations, and related these behaviours to tool use as well as that the squirrels are smart.

Thanks!

One strength of this work is that the data were collected in the field, which may provide hard evidence with video footage showing the two flying squirrel populations made grooves on nuts as well as fixing them between twigs. This evidence will induce new interests to understand the causes and consequences of such nut grooving behaviour. It may be bold to claim that such behaviour involves advance cognition or cognitive process without proper, systematic, experiments. Accordingly, whether the squirrels are 'smart' remains unclear. The authors did well in describing and documenting the nut grooving behaviours of the two species of flying squirrels, which has achieved their first aim. However, as mentioned above, whether such behaviour is 'smart' will need more systematic investigations.

We have removed the description about cognition or cognitive process in the paper, and the paper is focused on the grooving behavious. “Smart” is also removed, with other words used instead.

Author Response

Reviewer #3 (Public Review):

1) (Schichl et al. 2011 JBC 286:38466). This publication is not cited in the current version of the manuscript. The results of Schichl et al. seem particularly relevant for the interpretation of some of the results presented here and should be considered in the final discussion and conclusions of the present work.

This reference and related text was added in the discussion section in the revised manuscript (lines 508-517).

2) The ubiquitination of endogenous TTP has not been demonstrated.

New data assessing the ubiquitination of endogenous TTP was added as Figure 1 – figure supplement 1D.

3) The type of ubiquitination detected on the overexpressed version of TTP is not characterized. This seems important in view of the results of Schichl et al. who showed non-degradative ubiquitination (K63) of TTP.

New data with the detection of K48- or K63-linked poly-ubiquitin chain by specific antibodies was added as Figure 1 – figure supplement 1G. These data show that recombinant poly-ubiquitin chains can be readily detected with both antibodies, but that only K48-linked chains were detected on TTP IPed from cells.

4) The half-life of the non-ubiquitinated mutant of TTP (K→R) was not precisely compared to the half-life of the wild-type TTP protein (similar to the experiment presented in 1B).

New data from TTP-KtoR chase experiments was added as Figure 1 – figure supplement 1E. The half-life was increased substantially from 1.4 h for wtTTP to 5.7 h for the mutant.

5) The effect of the E1 ubiquitin ligase TAk-243 on endogenous TTP levels was not tested.

New data assessing the effect of TAK-243 on endogenous TTP was added as Figure 1 – figure supplement 1B. Consistent with our data with exogenously expressed TTP, treatment with the inhibitor increased the abundance of endogenous TTP.

6) While they demonstrate that TTP-HA is efficiently degraded after 3 to 7h of LPS stimulation (Fig 1B) and that the stronger decrease in mCherry-TTP fusion level occurs between 4 and 6h of LPS stimulation the screen for identification of TTP modulators is performed 16h of LPS stimulation (Fig 2A). The rationale behind this experimental setting is not explicitly described.

We found that endogenous TTP and mCherry-TTP levels were substantially lower at 16 h post-LPS stimulation compared to 6 h. (see Fig. 1D), and reasoned that this would yield the best genetic screen window in which to identify mutant cells with non-functional degradation mechanisms.

7) The authors did not directly test the effect of HUWE1 inactivation on endogenous TTP accumulation after blocking protein synthesis. This control seems important as data presented in figure 2E could result both from an effect of Huwe1 level on LPS-induced TTP synthesis and TTP degradation.

New data from chase experiments with endogenous TTP have been added as Fig. 2G. Consistent with the data presented in Fig. 2E, TTP levels declined during the chase period in sgROSA control cells, with an estimated half-life of 3.7 h. In contrast, TTP levels did not significantly decline during the CHX chase period in Huwe1 KO cells, resulting in an estimated TTP protein half-life of ~20 h in this genotype.

8) In the data presented in figure 2, it is not entirely clear what exactly the authors are referring to as "endogenous TTP". In Figure 2C endogenous TTP is detected by western blot on cells transfected with an mCherry-TTP fusion. In this case, the size difference allows unambiguous identification of the endogenous form of TTP (although one could not exclude that overexpressing a TTP fusion protein might affect the level of the endogenous protein). However, TTP and mCherry-TTP cannot be distinguished by FACS (Fig2 D and E). If cells used in the experiments shown in 2C and 2D-E are distinct, this should be mentioned more explicitly in the legend of Fig. 2. Otherwise, the detection of endogenous TTP should be performed on cells that do not express mCherry-TTP.

Results from Fig. 2D/E are indeed from cells that do not express mCherry-TTP. Endogenous TTP is detected in these cells by intracellular antibody staining. The figure legend text has been updated to reflect that panel 2C is with the RAW264.7-Dox-Cas9-mCherry-TTP cell line, and D-E is with the RAW264.7-Dox-Cas9 cell line.

9) The third part of the manuscript aims to demonstrate that loss of Huwe1 decreases the half-life of pro-inflammatory mRNAs controlled by TTP. In my opinion, this conclusion is reliably supported by the data presented in Figure 3 and Supplementary Figure 3. As the conclusion of this paragraph refers to the effect of TTP on the stability of these mRNAs, the measurement of TNF mRNA stability (Fig. sup. 3C) should be presented in the main part of Fig. 3.

The TNF mRNA stability figure panel was moved to the main figures as Fig. 3C.

10) Fig 4E aims to identify kinases and phosphatases potentially involved in TTP stability (line 277, line 298). However, the approach used here (a measure of intracellular TTP level) cannot distinguish between increased production of TTP or a decrease in TTP degradation.

One of the main points of this experiment was to assess whether the steady-state increase in TTP in HUWE1 KO cells, which stems for an important part from increased stability (Fig. 2G), was influenced by TTP phospho-status. Thus, while we do not explicitly measure TTP protein half-life in this particular assay, it is very likely to reflect changes in TTP protein stability. This idea is consistent with the fact that treatment with p38i, MK2i, and CaclycA affected TTP steady-state levels consistent with their previously reported effects on TTP protein stability.

11) Also, the result presented in fig. 4E, are not totally consistent with the results presented in 4A. Fig4D shows a similar level of endogenous TTP accumulating after 2h of LPS stimulation in Huwe1 KO and control cells while a clear difference in TTP level is observable in the same condition in fig. 4A. Could the difference in the TTP detection method (Western vs intracellular FACS) be responsible for this discrepancy?

We do not exactly know, but agree that this could indeed be influenced by the measurement method per se, as well as small variations in cell density, or total sample numbers in a particular experiment (as this may increase the time outside of the incubator for handling/stimulations). The much larger sample size of the experiment from panel 6E, and having multiple different stimulations, may have contributed to a slightly delayed timing of the Huwe1-dependent phenotype. It is important to note, that we have consistently demonstrated with different measurement methods, that TTP is initially stabilized post-LPS treatment (2-3 h, insensitive to Huwe1 KO), followed by TTP degradation (6-16h, sensitive to Huwe1 KO).

12) These experiments and data presented in Fig.5D show that the level of the TTP paralog ZFP36L1 accumulates in huwe1 KO cells but do not demonstrate that HUWE1 affects ZFP36L1 protein stability.

We agree, and changed all instances in the text that claimed ZFP36L1 ‘stabilization’ to ‘increase in abundance’.

13) Based on data presented in fig. 6 B and sup. 6B the authors conclude that residues S52 and 178, previously identified as regulators of TTP stability, are unlikely to be involved in HUWE1-dependent TTP accumulation. The data are only based on 2 independent experiments, one of which (fig 6B) shows a difference in TTP S52/S178 mutant in Huwe1 deficient cells as compared to wt TTP. These results seem therefore too preliminary to reliably exclude the implication of S52 and 178 on the HUWE1 accumulation of TTP.

Additional new data with the S52/178 TTP mutant of six biological replicates has been added to the manuscript as Figure 6 – figure supplement 1C. Data from these experiments are consistent with our other results, and show that protein levels similarly increase for both wtTTP and the S52/178A mutant in Huwe1 KO cells.

14) From these data, the authors conclude (line 416) that N-terminal deletion does not affect the TTP protein level. However, TTP accumulation in Huwe1 KO cells seems mostly lost in mutant N4. As mentioned above the limited number of replicates (n=2) and the absence of a statistical test makes the interpretation of this result difficult.

Additional new data with the Δ4 mutant of two biological replicates has been added to the manuscript as Figure 6 – figure supplement 1E. Data from these experiments are consistent with our other results, and show that protein levels similarly increase for the Δ4 mutant in Huwe1 KO cells.

15) Several TTP C-terminal mutants show a HUWE1-independent accumulation when compared to the wt protein (Fig6. D). Is this region identical to the unstructured region identified by Ngoc (line 1255) as a potent regulator of TTP degradation? If relevant this point should be discussed.

Ngoc showed that fusion to GFP of either the N-terminal TTP part, or the TTP Cterminal part (aa 214-436), destabilized GFP in cells. Thus, the GFP destabilization was seemingly indiscriminate, and possibly caused by the disordered nature of the fusion construct per se. Since the C-terminal TTP part fused to GFP by Ngoc included aa 214-436, we cannot rule out that part of this effect was HUWE1-dependent. However, the discrepancy with our finding that the TTP N-terminus does not contribute to HUWE1-dependent TTP regulation, may suggest that the GFP fusions by Ngoc were destabilized by more general protein principles, rather than HUWE1-specific effects. Additional text conveying this notion was added to the Discussion section (line 490-497).

Author Response

Reviewer #1 (Public Review):

Understanding the evolution of nitrogenases is a very important problem in the field of evolutionary biogeochemistry. Ancestral sequence reconstruction at least in theory could offer insights into how this planet alerting activity evolved from ancestors that did not reduce nitrogen. But the very many components of the nitrogenase enzyme system make this a very challenging question to answer.

This paper now demonstrates the first empirical resurrection of functional ancestral nitrogenases both in vivo and in vitro. The nodes that are resurrected are very shallow in the nitrogenase tree and do not help answer how these proteins evolved. The authors' reasoning for choosing these nodes is that they are likely compatible with the metal cluster assembly machinery of their chosen host organism, A. vinelandii. The reader is left to wonder if deeper, more interesting nodes were tried but didn't yield any activity. As the paper stands, it proves that relatively shallow nitrogenase ancestors can be resurrected, but these nodes do not yet teach us anything very fundamental about how these enzymes evolved.

Technically, this work was no doubt challenging. Genome engineering in A vinelandii is very difficult and time-consuming. This organism was chosen because it is an obligate aerobe, which makes it easier to handle than the many anaerobic bacteria and archaea that harbor nitrogenases. It does make one wonder if this choice of organism is wise: the authors themselves note that it probably has a set of specialized proteins that allow the nitrogenase to be assembled and function in the presence of oxygen. This may limit A. vinelandii's potential future ancestral reconstructions deeper in the tree, which according to the authors' reasoning probably requires different assembly machinery.

The ancestral sequence reconstruction is done in two different ways: Two out of three reconstructions are carried out with what appears to be an incorrect algorithm implemented in older versions of RaxML. This algorithm is not a full marginal reconstruction, because it only considers the descendants of the node of interest for the reconstruction. The full algorithm (implemented e.g. in PAML and the newest versions of RaxML) considers all tips for a marginal reconstruction. The fact that this was called a marginal ancestral sequence reconstruction in RaxML's manual is unfortunate - as far as I understand it is in fact just the internal labelling of nodes produced by the pruning algorithm, which is not equivalent to a marginal reconstruction. In this specific case, it is unlikely that this has led to any fundamental issues with the reconstructions (as all are functional nitrogenases, which is to be expected in this part of the tree). For the shallower of the two nodes, the authors in fact verify that they get the same experimental results if they use PAML's full implementation of a marginal reconstruction (which yields a somewhat different sequence for this node). It would have been helpful to point this RaxML-related issue out in the methods, so as to prevent others from using this incorrect implementation of the ASR algorithm.

One other slightly confusing aspect of the paper is that it contains two different maximum likelihood trees, which were apparently inferred using the same dataset, model, and version of RaxML. It is unclear why they have different topologies. This probably indicates a lack of convergence. Again, this does not cast any doubt on the uncontroversial findings of this paper that shallow nodes within the nitrogenases are also nitrogenases.

We thank the reviewer for their careful appraisal of our article, and their helpful recommendations for improving its quality. We appreciate the reviewer’s comment regarding the experimental challenges associated with nitrogenase engineering and genetic studies of our bacterial model, Azotobacter vinelandii. The complexity of nitrogen fixation machinery does indeed present several experimental obstacles, though, as we note in our revised article, this feature also makes the systems-level approach we have implemented here ideal for evolutionary studies of nitrogenases and their associated network.

The reviewer focuses on three central points: 1) the relevance of the targeted ancestral nodes for addressing fundamental questions concerning nitrogenase origins, 2) the applicability of our bacterial model for older reconstructions, and 3) issues associated with the different trees/methods for ancestral sequence reconstruction.

Addressing the first point, we concede that targeting relatively shallow nodes cannot specifically test hypotheses concerning the earliest stages of nitrogenase evolution (e.g., “how this planet altering activity evolved from ancestors that did not reduce nitrogen”). Our central result is that a specific, enzymatic mechanism for dinitrogen binding reduction (established for three modern nitrogenases to date) extends back through nitrogenase ancestry over the studied timeline. More broadly, a conserved nitrogenase mechanism in the only surviving family of nitrogenase families suggests that life may have been constrained in its available strategies for achieving this challenging biochemical reaction. By comparison, multiple abiotic pathways for nitrogen fixation are feasible, and another, ecologically vital metabolism, carbon fixation, can proceed by at least seven pathways. Deeper investigations into these possible evolutionary constraints and across deeper portions of the nitrogenase tree will require continued study, which we anticipate will be facilitated by the experimental approach presented in this article.

Concerning the applicability of our bacterial model, we agree that it is possible that older reconstructions may require different host organisms so as to provide a compatible genetic background. Similar considerations we have outlined in our article, including a systematic evaluation of the genetic components that likely accompanied nitrogenase ancestors in their ancient hosts, will likely be necessary. Nevertheless, we foresee that the general, systems-level approach that we have built for Azotobacter can be adapted for additional microbial models, and that these efforts will be worthwhile given the significance of biological nitrogen fixation to evolutionary biogeochemistry and microbial engineering applications.

Finally, we thank the reviewer for noting the differences in the ancestral sequence reconstruction algorithms of RAxML v.8 and PAML and welcome an explanation of these issues in our revised article. We confirm that RAxML v.8 does not perform full marginal reconstruction (in contradiction to its description in the RAxML manual). Due to this concern, we repeated our ancestral sequence reconstruction with PAML, which, like newer versions of RAxML, does implement the full algorithm. Here, ancestors reconstructed by RAxML v.8 and PAML from equivalent phylogenetic nodes yield comparable experimental results, indicating that the algorithm differences have not significantly impacted the major outcomes of our study. In the second analysis, we repeated the entire phylogenetic ancestral sequence reconstruction workflow, though did not trim the alignment as we did in the first case (this has now been clarified). This likely explains the differences in our trees, as the reviewer notes. We have included these details in the Materials and Methods section of our revised article.

In addition to expanding upon the points outlined above throughout the revised article, we have included additional text in the Discussion that elaborates on the limitations of our study, and in particular, the need to explore deeper portions of the nitrogenase tree in future work.

Reviewer #2 (Public Review):

The authors convincingly show that their reconstructed ancestral nitrogenases are active both in vivo and in vitro, and show similar inhibitory effects as extant/wild-type enzymes.

The conclusion that, evolutionarily, there is a "single available mechanism for dinitrogen reduction" is not well explored in the paper. This suggests a limitation of using ancestral sequence reconstruction in this instance.

We thank the reviewer for their comments and appreciate their assessment that the core experimental results are conclusively demonstrated, including in vivo/in vitro activity of ancestral nitrogenase enzymes and that they all exhibit the specific mechanism for dinitrogen binding and reduction, evidenced by hydrogen inhibition.

We note the reviewer’s concern regarding the evolution of the dinitrogen reduction mechanism described above. Our primary conclusion is that this mechanism is conserved in the studied nitrogenase ancestors, which, together with previous demonstrations of this mechanism in the different nitrogenase isozymes (Mo, V, Fe) of Azotobacter vinelandii, suggests that this is an early evolved feature of the nitrogenase family. These enzymes have thus not only been performing an ecologically vital, metabolic function, but have likely been achieving this challenging biochemical reaction in the same manner for billions of years. We discuss the resulting implications as they relate to evolutionary constraints on biological nitrogen fixation strategies. We clarify that our presented paleomolecular approach cannot directly evaluate alternate evolutionary scenarios that did not persist and were not preserved in extant genomic sequences, as ancestral sequence reconstruction is fundamentally informed by extant sequence diversity. Our approach is a powerful tool for defining the contours of ancestral nitrogenase sequence-function space, which can serve as a basis for engineering and evaluating alternate scenarios. We have clarified these points in our Discussion.

Reviewer #3 (Public Review):

In this work, the authors attempt to probe the constraints on the early evolution of nitrogen fixation, the development of which presented a key metabolic transition. Given that life on Earth evolved only once (to our knowledge) which aspects were necessary and which may have taken a different course are open questions. Are there alternative forms of life, metabolic networks, or even enzymatic mechanisms that could have replaced the ones we see today, or is the space of possible biologies limited? This manuscript tests the ability of ancestrally-reconstructed molybdenum-dependent nitrogenase complexes to support diazotrophic growth in Azotobacter vinelandii, as well as in vivo and in vitro activity, which all point towards a conserved mechanism for nitrogen reduction at least since proteobacteria divergence.

This is an ambitious project, requiring multiple techniques, systems, and approaches, and the successful combination of these is one of the major strengths of this work. Using parallel techniques is an important way to be certain that the overall results are robust, and an appropriate mix of in vivo and in vitro experiments is chosen here. The manuscript should serve as a useful model for how to combine phylogenetics and biochemistry.

The nature of ASR means that a solid phylogeny and/or understanding of how robust the results are to uncertainty in reconstructed states is essential since all results flow from there. The overall phylogenetic methods used are appropriate and the system is an apt one for the technique, but there is not quite enough detail in the methods to be certain of the results. Given that only the single maximum a posteriori sequence is assayed at every 3 nodes, this may have compounding results in that the sensitivity to uncertainty in the reconstruction is increased. The authors appropriately make qualitative rather than quantitative inferences, but some hesitation towards the overall results still exists.

The assumption that the Anc1A/B and Anc2 nodes correspond to ancestral states might be undermined by horizontal gene transmission, which has been reported for nif clusters. In particular, there may be different patterns of transmission for each element of the cluster. By performing reconstruction with a concatenated alignment, the phylogenetic signal is potentially maximized, but with the assumption that each gene has an identical history. Discordant transmission may cause an incorrect topology to be recovered.

Finally, I am unsure if ASR is the most appropriate approach to answer questions of contingency and alternative pathways for protein evolution. ASR may tell what nitrogenase millions or billions of years ago looked like, but it can only say what has already existed. If there are different mechanisms or metabolic pathways enabling nitrogen fixation that simply never came to pass, via contingency and entrenchment or simple chance, ASR would say nothing about them. It is true that a conserved mechanism would point towards a constrained space for evolving nitrogen fixation, but that does not directly address it.

Overall, despite these issues, the manuscript is compellingly written and the figures are attractive and clear, and help get the major narrative across. This work will be of interest to protein biochemists of evolutionary bent and microbial physiologists with an interest in the origins of life.

We thank the reviewer for their evaluation of our study and appreciate their comments regarding the experimental effort involved and scientific significance. We have carefully considered their recommendations to improve our article.

The reviewer’s critical comments concern 1) the level of detail regarding the phylogenetic methodology, 2) the impact of horizontal gene transfer on phylogenetic reconstructions, and 3) the appropriateness of ancestral sequence reconstruction for accessing alternate evolutionary scenarios in the emergence of biological nitrogen fixation.

We have addressed the first point by including additional methodological details regarding our phylogenetic analyses in our Materials and Methods section, including alignment and model testing tools, as well as our rationale for using two ancestral sequence reconstruction methods, RAxML and PAML.

Regarding the second point, we acknowledge that horizontal gene transfer has played a significant role in the evolution and distribution of biological nitrogen fixation, which has been established and explored in previous work by others. We have included in our Discussion an additional paragraph which addresses potential impact of horizontal gene transfer in nitrogenase evolution. Though we do not expect horizontal transfer to contribute a significant source of uncertainty in the timeline studied for the reasons discussed in the revised manuscript, we agree that it is an important consideration for future work and that may impact reconstructions in other lineages within the nitrogenase phylogeny.

Finally, in new text within the Discussion, we also acknowledge that ancestral sequence reconstruction cannot yet directly test alternate historical scenarios. We have clarified our language concerning conservation and constraints in the evolution of biological nitrogen fixation. Because ancestral sequence reconstruction is informed by modern sequences, it is limited to exploring the historical sequence space within their shared ancestry. It is therefore possible that, early in the history of life, there were multiple enzymatic strategies for fixing nitrogen, and that they were outcompeted and thus have left no trace in modern genomes. Another possibility is that these alternate strategies simply never evolved.

In the present study, we have identified a pattern of conservation with regard to a specific mechanism for dinitrogen binding and reduction, suggesting a level of evolutionary constraint that can be further interrogated. For example, ancestral sequence reconstruction, as implemented in our nitrogenase resurrection strategy, can be used to empirically investigate the underlying sources of these constraints. We note that despite decades of research in this domain, a full understanding of how nitrogenases perform this remarkable metabolic step, both today and in the past, remains elusive (as other reviewers of the present study have also noted). Evolutionarily informed studies of nitrogenase function enabled by ASR can reveal the design principles that have shaped its direct ancestry, which can potentially serve as a basis for engineering alternative molecular strategies for nitrogen fixation. The power of the molecular paleogenetic approach here is in extending functional investigations beyond the sequence space occupied by modern nitrogenase and identifying patterns in their functional variation through their evolutionary histories.

Author Response

Reviewer #1 (Public Review):

Because of the importance of brain and cognitive traits in human evolution, brain morphology and neural phenotypes have been the subject of considerable attention. However, work on the molecular basis of brain evolution has tended to focus on only a handful of species (i.e., human, chimp, rhesus macaque, mouse), whereas work that adopts a phylogenetic comparative approach (e.g., to identify the ecological correlates of brain evolution) has not been concerned with molecular mechanism. In this study, Kliesmete, Wange, and colleagues attempt to bridge this gap by studying protein and cis-regulatory element evolution for the gene TRNP1, across up to 45 mammals. They provide evidence that TRNP1 protein evolution rates and its ability to drive neural stem cell proliferation are correlated with brain size and/or cortical folding in mammals, and that activity of one TRNP1 cis-regulatory element may also predict cortical folding.

There is a lot to like about this manuscript. Its broad evolutionary scope represents an important advance over the narrower comparisons that dominate the literature on the genetics of primate brain evolution. The integration of molecular evolution with experimental tests for function is also a strength. For example, showing that TRNP1 from five different mammals drives differences in neural stem cell proliferation, which in turn correlate with brain size and cortical folding, is a very nice result. At the same time, the paper is a good reminder of the difficulty of conclusively linking macroevolutionary patterns of trait evolution to molecular function. While TRNP1 is a moderate outlier in the correlation between rate of protein evolution and brain morphology compared to 125 other genes, this result is likely sensitive to how the comparison set is chosen; additionally, it's not clear that a correlation with evolutionary rate is what should be expected. Further, while the authors show that changes in TRNP1 sequence have functional consequences, they cannot show that these changes are directly responsible for size or folding differences, or that positive selection on TRNP1 is because of selection on brain morphology (high bars to clear). Nevertheless, their findings contribute strong evidence that TRNP1 is an interesting candidate gene for studying brain evolution. They also provide a model for how functional follow-up can enrich sequence-based comparative analysis.

We thank the reviewer for the positive assessment. With respect to our set of control genes and the interpretation of the correlation between the evolution of the TRNP1 protein sequence and the evolution of brain size and gyrification, we would like to mention the following: we do think that the set is small, but we took all similarly sized genes with one coding exon that we could find in all 30 species. Furthermore, the control genes are well comparable to TRNP1 with respect to alignment quality and average omega (Figure 1-figure supplement 3). Hence, we think that the selection procedure and the actual omega distribution make them a valid, unbiased set to which TRNP1’s co-evolution with brain phenotypes can be compared to. Moreover, we want to point out that by using Coevol, we correlate evolutionary rates, that is the rate of protein evolution of TRNP1 as measured with omega and the rate of brain size evolution that is modeled in Coevol as a Brownian motion process. We think that this was unclear in the previous version of our manuscript, and appreciate that the reviewer saw some merit in our analyses in spite of it.

Finding conclusive evidence to link molecular evolution to concrete phenotypes is indeed difficult and necessarily inferential. This said, we still believe that correlating rates of evolution of phenotype and sequence across a phylogeny is one of the most convincing pieces of evidence available.

Reviewer #2 (Public Review):

In this paper, Kliesmete et al. analyze the protein and regulatory evolution of TRNP1, linking it to the evolution of brain size in mammals. We feel that this is very interesting and the conclusions are generally supported, with one concern.

The comparison of dN/dS (omega) values to 125 control proteins is helpful, but an important factor was not controlled. The fraction of a protein in an intrinsically disordered region (IDR) is potentially even more important in affecting dN/dS than the protein length or number of exons. We suggest comparing dN/dS of TRNP1 to another control set, preferably at least ~500 proteins, which have similar % IDR.

Thank you for this interesting suggestion. As mentioned in the public response to Reviewer #1, we are sorry that we did not explain the rationale of the approach very well in the previous version of the manuscript. As also argued above, we think that our control proteins are an unbiased set as they have a comparable alignment quality and an average omega (dN/dS) similar to TRNP1 (Figure 1-figure supplement 3). While IDR domains tend to have a higher omega than their respective non-IDR counterparts, we do not think that the IDR content should be more relevant than omega itself as we do not interpret this estimate on its own, but its covariance with the rate of phenotypic change. Indeed, the proteins of our control set that have a higher IDR content (D2P2, Oates et al. 2013) do not show stronger evidence to be coevolving with the brain phenotypes (IDR content vs. absolute brain size-omega partial correlation: Kendall's tau = 0.048, p-value = 0.45; IDR content vs. absolute GI-omega partial correlation: Kendall’s tau = -0.025, p-value = 0.68; 88 proteins (71%) contain >0% IDRs; 8 proteins contain >62% (TRNP1 content) IDRs.

Reviewer #3 (Public Review):

In this work, Z. Kliesmete, L. Wange and colleagues investigate TRNP1 as a gene of potential interest for the evolution of the mammalian cortex. Previous evidence suggests that TRNP1 is involved in self-renewal, proliferation and expansion in cortical cells in mouse and ferret, making this gene a good candidate for evolutionary investigation. The authors designed an experimental scheme to test two non-exclusive hypotheses: first, that evolution of the TRNP1 protein is involved in the apparition of larger and more convoluted brains; and second, that regulation of the TRNP1 gene also plays a role in this process alongside protein evolution.

The authors report that the rate of TRNP1 protein evolution is strongly correlated to brain size and gyrification, with species with larger and more convoluted brains having more divergent sequences at this gene locus. The correlation with body mass was not as strong, suggesting a functional link between TRNP1 and brain evolution. The authors directly tested the effects of sequence changes by transfecting the TRNP1 sequences from 5 different species in mouse neural stem cells and quantifying cell proliferation. They show that both human and dolphin sequences induce higher proliferation, consistent with larger brain sizes and gyrifications in these two species. Then, the authors identified six potential cis-regulatory elements around the TRNP1 gene that are active in human fetal brain, and that may be involved in its regulation. To investigate whether sequence evolution at these sites results in changes in TRNP1 expression, the authors performed a massively parallel reporter assay using sequences from 75 mammals at these six loci. The authors report that one of the cis-regulatory elements drives reporter expression levels that are somewhat correlated to gyrification in catarrhine monkeys. Consistent with the activity of this cis-regulatory sequence in the fetal brain, the authors report that this element contains binding sites for TFs active in brain development, and contains stronger binding sites for CTCF in catarrhine monkeys than in other species. However, the specificity or functional relevance of this signal is unclear.

Altogether, this is an interesting study that combines evolutionary analysis and molecular validation in cell cultures using a variety of well-designed assays. The main conclusions - that TRNP1 is likely involved in brain evolution in mammals - are mostly well supported, although the involvement of gene regulation in this process remains inconclusive.

Strengths:

• The authors have done a good deal of resequencing and data polishing to ensure that they obtained high-quality sequences for the TRNP1 gene in each species, which enabled a higher confidence investigation of this locus.

• The statistical design is generally well done and appears robust.

• The combination of evolutionary analysis and in vivo validation in neural precursor cells is interesting and powerful, and goes beyond the majority of studies in the field. I also appreciated that the authors investigated both protein and regulatory evolution at this locus in significant detail, including performing a MPRA assay across species, which is an interesting strategy in this context.

Weaknesses:

• The authors report that TRNP1 evolves under positive selection, however this seems to be the case for many of the control proteins as well, which suggests that the signal is non-specific and possibly due to misspecifications in the model.

• The evidence for a higher regulatory activity of the intronic cis-regulatory element highlighted by the authors is fairly weak: correlation across species is only 0.07, consistent with the rapid evolution of enhancers in mammals, and the correlation in catarrhine monkeys is seems driven by a couple of outlier datapoints across the 10 species. It is unclear whether false discovery rates were controlled for in this analysis.

• The analysis of the regulatory content in this putative enhancer provides some tangential evidence but no reliable conclusions regarding the involvement of regulatory changes at this locus in brain evolution.

We thank the reviewer for the detailed comments. Indeed, TRNP1 overall has a rather average omega value across the tree and hence also the proportion of sites under selection is not hugely increased compared to the control proteins. This is good because we want to have comparable power to detect a correlation between the rate of protein evolution (omega) and the rate of brain size or GI evolution for TRNP1 and the control proteins. Indeed, what makes TRNP1 special is the rather strong correlation between the rate of brain size change and omega, which was only stronger in 4% of our control proteins. Hence, we do not agree with the weakness of model misspecification for TRNP1 protein evolution.

We agree that the correlation of the activity induced by the intronic cis regulatory element (CRE) with gyrification is weak, but we dispute that the correlation is due to outliers (see residual plot below) or violations of model assumptions (see new permutation analysis in the Results section). There are many reasons why we would expect such a correlation not to be weak, including that a MPRA takes the CRE out of its natural genomic context. Our conclusions do not solely rest on those statistics, but also on independent corroborating evidence: Reilly et al (2015) found a difference in the activity of the TRNP1 intron between human and macaque samples during brain development. Furthermore, we used their and other public data to show that the intron CRE is indeed active in humans and bound by CTCF (new Figure 4 - figure supplement 2).

We believe that the combined evidence suggests a likely role for the intron CRE for the co-evolution of TRNP1 with gyrification.

Author Response

Reviewer #1 (Public Review):

The study's primary motivating goal of understanding how nutrigenomic signaling works in different contexts. The authors propose that OGT- a sugar-sensing enzyme- connects sugar levels to chromatin accessibility. Specifically, the authors hypothesize that the OGT/Plc-PRC axis in sweet taste neurons interprets the sugar levels and alters chromatin accessibility in sugar-activated neurons. However, the detailed model presented by authors on OGT/PRC/Pcl Rolled in regulating nutrigenomic signaling relies on pharmacological treatments and overexpression of transgenes to derive genetic interactions and pathways; these approaches provide speculative rather than convincing evidence. Secondly, evidence is absent to show that PRC occupancy remains the same in other neurons (non-sweet taste neurons) under varied sugar levels or OGT manipulations. Hence, the claim that OGT-mediated access to chromatin via PRC-Plc is a key regulatory arm of nutrigenomic signaling needs further substantiation.

We thank the reviewer for their thoughtful reading of the manuscript and their suggestions. We disagree with the reviewer’s assessment that our work only relies solely on overexpression and pharmacological treatments and that this provides only “speculative” evidence. Indeed, both of the other two reviewers praised our approach:

Reviewer 2: “This is an elegant group of experiments revealing mechanisms for how nutrigenomic signaling triggers cellular responses to nutrients”

Reviewer 3: “Strengths: Good genetically targeted interventions; Thorough exploration of the epistatic relationships between different players in the system … The conclusions in this manuscript are mostly well or at least reasonably supported by data.

All of our experiments combine genetic manipulations in combination with dietary and/or pharmacological treatments to show that molecular, neural, and behavioral taste phenotypes arise only in specific contexts, so no single phenotype occurs due to nonspecific manipulations. Without this approach, most of these epistatic relationships would be largely inaccessible in this system. We have also used a combination of both genetic and pharmacological tools to implicate not only genes but also their function (i.e., enzymatic activity) to nutrient-specific effects. Third, we established causality and relationship by inducing and rescuing the molecular, behavioral, and electrophysiological phenotypes. Thus, our model is based on a combination of direct and indirect data (genetic manipulations are by nature inferential) obtained from a controlled and careful set of experiments. Limitations of our approach were laid out under the “Limitation” section of the discussion, as well as alternative interpretations or possibilities. In the manuscript's revised version, we added additional genetic experiments to further support and validate our model and expanded data analyses as suggested by the reviewer.

Reviewer #2 (Public Review):

Nutrigenomics has advanced in recent years, with studies identifying how the food environment influences gene expression in multiple model organisms. The molecular mechanisms mediating these food-gene interactions are poorly understood. Previous work identified the enzyme O-GlcNAC (OGT) in mediating the decreased sensitivity in sweet-taste cells when exposed to a high-sugar diet. The present study, using fly gustatory neurons as a model, provides mechanistic insight into how nutrigenomic signaling encodes nutritional information into cellular changes. The authors expand previous work by showing that OGT is associated with neural chromatin at introns and transcriptional start sites, and that diet-induced changes in chromatin accessibility were amplified at loci with presence of both OGT and PRC2.1. The work also identifies Mitogen Activated Kinase as a critical mediator in this pathway. This is an elegant group of experiments revealing mechanisms for how nutrigenomic signaling triggers cellular responses to nutrients.

We thank the reviewer for their thoughtful reading of the manuscript and their positive and actionable suggestions. We have addressed these in the revised manuscript.

Reviewer #3 (Public Review):

This paper dissects the molecular mechanisms of diet induced taste plasticity in Drosophila. The authors had previously identified two proteins essential for sugar-diet derived reduction of sweet taste sensitivity - OGT and PRC2.1. Here, they showed that OGT, an enzyme implicated in metabolic signaling with chromatin binding functions, also binds a range of genomic loci in the fly sweet gustatory receptor neurons where binding in a subset of those sites is diet composition dependent. Furthermore, a minority of OGT binding sites overlapped with PRC2.1 recruiter Pcl, where collectively binding of both proteins increased under sugar-diet while chromatin accessibility decreased. The authors demonstrate, that the observed taste plasticity requires catalytic activity of OGT, which impacts chromatin accessibility at shared OGT x Pcl but not diet induced occupancy. In an effort to identify transcriptional mechanisms that instantiate the plastic changes in sensory neuron functions the authors looked for transcription factors with enriched motifs around OGT binding sites and identified Stripe (Sr) as a transcription factor that yielded sugar taste phenotypes upon gain and loss of function experiments. In follow-up overexpression experiments, they show that this results in reduced taste sensitivity and reduced taste evoked spiking in gustatory receptor neurons. Notably the effects of Sr on taste sensitivity also depend on OGT catalytic activity as well as PRC2.1 function. Finally, they explore the function of rolled (rl) - an extracellular-signal regulated kinase (ERK) ortholog in Drosophila, suggested to function upstream of Sr - in diet induced gustatory plasticity. The authors showed that the overexpression of the constitutively active form of rl kinase results in reduced neuronal and behavioral responses to sucrose which was dependent on OGT catalytic activity. In sum, these findings reveal several new players that link dietary experience to sensory neuron plasticity and open up clear avenues to explore up- and downstream mechanisms mediating this phenomenon.

Strengths:

• Good genetically targeted interventions

• Thorough exploration of the epistatic relationships between different players in the system• Identification of several new signaling systems and proteins regulating diet derived gustatory plasticity

Weaknesses:

• The GO term enrichment analyses with little functional follow up has limited explanatory power• ERK/rl data is a bit hard to interpret since any imbalance in this system appears to reduce gustatory sensitivity.

The conclusions in this manuscript are mostly well or at least reasonably supported by data.

We appreciate the reviewer’s thoughtful read of the manuscript and their feedback. We were pleased to read the reviewer’s positive comments on the experimental treatment of epistatic relationships and the identification of new pathways; we have addressed the reviewer’s comments and suggestions in the revised manuscript.

We agree with the reviewer about the limited explanatory power of the GO term analysis. We have expanded our computation analysis of the OGT/PRC2 genes in Figure 5 and selected several of these genes for functional analysis. In the revised version of the manuscript, we show that several of the genes affected by diet via this nutrigenomic pathway impact sugar taste sensation as measured by PER. We also agree with the reviewer that the Erk data are harder to interpret than those from OGT or PRC2; this effect is somewhat expected, given the reported action of this kinase in neural activity and plasticity. Importantly, the epistatic interactions between ERK/Sr and OGT/PRC2 we discovered are intriguing and may be involved in other cellular processes beyond taste.

Below are a few recommendations for improvement:

• The paper claims to address cell-type-specific nutrigenomic regulatory mechanisms. However, this work only explores nutrigenomic mechanisms in a single cell type (Gr5a+ sweet sensing cells) and we don't really learn whether these nutrigenomic mechanisms exist in all other cell types or just Gr5a+ cells. It would be valuable to see how specific OGT and PRC2.1 binding locations and effects on chromatin accessibility are in a different cell type - e.g. bitter sensing Gr66a. This would reveal how global in nature these findings are and or which aspects of nutrigenomic signaling are specific for sweet sensory cells.

This study is a cell-specific investigation of nutrigenomic mechanisms in the Gr5a+ sweet taste neurons, which is what we outlined to do. It was not our intention for this study to examine mechanisms across different cell types. However, we can understand the reviewer’s comment after rereading the abstract and introduction. As such, we have rewritten part of the manuscript to better introduce the rationale behind the study as the integration of metabolic signaling and cellular contexts. We hope this is now an improved framing for the study rationale.

(As in response to the author’s recommendations): About analyzing the effects of diet on other cells; no doubt this is an interesting question. However, this also signifies embarking on a completely separate project that would take, optimistically speaking, at least one year to complete and require a budget of ~ $130,000 (see breakdown). Thus, this suggestion doesn’t seem in line with the peer review and editorial philosophy of eLife. Carrying out this new project would result in an additional 6-7 figures but would not fundamentally change the conclusion of the current work; in fact, it may even take away from the targeted integration of molecular biology and neuroscience we have tried to achieve. Beyond this, we do not have such an unallocated budget, and so this new project would require us first to generate preliminary data on the bitter neurons to write then a grant proposal to fund it; as you can appreciate, this would take longer than a year, especially since we do not even know if the bitter gustatory neurons are affected by a high-sugar diet. Beyond this, looking at the bitter neurons would do little to prove specificity. If we found no effects of this pathway on the activity of the bitter neurons, it wouldn’t establish that the changes in the sweet taste neurons are specific. In fact, the same pathway could be acting in some of the other thousands of fly circuits that were not investigated (Black swan effect). If we did find that OGT/PRC2/Sr play a role in the bitter neurons, it would also do little to disprove specificity since their targets would likely be different because the sets of genes expressed in these two sensory neurons are different. By analogy, the protein sensor mTOR is expressed and active in every cell, where it modulates some of the same targets (i.e., S6K); however, the effects of the pathway may be different due to the distinct metabolic and genetic idiosyncrasies of cells, as well as cellular compartments. This lack of specificity doesn’t mean that mTOR is not important. Finally, we would like to note that we have tested the effects of manipulating OGT levels in other neurons (dopamine and Mushroom Body Output Neurons) without effects on behavior or neural responses (May et al. 2020; Pardo-Garcia et al. 2022); based on these, OGT doesn’t seem to affect neurons indiscriminately.

Budget = $129,000

Salary and benefit for PD for 10 calendar months: (2 months behavior experiments, 2 months training for molecular biology experiments and troubleshooting in new neurons, 4 months growing flies and conducting experiments, 2 months data analysis and visualization)= $75,000. DAM ID: Pcl:dam and OGT:dam in CD and SD, with and without OSMI x 4 biological replicates per condition= 32 samples @ $500 per sample (UM Genomics core) $16,0000

TRAP: Pcl mutant and OSMI in CD and SD x 4 biological replicates per condition + sequencing input = 32 samples @ $500 per sample (UM Genomics core) $16,0000

Animals: $500 per person/10 months = $5,000

Reagents: including sequencing kit (32 reactions =$6,000) x 2 = $12,000, and other reagents such as drugs and plastic = $17,000

Note that this PD would have to be hired and retrained. The first author of the manuscript who carried out the molecular experiments graduated in Dec 2021 but failed to pass on the technical knowledge due to COVID restrictions at the UM: we were completely shut down until July 2020, and at 20% capacity from March 2020 to July 2021 (people couldn’t also work together to show techniques), and no new people joined the lab in 2020-2022 (most of the 2021 grad student class deferred to 2022).

● Behavioral data from the screen identifying Sr is missing. Which other candidates were screened and what were the phenotypes?

We have now added the screen data in Fig. 5-Supplemental Fig. 1C. We targeted RNAi and OE transgenes against the candidate transcription factors (or control RNAi) to the Gr5a+ neurons and measured PER to 30, 20, and 5% sucrose in fasted flies on a control diet.

● Go terms analysis for Figure 4

We selected a dozen DEGs dependent on OGT and PRC2.1 (purple circle in Fig. 4E) and tested the effects on PER when these were overexpressed or knocked down (depending on the direction of changes in the SD). In Fig. 4F we show the effects of a handful of them on proboscis responses to sucrose.

Author Response

Reviewer #2 (Public Review):

The ability of the model to recreate one non-trivial aspect of the crossover distribution is not sufficient to rule out other possible models, which would be necessary to consider this work a significant advance. However, if the authors are able to provide additional, non-trivial predictions relating to this and to other experimental conditions, this would dramatically elevate their ability to claim that a coarsening-based mechanism is indeed the most plausible one to explain crossover distribution. Some of these conditions could involve experimental perturbation of key parameters in the model: HEI10 levels, the number of DSBs or recombination intermediates (the 'substrate' that ends up resulting in crossovers), the length of time coarsening is allowed to proceed, or the volume of the nucleus.

As discussed above, we have now included additional experiments and modelling investigating the patterning of late-HEI10 foci in a pch2 mutant, which exhibits partial synapsis. We have also demonstrated that the nucleoplasmic coarsening model can explain the recently published massive elevation of COs in zyp1 + HEI10 overexpressor lines (Durand et al., 2022). We hope that these additional results, explaining other non-trivial aspects of CO patterning, sufficiently elevates this work to be considered as a significant advance within the field.

Reviewer #3 (Public Review):

The new model assumes the possibility of loading HEI10 directly from the nucleoplasm, which of course is logical considering the phenotype of the zyp1 mutant in Arabidopsis. However, in a situation where the SC is fully functional, should not we expect some level of nucleoplasmic coarsening in addition to the dominant SC-mediated coarsening? Should the original model not be corrected, and if it is not necessary (e.g., because it included this effect from the very beginning, or the effect is too weak and therefore negligible), the authors should discuss it. With reference to this observation, it would be worthwhile to compare different characteristics of both types of coarsening (e.g., time course).

We agree with this reviewer that it seems intuitive and likely that some small amount of nucleoplasmic coarsening will persist even in the wild-type situation. As mentioned above, we have now explicitly modelled a combined version of the coarsening model than incorporates aspects of SC and nucleoplasm-mediated coarsening and compared this to simulation outputs from our original coarsening model (which did not incorporate nucleoplasmic recycling). The effects and implications of combining the two models on coarsening dynamics are now discussed.

Recently, a preprint from the Raphael Mercier group has been released, in which the authors show a massive increase in crossover frequency in zyp1 mutants overexpressing HEI10. I think this is a great opportunity to check to what extent the parameters adopted by the authors in the nucleoplasmic coarsening model are universal and can correctly simulate such an experimental set-up. Therefore, can the authors perform such a simulation and validate it against the experimental data in Durand et al. doi.org/10.1101/2022.05.11.491364? Can CO sites identified by Durand et al. be used instead of MLH1 foci for the modeling?

As mentioned above, we have now incorporated additional modelling demonstrating that the nucleoplasmic coarsening model can reproduce the massive increase in COs observed in zyp1 + HEI10 overexpressor lines (Durand et al., 2022). We have compared our model simulations against cytological data from this study (MLH1 counts from male Col-0 plants) as we feel this is the most appropriate data to compare our model against. The remaining CO patterning data in the Durand et al., paper is from genetic experiments, which are not optimal for comparing model simulations against for two main reasons. Firstly, the metric of interference (and coarsening) is microns of axis/SC length and not, for example, Mbp and we feel that (due to the non-uniform compaction of chromatin along pachytene chromosomes) the coarsening model cannot currently be reliably used to explain genetic mapping data. Secondly, genetic CO data includes both class I and class II COs, whereas the coarsening model only simulates class I CO patterning. Therefore, we strongly feel that, for now, it is better to exclusively rely on cytological data to fit our model against.

Author Response

Reviewer #2 (Public Review):

By now, the public is aware of the peculiarities underlying the omicron variants emergence and dissemination globally. This study investigates the mutational biography underlying how mutation effects and epistasis manifest in binding to therapeutic receptors.

The study highlights how epistasis and other mutation effect measurements manifest in phenotypes associated with antibody binding with respect to spike protein in the omicron variant. It rigorously tests a large suite of mutations in the omicron receptor binding domain, highlighting differences in how mutation effects affect binding to certain therapeutic antibodies.

Interestingly, mutations of large effect drive escape from binding to certain antibodies, but not others (S309). The difference in the mutational signature is the most interesting finding, and in particular, the signature of how higher-order epistasis manifests in the partial escape in S309, but less so in the full escape of other antibodies.

The results are timely, the scope enormous, and the analyses responsible.

My only main criticisms walk the stylistic/scientific line: many of the others have pioneered discussions and methods relating to the measurement of epistasis in proteins and other biomolecules. While I recognize that the purpose of this study is focused on the public health implications, I would have appreciated more of a dive into the peculiarity of the finding with respect to epistasis. I think the authors could achieve this by doing the following:

a) Reconciling discussions around the mutation effects in light of contemporary discussions of global epistasis "vs" idiosyncratic epistasis, etc. Several of the authors of the manuscript have written other leading manuscripts of the topic. I would appreciate it if the authors couched the findings within other studies in this arena.

We added a discussion related to global epistasis at the end of the “Epistasis Analysis” methods section. We tried to highlight that the cause and relevance of global epistasis phenomena are quite different at molecular and at organismic level.

B) While the methods used to detect epistasis in the manuscript make sense, the authors surely realize that methods used to measure is a contentious dimension of the field. I'd appreciate an appeal/explanation as to why their methods were used relative to others. For example, the Lasso correction makes sense, but there are other such methods. Citations and some explanation would be great.

We added more context and justification in the methods section (Epistasis Analysis). We used Lasso correction not particularly to obtain a sparser representation of the epistasis coefficients (an assumption that is not always valid, particularly within proteins) but rather to reduce instabilities created by the Tobit model inference. In this inference, the model coefficients are unbounded. Thus, if one mutation causes a complete binding loss, all epistatic terms associated with this mutation are not constrained and can become very large in magnitude. A Lasso term with a small coefficient constrains these coefficients but will have a limited influence on the other coefficients.

Lastly (somewhat relatedly), I found myself wanting the discussion to be bolder and more ambitious. The summary, as I read it, is on the nose and very direct (which is appropriate), but I want more: What do the findings say for greater discussions surrounding evolution in sequence space? For discussions of epistasis in proteins of a certain kind? In, my view, this data set offers fodder for fundamental discussion in evolutionary biology and evolutionary medicine. I recognize, however, the constraints: such topics may not be within the scope of a single paper, and such discussions may distract from the biomedical applications, which are more relevant for human health.

But I might say something similar about the biomedical implications: the authors do a good job outlining exactly what happened, but what does this say about patterns (the role of mutations of large effect vs. higher-order epistasis) in some traits vs others? Why might we expect certain patterns of epistasis with respect to antibody binding relative to other pathogenic virus phenotypes?

We agree that these are interesting questions, and have added a paragraph in the discussion to explore these points.

In summary: rigorous and important work, and I congratulate the authors.

Author Response

Reviewer #1 (Public Review):

In this work, the authors investigate a means of cell communication through physical connections they call membrane tubules (similar or identical to the previously reported nanotubes, which they reference extensively). They show that Cas9 transfer between cells is facilitated by these structures rather than exosomes. A novel contribution is that this transfer is dependent on the pair of particular cell types and that the protein syncytin is required to establish a complete syncytial connection, which they show are open ended using electron microscopy.

The data is convincing because of the multiple readouts for transfer and the ultrastructural verification of the connection. The results support their conclusions. The implications are obvious, since it represents an avenue of cellular communication and modifications. It would be exciting if they could show this occurring in vivo, such as in tissue. The implication of this would be that neighboring cells in a tissue could be entrained over time through transfer of material.

Thank the reviewer for his/her comments and suggestion. It’s possible that the thick tubular connections found in this study also exist in vivo. A previous study reported that TNT-like structures were found in mouse or human primary tumor cells (PMID: 34494703; PMID: 34795441). Our transfer assays could be adopted to evaluate such transfer in primary cultures and in vivo. We anticipate this for future work.

Reviewer #2 (Public Review):

There is a lot of interest in how cells transfer materials (proteins, RNA, organelles) by extracellular vesicles (EV) and tunneling nanotubes (TNTs). Here, Zhang and Schekman developed quantitative assays, based on two different reporters, to measure EV and direct contact-dependent mediated transfer. The first assay is based on transfer of Cas9, which then edits a luciferase gene, whose enzymatic activity is then measured. The second assay is based on a split-GFP system. The experiments on EV trafficking convincingly show that purified exosomes, or any other diffusible agent, are unable to transfer functional Cas9 (either EV-tethered or untethered) and induce significant luciferase activity in acceptor cells. The authors suggest a plausible model by which Cas9 (with the gRNA?) gets "stuck" in such vesicles and is thus unable to enter the nucleus to edit the gene.

To test alternative pathways of transfer, e.g. by direct cell-cell contact, the authors co-cultured donor and acceptor cells and detect significant luciferase activity. The split GFP assay also showed successful transfer. The authors further characterize this process by biochemical, genetic and imaging approaches. They conclude that a small percentage of cells in the population produce open-ended membrane tubules (which are wider and distinct from TNTs) that can transfer material between cells. This process depends on actin polymerization but not endocytosis or trogocytosis. The process also seems to depend on endogenously expressed Syncytin proteins - fusogens which could be responsible for the membrane fusion leading to the open ends of the tubules.

The paper provides additional solid evidence to what is already known about the inefficiency of EV-mediated protein transport. Importantly, it provides an interesting new mechanism for contact-dependent transport of cellular material and assigns valuable new information about the possible function of Syncytins. However, the evidence that the proteins and vesicles transfer through the tubules is incomplete and a few more experiments are required. In addition, certain inconsistencies within the paper and with previous literature need to be resolved. Finally, some parts of the text, methods and the figures require re-writing or additional information for clarity.

Major comments

1) In Figure 1F, the authors compare the function of exosome-transported SBP-Cas9-GFP vs. transient transfection of SBP-Cas9-GFP. It is not clear if the cells in the transiently transfected culture also express the myc-str-CD63 and were treated with biotin. It is important to determine if CD63-tethering itself affects Cas9 function.

Thank the reviewer for his comments and suggestions. We now show in Figure 1- figure supplement 1D that CD63-tethering itself does not affect Cas9 function.

2) The authors do not rule out that TNTs are a mode of transfer in any of their experiments. Their actin polymerization inhibition experiments are also in-line with a TNT role in transfer. This possibility is not discussed in the discussion section.

Yes, the results in this study do not rule out a role for TNTs in the transfer. At present, we are not aware of conditions that would functionally distinguish transfer mediated by TNTs and thick tubules. We have now included this in the Discussion section.

3) Issues with the Split GFP assay:

a) On page 4, line 176, the authors claim that "A mixture of cells before co-culture should not exhibit a GFP signal". However, this result is not presented.

The results of mixture experiment are included in Figure 2-figure supplement 1D, E.

b) The authors show in Figure 2C and F that in MBA/HEK co-culture or only HEK293T co-culture, there are dual-labeled, CFP-mCherry, cells. First - what is the % of this sub-population? Second, the authors dismiss this population as cell adhesion (Page 5, line 192) - but in the methods section they claim they gated for single particles (page 17, line 642), supposedly excluding such events. There is a simple way to resolve this - sort these dual labeled cells and visualize under the microscope. Finally - why do the authors think that the GFP halves can transfer but not the mature CFP or mCherry?

The plot in the Figure 2C and F are displayed in an all-cell mode, not in singlet mode. The percentage of dual-labeled CFP-mCherry in singlet was 0-0.2%. Thus, most of the signal was from doublet, or cell adhesion. We did not claim that the mature CFP or mCherry cannot be transferred. We suggested that the GFP signal of split-GFP recombination may be a more accurate reflection of cytoplasmic transfer between cells. In contrast, mature CFP or mCherry may simply attach to the cell surface but not enter into the other cells.

c) In the Cas9 experiments - the authors detect an increase in Nluc activity similar in order of magnitude that that of transient transfection with the Cas9 plasmid - suggesting most acceptor cells now express Nluc. However, only 6% of the cells are GFP positive in the split-GFP assay. Can the authors explain why the rate is so low in the split-GFP assay? One possibility (related to item #2 above) is that the split-GFP is transferred by TNTs.

The Cas9-based Nluc activity assay is more sensitive as it measures an enzyme with a very high turnover number. The split-GFP assay requires a transfer of GFP fragments to produce intact GFP molecules where the signal is not amplified. We think this explains the dramatic increase in a signal once Cas9 is transferred. Our cell sorting results suggest that at least 6% of the receptor cells are transferred in the co-cultures. Of course, nothing in either analysis rules out a role for TNTs in this transfer.

4) The membrane tubules, the membrane fusion and the transfer process are not well characterized:

a) The suggested tubules are distinct from TNTs by diameter and (I presume, based on the images) that they are still attached to the surface - whereas TNTs are detached. However, how are these structures different from filopodia except that they (rarely) fuse?

We used TIRF microscopy and found that the thick tubules are not attached to the surface (not shown). Filopodia are much closer in diameter to TNTs (0.1-0.4 micron). The thick tubules we observe are much thicker (2-4 micron in diameter).

b) Figure 5E shows that the acceptor cells send out a tubule of its own to meet and fuse. Is this the case in all 8 open-ended tubules that were imaged? Is this structure absent in the closed-ended tubules (e.g. as seen in Figures 6 & 8)?

Around half of open-ended tubules appeared to emanate from acceptor cells. Likewise, for closed-ended tubules, for example, in Figure 6E where a recipient HEK293T cell projected a short tubule.

c) The authors suggest a model for transport of the proteins tethered to vesicles (via CD63 tethering). However, the data is incomplete.

i) They show only a single example of this type of transport, without quantification. How frequent is this event?

The transport of the proteins tethered to vesicles (via CD63 tethering) were found in all 8 open-ended tubules that we detected in this study.

ii) Furthermore, the labeling does not conclusively show that these are vesicles and not protein aggregates. Labeling of the vesicle - by dye or protein marker will be useful to determine if these are indeed vesicles, and which type.

In Figure 4B, the moving punctum in a tubular connection appears to contain SBP-Cas9-GFP, Streptavidin-CD63-mCherry, and the cell surface WGA conjugate that may have been internalized into a donor cell endosome, which indicates that the moving punctum is vesicle type. Nonetheless, in general we cannot distinguish the forms of Cas9 that are transferred and become localized to the nucleus of target cells and we make no claim other than to suggest this possibility that Cas9 may be transferred as an aggregate.

iii) The data from Figure 2 suggest (if I understand correctly) transfer of the CD63-tethered half-GFP, further strengthening the idea of vesicular transfer. However, the authors also show efficient transfer of untethered Cas9 protein (Figure 2A and other figures). Does this mean that free protein can diffuse through these tubules? The Cas9 has an NLS so the un-tethered versions should be concentrated in the nucleus of donor cells. How, then, do they transfer? The authors do not provide visual evidence for this and I think it is important they would.

Based on the results using the Cas9-based luciferase assay (His- or SBP-tagged Cas9) (Figure 2A) and split-GFP assay (free GFP1-10) (Figure 2G), we suggest that free protein could be transferred between cells. Our current imaging approach is not designed to quantify protein diffusion. However, we are able to detect from images that Cas9-GFP does not colocalize exclusively with CD63 or concentrate in the nucleus, but also appears in the cytoplasm. These data indicate that both vesicle association and free diffusion may mediate the transfer through tubules. We thank the referee for emphasizing this issue which we will consider for future work to distinguish the transfer types through tubules.

iv) In Figures 6 & 8, where transfer is diminished, there are still red granules in acceptors cells (representing CD63-mcherry). Does this mean that vesicles do transfer, just not those with Cas9-GFP? Is this background of the imaging? The latter case would suggest that the red granule moving from donor to acceptor cells in figure 4 could also be "background". This matter needs to be resolved.

There are a few red puncta in the acceptor cell in Figure 6B. Since the acceptor cell is close to and overlapped with other donor cells containing CD63-mCherry, the red signal may, as the reviewer suggests, be from donor cells and not as a result of transfer through tubular connections. However, donor-acceptor cultures of HEK293T where transfer is not observed, little CD63-mCherry signal, for example, in Figure 6a, was seen in acceptor cells, even during several hours of observation (Figure 6- figure supplement video). A minor red signal could arise from exosomes secreted by donor cells that are internalized by acceptor cells. Images of single-culture receptor cells were added in Figure 4- figure supplement 1.

For Figure 8, we used MDA-MB-231 syncytin-2 knock-down cells containing Fluc:Nluc:mCherry as the receptor cell, thus in these experiments the red signal most likely represents mCherry expressed in the acceptor cells.

In Figure 4, we observed moving punctum in a tubular connection which contained co-localized green, red, and purple signals, corresponding to SBP-Cas9-GFP, streptavidin-CD63-mCherry, and the WGA conjugate, respectively. The video of punctum transport (Figure 4-figure supplement video) suggests that the red signal is not “background”.

5) Why do HEK293T do not transfer to HEK293T?

a) A major inexplicable result is that HEK293T express high levels of both Syncytin proteins (Figure 7 - supp figure 1A) yet ectopic expression of mouse Syncytin increases transfer (Figure 7E). Why would that be? In addition, Fig 3A shows high transfer rates to A549 cells - which express the least amount of Syncytin. The authors suggest in the discussion that Syncytin in HEK293T might not be functional without real evidence.

We cannot yet explain why the basal level of syncytin expressed in HEK293 cells is insufficient to promote open-ended tubular connections between these cells. It could be that the proteins are not well represented in a processed form at the cell surface. Nonetheless, ectopic expression of mouse syncytin-A in HEK293T produced some increased transfer but less than when syncytin-A is ectopically expressed in MDA-MB-231 cells (up to 4-fold vs. 30-fold change of Nluc/Fluc signal) (Figure 7E). Furthermore, we have added new results which show that apparent furin-processed forms of syncytin-A, -1 and -2 can be detected by cell surface biotinylation in transfected MDA-MB-231 cells (Figure 8-figure supplement 1D). All we demonstrate is that syncytin in the acceptor cell is required for fusion and we make no claim that it is the only protein or lipid at the cell surface in the acceptor cell required for fusion. Clearly, more work is essential to establish the complexity of this fusion reaction.

For A549 cells, syncytin-1 is highly expressed in A549 cells, thus it is possible that syncytin-1 in A549 plays crucial roles in the process.

b) In addition - previous publications (e.g. PMID: 35596004; 31735710) show that over expression of syncytin-1 or -2 in HEK293T cells causes massive cell-cell fusion. The authors do not provide images of the cells, to rule out cell-cell fusion in this particular case.

Overexpression of syncytin-1 or -2 in cells indeed causes massive cell-cell fusion, while overexpression of syncytin-A induced much less cell fusion than syncytin-1, or -2. We have now added new images shown in Figure 8-figure supplement 1A-C to document these observations. It may be that overexpressed human syncytins are better represented in a furin-processed form in both cell types. In contrast, we did not observe donor-acceptor cell fusion at basal levels of expression of syncytin in HEK293T and MDA-MB-231. For example, the Figure 4-figure supplement video shows that tubular structures were seen to form and break during the course of visualization with a tubule fusion event but no cell fusion to form heterokaryons.

Reviewer #3 (Public Review):

In this manuscript, Zhang and Schekman investigated the mechanisms underlying intercellular cargo transfer. It has been proposed that cargo transfer between cells could be mediated by exosomes, tunneling nanotubes or thicker tubules. To determine which process is efficient in delivering cargos, the authors developed two quantitative approaches to study cargo transfer between cells. Their reporter assays showed clearly that the transfer of Cas9/gRNA is mediated by cell-cell contact, but not by exosome internalization and fusion. They showed that actin polymerization is required for the intercellular transfer of Cas9/gRNA, the latter of which is observed in the projected membrane tubule connections. The authors visualized the fine structure of the tubular connections by electron microscopy and observed organelles and vesicles in the open-ended tubular structure. The formation of the open-ended tubule connections depends on a plasma membrane fusion process. Moreover, they found that the endogenous trophoblast fusogens, syncytins, are required for the formation of open-ended tubular connections, and that syncytin depletion significantly reduced cargo Cas9 protein transfer.

Overall, this is a very nice study providing much clarity on the modes of intercellular cargo transfer. Using two quantitative approaches, the authors demonstrated convincingly that exosomes do not mediate efficient transfer via endocytosis, but that the open-ended membrane tubular connections are required for efficient cargo transfer. Furthermore, the authors pinpointed syncytins as the plasma membrane fusogenic proteins involved in this process. Experiments were well designed and conducted, and the conclusions are mostly supported by the data. My specific comments are as follows.

1) The authors showed that knocking down actin (which isoform?) in both donor and acceptor cells blocked transfer, and more so in the acceptor cells perhaps due to the greater knockdown efficiency in these cells. However, Arp2/3 complex knockdown in donor cells, but not recipient cell, reduced Cas9 transfer. It would be good to clarify whether the latter result suggests that the recipient cells use other actin nucleators rather than Arp2/3 to promote actin polymerization in the cargo transfer process. Are formins involved in the formation of these tubular connections?

We thank the reviewer for his/her comments and suggestions. Beta-actin was knocked down in this study. We tried a formin inhibitor, SMIFH2 which resulted in a decrease the Cas9 transfer between cells (Figure 3F).

2) The authors provided convincing evidence to show that the tubular connections are involved in cargo transfer. Intriguingly, in Figure 4-figure supplement video (upper right), protein transfer appeared to occur along a broad cell-cell contact region instead of a single tubular connection. How often does the former scenario occur? Is it possible that transfer can happen as long as cells are contacting each other and making protrusions that can fuse with the target cell?

In the Figure 4-figure supplement video (upper right), it may be that several membrane tubes from several different donor cells contact at sites close to one another on the recipient cell resulting in the appearance a broad cell-cell contact. This was a rare observation. In our quantification, only 8 connections were open-ended in 120 cell-cell contact junctions. Once open-ended, or plasma membrane fused, cargo transfer is observed.

3) The requirement of MFSD2A in both donor (HEK293T) and recipient (MDA-MB-231) cells is consistent with a role for syncytin-1 or 2 in both types of cells. Since HEK293T cells contain both syncytins and MFSD2A but cargo transfer does not occur among these cells, does this suggest that syncytins and/or MFSD2A are only trafficked to the HEK293T cell membrane in the presence of MDA-MB-231 cells?

A proper answer to this question requires the visualization of syncytins and MFSD2A. The commercial syncytin antibodies were inadequate for immunofluorescence. In advance of the more detailed effort required to tag the genes for endogenous syncytin 1 and 2, we performed live cell imaging and surface biotin labeling of cells transiently transfected to express fluorescently-tagged forms of syncytin-1, -2 and -A. We now show that syncytin-A, -1, and -2 partially localize to the plasma membrane or the cell surface of MDA-MB-231 and at points of cell-cell contact. In fact, overexpression of codon-optimized human syncytin-1, and -2 induced dramatic HEK293T cell-cell fusion. However, at basal levels of syncytin expression, HEK293T could not form open-ended tubular connections, which may be because the basal level of syncytins are not well represented in a processed form at the cell surface or their activity is limited by unknown factors.

As an independent test of cell surface localization, we used surface biotinylation to show that a fraction of the syncytins can be labeled externally (Figure 8-figure supplement 1D). This fraction shows evidence of proteolytic processing consistent with furin cleavage whereas the overwhelming majority of transfected syncytins detected in a blot of lysates suggests that most remain in the unprocessed precursor form, consistent with the punctate and reticular fluorescence images (Figure 8-figure supplement 1A-C).

We used IF and GFP-tagged MFSD2A and found this protein partially localized to the plasma membrane of HEK293T cells (Figure 9E, F). Given the results reveal that cargos could be transferred among MDA-MB-231 cells (Figure 2G), syncytin and its receptor appear to function in transfer among these cells.

Author Response:

eLife assessment

This is a valuable initial study of cell type and spatially resolved gene expression in and around the locus coeruleus, the primary source of the neuromodulator norepinephrine in the human brain. The data are generated with cutting-edge techniques, and the work lays the foundation for future descriptive and experimental approaches to understand the contribution of the locus coeruleus to healthy brain function and disease. However, due to small sample size and the need for additional confirmatory data, the data only incompletely support the main conclusions presented here. With the strengthening of the analyses, this paper, and the associated web application, will be of great interest to neuroscientists working on arousal-based behaviors and neurological and neuropsychiatric phenotypes.

Thank you for the assessment and comments. Overall, the majority of the issues raised by the reviewers relate either directly or indirectly to limitations of the sample size that precluded further optimization of protocols and expansion of the dataset. We fully acknowledge the limited sample size in this dataset and aim to be transparent about the limitations of the study. This is the first report of snRNA-seq and spatially-resolved transcriptomics in the human locus coeruleus (LC). The LC is a very small nucleus, located deep within the brainstem, which is extremely challenging to study due to its small size, difficult to access location, and the very small number of norepinephrine (NE) neurons located within the nucleus, which were of prime interest for this study. We note that this study represents our initial attempt to molecularly and spatially characterize cell types within the human LC. We note that we did not have significant, established funding from extramural sources dedicated to this study, and tissue resources for the LC are difficult to ascertain, contributing to the small sample size in this initial study. We acknowledge that there are limitations in sample size as well as data quality. Findings from this study will be used to inform, improve, and optimize future and ongoing experimental design, as well as technical and analytical workflows for larger-scale studies. As brought up by one of the reviewers, this field is still in its infancy -- pilot experimentation in new brain regions is labor-intensive and these sequencing approaches remain costly. Moreover, due to the small size and difficulties in dissecting, tissue resources from the human brain in this area are a highly limited resource. Hence, notwithstanding limitations, in our view it is important to release the data for community access at this time. Specific responses to the reviewers’ comments are provided point-by-point in the following sections.

Reviewer #1 (Public Review):

Weber et al. collect locus coeruleus (LC) tissue blocks from 5 neurotypical European men, dissect the dorsal pons around the LC and prepare 2-3 tissue sections from each donor on a slide for 10X spatial transcriptomics. […] The authors transparently present limitations of their work in the discussion, but some points discussed below warrant further attention.

Specific comments:

1) snRNAseq:

a. Major concerns with the snRNAseq dataset are A) the low recovery rate of putative LC-neurons in the snRNAseq dataset, B) the fact that the LC neuron cluster is contaminated with mitochondrial RNA, and C) that a large fraction of the nuclei cannot be assigned to a clear cell type (presumably due to contamination or damaged nuclei). The authors chose to enrich for neurons using NeuN antibody staining and FACS. But it is difficult to assess the efficacy of this enrichment without images of the nuclear suspension obtained before FACS, and of the FACS results. As this field is in its infancy, more detail on preliminary experiments would help the reader to understand why the authors processed the tissue the way they did. It would be nice to know whether omitting the FACS procedure might in fact result in higher relative recovery of LC-neurons, or if the authors tried this and discovered other technical issues that prompted them to use FACS.

Thank you for these comments. We agree these are valid concerns in assessing the data quality and validity of the findings from the snRNA-seq dataset. We will respond to these concerns here to the best of our ability, but in some cases, we do not have definitive answers since comparison data are not yet available for this region. In particular, we were limited in resources for this initial study -- some of the results of the study and issues that we identified in attempting to molecularly profile cells in the human LC were surprising to us, and we intend to generate additional samples and troubleshoot these issues to improve data quality and increase recovery in future work. However, these experiments are (i) expensive, (ii) time- and labor-intensive, and (iii) the tissue for this region is limited and difficult to ascertain. Given the extremely small size of the LC, the tissue resource is quickly depleted. For this study, we had fixed resources and made best-guess decisions on how to proceed with the experimental design, based on our experience with snRNA-seq in other human brain regions (Tran and Maynard et al. 2021). However, the LC is a unique region, and our experiences with this dataset will guide us to make technical adjustments in future studies. Due to the limitations in the tissue resources and the lack of data currently available to the community, we wanted to share these results immediately while acknowledging the limitations of the study as we work to increase our resource availability to expand molecular and spatial profiling studies in this region of the human brain.

Regarding the reviewer’s concern that our choice to use FANS to enrich for neurons could have potentially led to more damage and contributed to the low recovery rate of LC-NE neurons and the mitochondrial contamination -- we do not have a definitive answer to this question, since we did not perform a direct comparison with non-sorted data. As noted above, our limited tissue resource dictated that we could not do both. We made the decision to enrich for neurons based on our previous experience with identifying relatively rare populations in other brain regions (e.g. nucleus accumbens and amygdala; Tran and Maynard et al. 2021). Based on this previous work, our rationale was that without neuronal enrichment, we could potentially miss the LC-NE population, given the relative scarcity of this neuronal population. The low recovery rate and relatively lower quality / contamination issues may be due to technical issues that lead to LC-NE neurons being more susceptible to damage during nuclear preparation and sorting. We agree that directly comparing to data prepared without NeuN labeling and sorting is reasonable, as the additional perturbations may indeed contribute to cell damage. As mentioned in the discussion, we do not have a definitive answer to the reasons for increased mitochondrial contamination and we suspect that multiple technical factors may contribute -- including the relatively large size and increased fragility of LC-NE neurons. We agree that systematically optimizing the preparation to attempt to increase recovery rate and decrease mitochondrial contamination are important avenues for future work.

b. It is unclear what percentage of cells that make up each cluster.

We will add this information in the clustering heatmaps or as a supplementary plot in a revised version of the manuscript.

c. The number of subjects used in each analysis was not always clear. Only 3 subjects were used for snRNAseq, and one of them only yielded 4 LC-nuclei. This means the results are essentially based on n=2. The authors report these numbers in the corresponding section, but the first sentence of the results section (and Figure 1C specifically!) create the impression that n=5 for all analyses. Even for spatial transcriptomics, if I understood it correctly, 1 sample had to be excluded (n=4).

This is correct. We will update the figures and text in a revised version of the manuscript to make this limitation (small sample size) more clear, and to further emphasize that the intention of this study is to provide initial data to help determine next steps and best practices for a larger scale and more comprehensive study on this region, especially given the limited availability of tissue resources and currently limited data resources available for this region.

2) Spatial transcriptomics:

a. It is not clear to me what the spatial transcriptomics provides beyond what can be shown with snRNAseq, nor how these two sets of results compare to each other. It would be more intuitive to start the story with snRNAseq and then try to provide spatial detail using spatial transcriptomics. The LC is not a homogeneous structure but can be divided into ensembles based on projection specificity. Spatial transcriptomics could - in theory - offer much-needed insights into the spatial variation of mRNA profiles across different ensembles, or as a first step across the spatial (rostral/caudal, ventral/dorsal) extent of the LC. The current analyses, however, cannot address this issue, as the orientation of the LC cannot be deduced from the slices analyzed.

We understand the point of the reviewer. However, we structured the manuscript in this format due to our aims of creating a data resource for the community as well as being transparent about the limitations of our study. Our experiments began with the spatial experiments on the tissue blocks because this (i) helped orient ourselves to the region, and (ii) provided guidance for how best to score the tissue blocks for the snRNA-seq experiments to maximize recovery of LC-NE neurons. Therefore, we also decided to present the results in this sequence.

The spatial data also provides more information in that the measurements are from nuclei, cytoplasm, and cell processes (instead of nuclei only). This is one of the main differences / advantages between the platforms at this level of spatial resolution. As noted above, we were also working with a finite tissue resource -- if we ran snRNA-seq first and captured no neurons, the tissue block would be depleted. Due to the logistics / thickness of the required tissue sections for Visium and snRNA-seq respectively, running Visium first allowed us to ensure that we could collect data from both assays.

Regarding a point raised below on why we only ran snRNA-seq on a subset of the donors -- this was due to resource depletion and not enough available tissue remaining on the tissue blocks to run the assay. We have conducted extensive piloting in other brain regions on the amount (mg) of tissue that is needed from various sized cryosections, and the LC is particularly difficult since these are small tissue blocks and the extent of the structure is small. Hence, in some of the subjects, we did not have sufficient tissue available for the snRNA-seq assay.

We agree with the reviewer that spatial studies could, in future work, offer needed and important information about expression profiles across the spatial axes (rostral/caudal, ventral/dorsal) of the LC. Our study provides us with insight about optimizing the dissections for spatial assays, as well as bringing to light a number of technical and logistical issues that we had not initially foreseen. For example, during the course of this study and parallel, ongoing work in other small, challenging brain regions, we have now developed a number of specialized technical and logistical strategies for keeping track of orientation and mounting serial sections from the same tissue block onto a single spatial array, which is extremely technically challenging. We are now well-prepared for addressing these issues in future studies with larger numbers of donors and samples, e.g. spaced serial sections across the extent of the LC to make these types of insights. Due to the rarity of the tissue, limited availability of information in this region, and high expense of conducting these studies, we want to share this initial data with the community immediately. We also note that in addition to the 10x Genomics Visium platform, which lacks cellular and sub-cellular resolution, many new and exciting spatial platforms are entering the market, which may be able to address questions in very small regions such as the LC at higher spatial resolution.

b. Unfortunately, spatial transcriptomics itself is plagued by sampling variability to a point where the RNAscope analyses the authors performed prove more powerful in addressing direct questions about gene expression patterns. Given that the authors compare their results to published datasets from rodent studies, it is surprising that a direct comparison of genes identified with spatial transcriptomics vs snRNAseq is lacking (unless this reviewer missed this comparison). Supplementary Figure 17 seems to be a first step in that direction, but this is not a gene-by-gene comparison of which analysis identifies which LC-enriched genes. Such an analysis should not compare numbers of enriched genes using artificial cutoffs for significance/fold-change, but rather use correlations to get a feeling for which genes appear to be enriched in the LC using both methods. This would result in one list of genes that can serve as a reference point for future work.

We agree this is a good suggestion, and will add additional computational analyses to address this point in a revised version of the manuscript.

c. Maybe the spatial transcriptomics could be useful to look at the peri-LC region, which has generated some excitement in rodent work recently, but remains largely unexplored in humans.

We agree this is an excellent suggestion -- assessing cross-species comparisons related to convergence, especially, of GABAergic cell populations in the human LC is of high interest. We note that these types of extensions are exactly the reason why we have provided the publicly accessible web app (R/Shiny app, which includes the ability to annotate regions). We hope that others will use these apps for specialized topics they are interested in. As discussed above, we note that our initial dissections precluded the ability to keep track of the exact orientation of our tissue sections on the Visium arrays with respect to their location within the brainstem, so definitive localization of this region across subjects is difficult in our current study. However, it is possible, for example, to investigate whether there is a putative peri-LC region that is densely GABAergic that is homologous with the GABAergic peri-LC region in rodents. We also raise attention to a recent preprint by Luskin and Li et al. (2022), who apply snRNA-seq and spatially-resolved transcriptomics to molecularly define both LC and peri-LC cell types in mice -- in a revised version of our manuscript, we will extend our computational analyses of inhibitory neuronal subtypes in our data (Supplementary Figures 13, 16) to directly compare with those identified in this study in more detail. As noted above, we we have now developed a number of specialized technical and logistical strategies for keeping track of orientation of sections from the tissue block onto a single spatial array, and we feel that combined with optimized dissection strategies for this region and the guide of RNAscope for GABAergic markers on serial sections, that annotating the peri-LC region on spatial arrays in future studies will be possible.

3) The comparison of snRNAseq data to published literature is laudable. Although the authors mention considerable methodological differences between the chosen rodent work and their own analyses, this needs to be further explained. The mouse dataset uses TRAPseq, which looks at translating mRNAs associated with ribosomes, very different from the nuclear RNA pool analyzed in the current work. The rat dataset used single-cell LC laser microdissection followed by microarray analyses, leading to major technical differences in terms of tissue processing and downstream analyses. The authors mention and reference a recent 10x mouse LC dataset (Luskin et al, 2022), however they only pick some neuropeptides from this study for their analysis of interneuron subtypes (Figure S13). Although this is a very interesting part of the manuscript, a more in-depth analysis of these two datasets would be very useful. It would likely allow for a better comparison between mouse and human, given that the technical approach is more similar (albeit without FACS), and Luskin et al have indicated that they are willing to share their data.

As noted above, we plan to extend our comparisons with the dataset from Luskin and Li et al. (2022) in a revised version of the manuscript, which will provide a more in-depth cross-species comparison. In addition, we also note that there are some additional recent studies using TRAPseq of LC-NE neurons in a functional context, i.e. treatment vs. control experiments or in model systems (e.g. Iannitelli et al. 2023), which provide new opportunities for understanding disease context using in-depth cross-species comparisons. By providing our dataset and reproducible code, we will enable others to adapt and extend these types of comparisons (i.e. TRAPseq of LC-NE neurons or LC snRNA-seq following functional manipulations or in the context of disease or behavioral models) in the future.

4) Statements in the manuscript about the unexpected identification of a 5-HT (serotonin) cell-cluster seem somewhat contradictory. Figure S14 suggests that 5-HT markers are expressed in the LC-regions just as much as anywhere else, but the RNAscope image in Figure S15 suggests spatial separation between these two populations. And Figure S17 again suggests almost perfect overlap between the LC and 5HT clusters. Maybe I misunderstood, in which case the authors should better clarify/explain these results.

In our view, the most likely scenario is that the 5-HT neurons come from contamination from the dorsal raphe nucleus based on spatial separation from the RNAscope images, which we agree are more definitive. As mentioned above, since we do not have definitive documentation for the tissue sections in terms of orientation, it is difficult to say with clarity that the regions are the dorsal raphe and which sub-portion of the dorsal raphe they are. This initial study has now allowed us to optimize and improve our dissection strategy and approaches for retaining documentation of the orientation of the tissue sections from their intact position within the brainstem as they move from cryosection to placement on the array, which will enable us to better annotate regions with definitive anatomical information with respect to the rostral/caudal and dorsal/ventral axes in future experiments. Given that there are reports in the rodent that 5-HT markers have been identified in LC-NE neurons (Iijima 1993; Iijima 1989), and taking into account the technical limitations in our study, we felt that it was premature to definitively conclude in the manuscript that we were sure these signals arose from the dorsal raphe. We will update this language in a revised version of the manuscript to ensure that these limitations are clear (referring to Supplementary Figures S14-15, S17).

Reviewer #2 (Public Review):

The data generated for this paper provides an important resource for the neuroscience community. The locus coeruleus (LC) is the known seed of noradrenergic cells in the brain. Due to its location and size, it remains scarcely profiled in humans. Despite the physically minute structure containing these cells, its impact is wide-reaching due to the known neuromodulatory function of norepinephrine (NE) in processes like attention and mood. As such, profiling NE cells has important implications for most neurological and neuropsychiatric disorders. This paper generates transcriptomic profiles that are not only cell-specific but which also maintain their spatial context, providing the field with a map for the cells within the region.

Strengths:

Using spatial transcriptomics in a morphologically distinct region is a very attractive way to generate a map. Overlaying macroscopic information, i.e. a region with greater pigmentation, with its corresponding molecular profile in an unbiased manner is an extremely powerful way to understand the specific cellular and molecular composition of that brain structure.

The technologies were used with an astute awareness of their limitations, as such, multiple technologies were leveraged to paint a more complete and resolved picture of the cellular composition of the region. For example, the lack of resolution in the spatial transcriptomic platform was compensated by complementary snRNA-seq and single molecule FISH.

This work has been made publicly available and accessible through a user-friendly application such that any interested researcher can investigate the level of expression of their gene of interest within this region.

Two important implications from this work are 1) the potential that the gene regulatory profiles of these cells are only partially conserved across species, humans, and rodents, and 2) that there may be other neuromodulatory cell types within the region that were otherwise not previously localized to the LC

Weaknesses:

Given that the markers used to identify cells are not as specific as they need to be to definitively qualify the desired cell type, the results may be over-interpreted. Specifically, TH is the primary marker used to qualify cells as noradrenergic, however, TH catalyzes the synthesis of L-DOPA, a precursor to dopamine, which in turn is a precursor for epinephrine and norepinephrine suggesting some of the cells in the region may be dopaminergic and not NE cells. Indeed, there are publications to support the presence of dopaminergic cells in the LC (see Kempadoo et al. 2016, Takeuchi et al., 2016, Devoto et al. 2005). This discrepancy is further highlighted by the apparent lack of overlap per given Visium spots with TH, SCL6A2, or DBH. While the single-nucleus FISH confirms that some of the cells in the region are noradrenergic, others very possibly represent a different catecholamine. As such it is suggested that the nomenclature for the cells be reconsidered.

We appreciate the reviewer’s comment, and are aware of the reports suggesting the potential presence of dopaminergic cells in the LC. We initially had the same thought as the reviewer when we observed Visium spots in the spatial data with lack of overlap between TH, SLC6A2, and DBH as well as single nuclei in the snRNA-seq data with lack of overlap between TH, SLC6A2, and DBH. This surprising result was exactly why we performed the smFISH/RNAscope experiment with these three marker genes. Given known issues with read depth and coverage in the 10x Genomics assays, we wanted to better understand if this was a technical limitation in the sequencing coverage, or rather a true biological finding. The RNAscope data showed very clearly that nearly every cell body we looked at had co-localization of these three marker genes. We included an image from a single capture array of one tissue section in Supplementary Figure 11, but could, in a revised version of the manuscript, provide additional examples to illustrate how conclusive the images were by visualization. As such, we were quite convinced that the lack of overlap on Visium spots and in single nuclei in the snRNA-seq data was more likely related to technical issues with sequencing coverage, rather than a biological finding. We also note that we checked for the presence of the dopamine transporter, SLC6A3, and as can be appreciated in the iSEE web app for the snRNA-seq data or the R/Shiny web app for the Visium data, there is virtually no expression of SLC6A3 in the dataset, which in our view provides additional evidence against the possibility that there are substantial quantities of dopaminergic cells in this human LC dataset. We will include supplementary plots showing the lack of SLC6A3 expression in a revised version of the manuscript.

The authors are unable to successfully implement unsupervised clustering with the spatial data, this greatly reduces the impact of the spatial technology as it implies that the transcriptomic data generated in the study did not have enough resolution to identify individual cell types.

The reviewer is correct -- this is a fundamental limitation of the 10x Genomics Visium platform, i.e. the spatial resolution captures multiple cells per spot (e.g. around 1-10 cells per spot in human brain tissue). We note that new spatial platforms now provide cellular resolution (e.g. Vizgen MERSCOPE, 10x Genomics Xenium, 10x Genomics Visium HD), which will help address this in future work. However, many of these cellular-resolution in situ sequencing platforms have the limitation that they do not quantify genome-wide expression, and instead require users to select a priori gene panels to investigate. This is a problem if no genome-wide reference datasets are available. Hence, despite the limited spatial resolution of the Visium platform, this dataset is useful precisely for helping investigators choose gene panels for higher-resolution platforms or higher-order smFISH multiplexing.

We also applied spatial clustering (using BayesSpace; Zhao et al. 2021) to attempt to segment the LC regions within the Visium samples in a data-driven manner as an alternative to the manual annotations, which was unsuccessful (and hence we relied on the manually annotated regions for downstream analyses) (Supplementary Figure S5). However, this is a different application of unsupervised clustering, which is separate from the task of identifying cell types.

The sample contribution to the results is highly unbalanced, which consequently, may result in ungeneralizable findings in terms of regional cellular composition, limiting the usefulness of the publicly available data.

We acknowledge the limitations of the work due to the small/unbalanced sample sizes. As mentioned above for Reviewer 1, this was an initial study in this region -- results of which will inform our (and hopefully others’) experimental design and approach to molecular profiling in this difficult to access brain region. Overall, this study was executed with finite tissue and financial resources and was intended to uncover limitations and help develop best practices and design workflows for future studies with larger numbers of donors and samples. Given the limited data availability for this brain region, we wanted to make this dataset available for the research community immediately. In addition, we note that making this genome-wide dataset available will help inform targeted gene panel design for higher-resolution platforms (e.g. 10x Genomics Xenium).

This study aimed to deeply profile the LC in humans and provide a resource to the community. The combination of data types (snRNA-seq, SRT, smFISH) does in fact represent this resource for the community. However, due to the limitations, of which, some were described in the manuscript, we should be cautious in the use of the data for secondary analysis. For example, some of the cellular annotations may lack precision, the cellular composition also may not reflect the general population, and the presence of unexpected cell types may represent the accidental inclusion of adjacent regions, in this case, serotonergic cells from the Raphe nucleus.

We agree, and have attempted to explain these limitations in the manuscript. We will clarify the language regarding the interpretation of the annotated cell populations and unexpected cell types, and the limited sample sizes, in a revised version of the manuscript.

Nonetheless having a well-developed app to query and visualize these data will be an enormous asset to the community especially given the lack of information regarding the region in general.

Reviewer #3 (Public Review):

[…] This study has many strengths. It is the first reported comprehensive map of the human LC transcriptome, and uses two independent but complementary approaches (spatial transcriptomics and snRNA-seq). Some of the key findings confirmed what has been described in the rodent LC, as well as some intriguing potential genes and modules identified that may be unique to humans and have the potential to explain LC-related disease states. The main limitations of the study were acknowledged by the authors and include the spatial resolution probably not being at the single cell level and the relatively small number of samples (and questionable quality) for the snRNA-seq data. Overall, the strengths greatly outweigh the limitations. This dataset will be a valuable resource for the neuroscience community, both in terms of methodology development and results that will no doubt enable important comparisons and follow-up studies.

Major comments:

Overall, the discovery of some cells in the LC region that express serotonergic markers is intriguing. However, no evidence is presented that these neurons actually produce 5-HT.

The reviewer is correct that we did not provide any additional evidence to show that these neurons actually produce 5-HT. As noted above in the response to Reviewer 1, in our view, the most likely explanation is that these neurons are from dorsal raphe contamination on the tissue section. However, due to technical and logistical limitations in this study, we could not definitively say this because we did not clearly track the orientation of the tissue sections, and we did not have remaining tissue sections from all donor tissue blocks to repeat RNAscope experiments. For some of the donors, where we had remaining tissue sections to go back to repeat RNAscope experiments after completion of the snRNA-seq and Visium assays, we could see clear separation of the LC region / LC-NE neuron core from where putative 5-HT neurons were located (Supplementary Figure 15). However, we did not have sufficient tissue resources to map this definitively in all donors, and the orientation and anatomy of each tissue block were not fully annotated.

Due to the lack of clarity, and the fact that there have been reports that LC-NE neurons express serotonergic markers (Iijima 1993; Iijima 1989), we felt that it was premature to definitively declare that these putative 5-HT neurons that we identified were definitively from the raphe. We will clarify the language around this discrepancy in a revised version of the manuscript to ensure that these limitations are clearly described.

Concerning the snRNA-seq experiments, it is unclear why only 3 of the 5 donors were used, particularly given the low number of LC-NE nuclear transcriptomes obtained, why those 3 were chosen, and how many 100 um sections were used from each donor. It is also unclear if the 295 nuclei obtained truly representative of the LC population or whether they are just the most "resilient" LC nuclei that survive the process.

As discussed above for Reviewer 1, the reason we included only 3 of the 5 donors for the snRNA-seq assays was due to the tissue availability on the tissue blocks. We will clarify the language in a revised version of the manuscript to make this limitation more clear. We will also include additional details in the Methods section on the number of 100 μm sections used for each donor (which varied between 10-15, approximating 60-80 mg of tissue).

The LC displays rostral/caudal and dorsal/ventral differences, including where they project, which functions they regulate, and which parts are vulnerable in neurodegenerative disease (e.g. Loughlin et al., Neuroscience 18:291-306, 1986; Dahl et al., Nat Hum Behav 3:1203-14, 2019; Beardmore et al., J Alzheimer's Dis 83:5-22, 2021; Gilvesy et al., Acta Neuropathol 144:651-76, 2022; Madelung et al., Mov Disord 37:479-89, 2022). It was not clear which part(s) of the LC was captured for the SRT and snRNAseq experiments.

As discussed above for Reviewer 1, a limitation of this study was that we did not record the orientation of the anatomy of the tissue sections, precluding our ability to annotate the tissue sections with the rostral/caudal and dorsal/ventral axis labels. We agree with the reviewer that additional spatial studies, in future work, could offer needed and important information about expression profiles across the spatial axes (rostral/caudal, ventral/dorsal) of the LC. Our study provides us with insight about optimizing the dissections for spatial assays, as well as bringing to light a number of technical and logistical issues that we had not initially foreseen. For example, during the course of this study and parallel, ongoing work in other, small, challenging regions, we have now developed a number of specialized technical and logistical strategies for keeping track of orientation and mounting serial sections from the same tissue block onto a single spatial array, which is extremely technically challenging. We are now well-prepared for addressing these issues in future studies with larger numbers of donors and samples in order to make these types of insights.

The authors mention that in other human SRT studies, there are typically between 1-10 cells per expression spot. I imagine that this depends heavily on the part of the brain being studied and neuronal density, but it was unclear how many LC cells were contained in each expression spot.

The reviewer is correct that we did not include this information in the manuscript. We attempted to apply a computational method to count nuclei contained in each gene expression spot based on analyzing the histological H&E images (VistoSeg; Tippani et al. 2022), which we have developed and previously applied in data from the dorsolateral prefrontal cortex (DLPFC) (Maynard and Collado-Torres et al. 2021). Based on the segmentation using this workflow we observe that the counts in this region are similar to what we observed in the DLPFC, i.e., typically between 1-10 LC cells per expression spot, with approximately 1-2 LC-NE neurons (which are characterized by their large size) per expression spot. However, these analyses had several technical issues related to the images themselves, the relatively large size and pigmentation of LC-NE neurons, and parameter settings that had been optimized for different brain regions. We are currently optimizing this analysis workflow for these images to provide more accurate estimates of cell counts per spot to give readers additional context on the number of nuclei per spot in the annotated LC regions and outside the LC regions in a revised version of the manuscript.

Regarding comparison of human LC-associated genes with rat or mouse LC-associated genes (Fig. 2D-F), the authors speculate that the modest degree of overlap may be due to species differences between rodents and human and/or methodological differences (SRT vs microarray vs TRAP). Was there greater overlap between mouse and rat than between mouse/rat and human? If so, that is evidence for the former. If not, that is evidence for the latter. Also would be useful for more in-depth comparison with snRNA-seq data from mouse LC: https://www.biorxiv.org/content/10.1101/2022.06.30.498327v1.

We will investigate this question and discuss this in updated results in a revised version of the manuscript.

The finding of ACHE expression in LC neurons is intriguing, especially in light of work from Susan Greenfield suggesting that ACHE has functions independent of ACH metabolism that contributes to cellular vulnerability in neurodegenerative disease.

We thank the reviewer for pointing this out. We were very surprised too by the observed expression of SLC5A7 and ACHE in the LC regions (Visium data) and within the LC-NE neuron cluster (snRNA-seq data), coupled with absence of other typical cholinergic marker genes (e.g. CHAT, SLC18A3), and we do not have a compelling explanation or theory for this. Hence, the work of Susan Greenfield and colleagues suggesting non-cholinergic actions of ACHE, particularly in other catecholaminergic neurons (e.g. dopaminergic neurons in the substantia nigra) is very interesting. We will include references to this work and how it could inform interpretation of this expression in a revised version of the manuscript (Greenfield 1991; Halliday and Greenfield 2012).

High mitochondrial reads from snRNA-seq can indicate lower quality. It was not clear why, given the mitochondrial read count, the authors are confident in the snRNA-seq data from presumptive LC-NE neurons.

We will include additional analyses to further investigate and/or confirm this finding (e.g. comparing sum of UMI counts / number of detected genes and mitochondrial percentage per nucleus for this population to confirm data quality) in additional supplementary figures in a revised version of the manuscript.

References

• Greenfield (1991), A noncholinergic action of acetylcholinesterase (AChE) in the brain: from neuronal secretion to the generation of movement, Cellular and Molecular Neurobiology, 11, 1, 55-77.

• Halliday and Greenfield (2012), From protein to peptides: a spectrum of non-hydrolytic functions of acetylcholinesterase, Protein & Peptide Letters, 19, 2, 165-172.

• Iannitelli et al. (2023), The neurotoxin DSP-4 dysregulates the locus coeruleus-norepinephrine system and recapitulates molecular and behavioral aspects of prodromal neurodegenerative disease, eNeuro, 10, 1, ENEURO.0483-22.2022.

• Iijima K. (1989), An immunocytochemical study on the GABA-ergic and serotonin-ergic neurons in rat locus ceruleus with special reference to possible existence of the masked indoleamine cells. Acta Histochema, 87, 1, 43-57.

• Iijima K. (1993), Chemocytoarchitecture of the rat locus ceruleus, Histology and Histopathology, 8, 3, 581-591.

• Luskin A.T., Li L. et al. (2022), A diverse network of pericoerulear neurons control arousal states, bioRxiv (preprint).

• Maynard and Collado-Torres et al. (2021), Transcriptome-scale spatial gene expression in the human dorsolateral prefrontal cortex, Nature Neuroscience, 24, 425-436.

• Tippani et al. (2022), VistoSeg: processing utilities for high-resolution Visium/Visium-IF images for spatial transcriptomics data, bioRxiv (preprint).

• Tran M.N., Maynard K.R. et al. (2021), Single-nucleus transcriptome analysis reveals cell-type-specific molecular signatures across reward circuitry in the human brain, Neuron, 109, 3088-3103.

• Zhao E. et al. (2021), Spatial transcriptomics at subspot resolution with BayesSpace, Nature Biotechnology, 39, 1375-1384.

Author Response

Reviewer #1 (Public Review):

1) The authors show that there are several classes of Snf1 targets (Fig. 3e), most notably some that are phosphorylated immediately after Snf1 activation by glucose (<5 min) and others that are only phosphorylated after 15 min. In a simple view, all direct Snf1 targets should be phosphorylated immediately after Snf1 activation. Is that the case? What is the overlap between the direct targets found using the OBIKA assay and the slow and fast responding in vivo targets? What about the phosphorylation motif, does it differ between the groups? These points are not discussed in the text except to point out that the direct Snf1 target Msn4 is among the slowly phosphorylated group.

This is a very good point and we have performed the suggested analysis, which resulted in an interesting finding that we describe now in the text as follows:

“Notably, of the 145 confirmed target sites, 81 (i.e. 72%) were significantly regulated after both 5 min and 15 min. Of the remaining 64 sites, 32 responded only after 5 min, while the other 32 responded only after 15 min. Some of the former residues are located within Snf1 itself, the -subunit of the Snf1 complex (i.e. Sip1), the Snf1-targeting kinase Sak1, or Mig1, while some of the latter are located within the known Snf1-interacting proteins such as Gln3, Msn4, and Reg1. These observations indicate that Snf1-dependent phosphorylation initiates, as expected, within the Snf1 complex and then progresses to other effectors. Interestingly, based on the residues that responded exclusively after 5 min, we retrieved a perfect Snf1 consensus motif (i.e. an arginine residue in the -3 position and a leucine residue in the +4 position; Supplementary figure 2A). The one retrieved for the residues that respond exclusively at 15 min, in contrast, significantly deviated from this consensus motif (Supplementary figure 2B). The slight temporal deferral of Snf1 target phosphorylation may therefore perhaps in part be explained by reduced substrate affinity due to consensus motif divergence.”

2) The data showing that Snf1-dependent phosphorylation of Pib2 plays a key role in triggering inhibition of TORC1 is convincing but is entirely dependent on a rescue of the TORC1 inhibition defect seen in cells where Snf1 is inhibited. That is, TORC1 is normally inactivated during glucose starvation; this does not occur when Snf1 is inhibited by 2nm-pp1 but does occur when Snf1 is inhibited in a strain carrying a phosphomimetic version of Pib2 (Pib2SESE). This indicates that Pib2 phosphorylation is sufficient to replace Snf1 signaling and inhibit TORC1 during glucose starvation. However, in a simple model, a phosphodead version of Pib2 (SASA) should have the opposite effect. That is TORC1 should remain active during glucose starvation in the Pib2SASA strain-but that is not the case (Fig. 4g). This point is not discussed in the paper; why do the authors think that TORC1 is inhibited normally in the SASA mutant inhibits TORC1 normally?

We fully agree with this statement and have highlighted and discussed this issue now in the last paragraph of the results section (where we think this fits best) as follows:

“In contrast, the separated and combined expression of Sch9S288A and Pib2S268A,S309A showed, as predicted, no significant effect in the same experiment. Unexpectedly, however, the latter combination did not result in transient reactivation of TORC1, like we observed in glucose-starved, Snf1-compromised cells. This may be explained if TORC1 reactivation would rely on specific biophysical properties of the non-phosphorylated serines within Sch9 and Pib2 that may not be mimicked by respective serine-to-alanine substitutions. Alternatively, Snf1 may employ additional parallel mechanisms (perhaps through phosphorylation of Tco89, Kog1, and/or other factors; see above) to prevent TORC1 reactivation even when Pib2 and Sch9 cannot be appropriately phosphorylated. While such models warrant future studies, our current data still suggest that Snf1-mediated phosphorylation of Pib2 and Sch9 may be both additive and together sufficient to appropriately maintain TORC1 inactive in glucose-starved cells”

Reviewer #2 (Public Review):

1) Because PIB2 is a major focus of the manuscript, I was surprised that it was not discussed in the introduction. I think it would be appropriate to discuss prior evidence linking this protein to TORC1.

We thank the reviewer for this suggestion. Pib2 and its role in TORC1 control is now described in the introduction.

2) The authors introduce mutations into PIB2 at two sites determined to be phosphorylated by SNF1, at S268 and S309. Somewhat confusing results are obtained, in that the PIB2 null and phosphomimic mutants (S268E and S309E) confer a similar TORC1 phenotype, compared to the S268A S308A mutant. These results require further explanation than simply that "TORC1 inactivation defect in SNF1-compromised cells is due to a defect in PIB1 phosphorylation". This is particularly intriguing given that the opposite results are observed with the SCH9 mutants, where the null and alanine mutants confer a similar phenotype compared to the S to E mutants.

The finding that both loss of Pib2 and expression of the phosphomimetic allele yield the same phenotype is indeed counterintuitive. Hence, we fully agree with the criticism put forward here. We believe that the underlying reason for our observation is based on the unique property of Pib2 in having both a C-terminal TORC1-activating domain (CAD) and an-N-terminal TORC1-inhibitory domain (NID). We have addressed this point briefly in the discussion ("Our current data favor a model according to which Snf1-mediated phosphorylation of the Kog1-binding domain in Pib2 weakens its affinity to Kog1 and thereby reduces the TORC1-activating influence of Pib2 that is mediated by the C-terminal TORC1-activating (CAD) domain via a mechanism that is still largely elusive"), but now also address this issue in the results section as suggested.

3) The authors conclude, based on the co-IP data in Figure 4H, that interactions between KOG1 and PIB2 are direct. However, it remains possible that interactions between these proteins are mediated by other components of TORC1 or within cells. This should be addressed.

Please note that the Kog1-Pib2 interaction has previously been demonstrated by different methods. Accordingly, Pib2 has not only been shown to interact with Kog1 (or TORC1) in co-IP studies in vivo (PMID: 30485160, PMID: 29698392), but also by co-IP studies in vitro (PMID: 29698392, PMID: 28483912, PMID: 34535752). In addition, the interaction between Kog1-Pib2 has also been dissected (down to defined domains) by classical two hybrid analyses (PMID: 28481201). All of these studies are cited now in the introduction where Pib2 is discussed.

4) The authors demonstrate convincingly that the PIB2 and SCH9 SNF1-specific phospho-site mutants have a detectable effect on TORC1, primarily by examining TORC1-dependent phosphorylation of SCH9. What is unclear is whether phosphorylation at these sites has a significant physiological impact on cells. It appears that the rapamycin hyper-sensitivity displayed in Figure 6E is the only data presented to address this question. It would be appropriate for the authors to comment further on the significance of SNF1-dependent phosphorylation of these two substrates.

To further address the physiological role of the Snf1-dependent phosphorylation of Sch9 and Pib2 combined, we newly assessed the growth rate of the strain that expresses the Sch9SE and Pib2SESE alleles combined. Accordingly, we found the snf1as pib2SESE sch9SE strain to exhibit a significantly higher doubling time than the snf1as strain on both low-nitrogen-containing media and standard synthetic complete media. This is now included in the text (results section).

Reviewer #3 (Public Review):

1) Conceptually, the manuscript shows that Snf1 activity is important for the acute inhibition of TORC1 during glucose starvation. However, this is mainly restricted to 10 and 15 minutes of glucose starvation. After 20 minutes, TORC1 is inhibited by some unknown mechanisms independent of Snf1 (Hughes Hallet et al). This raises concern regarding the physiological relevance of Snf1-mediated TORC1 inhibition during acute glucose stress. The authors show that this regulation is important for the survival of cells under TORC1 inhibition. How do the authors envision that the acute role of Snf1 plays an important long-term physiological relevance during rapamycin treatment? Providing more support for the physiological relevance of this regulation will make this study of interest to a broad readership.

Please see our response to point 4 of reviewer #2.

2) Another major concern of the manuscript is the inconsistencies between the various representative immunoblots and their quantifications. The effect of AMPK activity on TORC1 signaling under glucose starvation seems very subtle. A few specific concerns are mentioned below:

a) In figure 1A, the increase in TORC1 activity upon inhibition of analogue sensitive Snf1as by 2NM-PP1 is very marginal. Although quantification shows a significant increase, a representative western blot figure should be shown.

We have replaced the original immunoblots with more representative ones in Figure 1A.

b) Does deleting Snf1 itself have any effect on TORC1 activity? Lane 4 of figure 1A shows reduced activity compared to lane 1.

TORC1 activity is generally assessed as the ratio between phosphorylated Sch9 and total Sch9 (see also below under (e)). Accordingly, based on the quantification of 6 blots (we added two more experiments to address this point; Figure 1B), loss of Snf1 has no significant impact on TORC1 activity in exponentially growing cells, as we expected.

c) To show the effect of Snf1 on the repression of TORC1, the time-course experiments are run on two separate gels in figure 1C. Hence, it is difficult to compare the effect of Snf1 on unscheduled reactivation of TORC1 under glucose starvation.

Please note that the data of the two blots were cross-normalized to the sample from exponentially growing cells (labeled “Exp”; i.e. the same sample was loaded on the two blots) in order to compare and quantify the effects of Snf1.

d) In figure 1E, the effect of Reg1 deletion on TORC1 activity seems minor as both phospho- and total levels of Sch9 are reduced.

As correctly pointed out by this reviewer, we consistently found the total Sch9 levels to be lower in reg1Δ cells when compared to wild-type cells. To assess TORC1 activity, we therefore always determine the ratio between phosphorylated Sch9 and total Sch9, and the respective ratio is significantly different in reg1∆ cells when compared to wild-type cells. We speculate that the reduced Sch9 levels in this mutant are caused by the reduced growth rate (PMID: 22140226) and hence lower protein synthesis rate (to which translation of SCH9 mRNA may be specifically sensitive).

Since further mechanistic insights are based on these initial findings of figure 1, solidifying these observations is very important.

3) In figure S1, the analogue sensitive Snf1as shows significant reduction in its activity (reduced S79 phosphorylation of ACC1-GFP). This raises the concern of whether this genetic background is an ideal system to resolve the mechanism of TORC1 suppression.

The Snf1as allele is indeed hypomorphic, which we acknowledge appropriately in the text. We would like to point out however, that we took great care in each experiment to include the DMSO control that allowed us to unequivocally assign any observed effects to the specific drug-mediated inhibition of Snf1as. Importantly, we think that the hypomorphic nature of the Snf1as allele (which allows normal growth on non-fermentable carbon sources) represents a minor trade-off when compared to the advantages that this allele provides over the use of a snf1∆ strain, which exhibits a fundamentally reprogrammed transcriptome/proteome (PMID: 17981722). Accordingly, this allele allows the assessment of Snf1 inhibition on very short time scales while minimizing confounding large-scale proteome rearrangements that may indirectly affect the studies. Moreover, use of the Snf1as allele also allowed us to compare our results more directly with other phosphoproteome studies that used the same allele (PMID: 25005228, PMID: 28265048). Finally, please also note that our main conclusions (on Snf1-mediated control of TORC1) are corroborated by additional genetic data such as the ones in Figure 1A/E where we use snf1∆ and reg1∆ cells.

4) In figure 2, during glucose restimulation, there is increased retention of Snf1as-pThr210 in the presence of 2NM-PP1. This suggests that the upstream glucose sensing pathway as well as Snf1 might be more active than in DMSO-treated cells. This also raises concerns regarding the suitability of the genetic background for the study. Can authors comment on why this phosphorylation persists? Does the phosphoproteomic analysis give any hint for this phenotype?

This is a very good point. In fact, we forgot to mention in the text that the observed effect of the 2NM-PP1 treatment on Snf1-Thr210 phosphorylation has already been studied and mechanistically explained earlier (PMID: 23184934). Accordingly, the entry of the drug into the broader catalytic cleft of the Snf1as mutant causes the catalytic domain to be stabilized in a conformation, which prevents dephosphorylation of pThr210 by the dedicated Glc7-Reg1 phosphatase heterodimer. This can be observed each time when we compared 2NM-PP1- and DMSO-treated cells and probed for Snf1-Thr210 phosphorylation. This is, in fact, an independent control for proper 2NM-PP1 functioning. We have now added a sentence (including reference) that pinpoints this issue in the text.

5) In figure 4H, where authors claim reduced binding of Kog1 to Pib2SESE, levels of Kog1 in input are also reduced. Can authors provide further support using colocalization studies? Also, does Pib2SESE has any defect in forming Kog1 bodies?

We took great care to load equal amounts of IPed Pib2-myc variants and then normalized the co-IPed Kog1-HA on the IPed Pib2-myc variant levels. The Kog1-HA input levels vary a bit between the 4 experiments, but they are on average not significantly lower in Pib2SESE-myc-expressing cells when compared to WT cells. In addition, in our Co-IP experiments, the beads are saturated with Pib2-myc variants and Kog1-HA levels are generally not limiting. We therefore deem it fair to say that the Pib2SESE has a reduced affinity for Kog1. Based on our experience with other co-localization studies of membrane-bound proteins and protein complexes (e.g. TORC1 versus EGOC), we find it extremely difficult to quantify local interactions by fluorescence microscopy (unless they are close to all or nothing). In this case, where we have a partial defect in the interaction between Kog1 and Pib2SESE, we anticipate that such analyses will not allow us to draw additional conclusions.

Regarding the issue of Kog1/TORC1-body formation: all of our mutations in PIB2 and SCH9 were introduced (by CRISPR-Cas9) in the genome of our snf1as strain, which was used throughout this study. To analyze Kog1/TORC1-bodies, we have therefore first tried to C-terminally tag KOG1 with GFP in the genome of our strain background (similarly as was done in the original description of Kog1 bodies; PMID: 26439012). However, because all our attempts failed to create KOG1-GFP in our strain, we assumed that this construct may be lethal in our strain background. This is not completely unexpected, as it is known that the Kog1-GFP allele is hypomorphic and temperature sensitive (PMID: 19144819). In an alternative approach, we have therefore set out to study TORC1 body formation in our strains by using a GFP-TOR1 allele that can be integrated into the genome and that expresses functional TORC1 (PMID: 25046117). As we have described earlier, the respective GFP-Tor1 construct localized on vacuolar membranes and on foci that we previously have shown to correspond to signaling endosomes (PMID: PMID: 30732525, 30527664). Unexpectedly, however, when we starved the respective cells for glucose, the number of GFP-Tor1 foci did only marginally increase (20%) in our strain background over a period of up to 1 hour. Given these various unexpected issues, we prefer to not include any of these preliminary data in the current version of our manuscript, but to rather follow up on these observations in a separate study. We deem this particularly justified as the current literature on TORC1-body and TOROID formation also appears controversial and may need further clarification. For instance, while TORC1-body formation has been suggested to represent a Snf1-dependent process that is dispensable for TORC1 inhibition (PMID: 30485160), TOROID formation has been suggested to represent a Snf1-independent process that is mechanistically linked to TORC1 inhibition (PMID: 28976958).

6) In figure 5F, where the authors claim the Sch9SE mutant has lower TORC1 activity, the difference is very minor. Furthermore, corresponding lanes also show reduced levels of Snf1as expression. Hence, improved blots are required here. Also, an in vitro kinase assay with full-length Sch9 KD with and without the Ser288 mutation could solidify the observation that phosphorylation of Ser288 indeed affects TORC1-mediated phosphorylation.

We have replaced the blots in Figure 5F with an alternative set that more clearly highlights the (statistically significant) differences, while also exhibiting more equal levels of Snf1as levels. Regarding the in vitro kinase assays: we have repeatedly tried to perform TORC1 kinase assays on full length Sch9KD without success. We currently believe that proper TORC1-mediated phosphorylation of Sch9 may have to occur on membranes to which both TORC1 and Sch9 are tethered through phospholipid interactions (PMID: 29237820). We are trying to set up such a system on liposomes, but we assume that this will be a major effort that cannot be resolved in due time.

7) In figure 6E, the Sch9SE mutant shows no effect in the presence of rapamycin. Thus, in vivo, phosphorylation at Ser288 may not be perturbing the phosphorylation of Sch9 by TORC1.

When cells are grown on glucose where TORC1 is highly active (as in Fig. 6E or 6A/B in Exp), expression of Sch9SE has no significant effect indeed. However, in glucose-starved cells, where TORC1 activity is low, expression of the Sch9S288E allele clearly and significantly contributes to inhibition of Sch9-Thr737 phosphorylation by TORC1 (Figure 6A/B and Figure 5F/G).

8) According to the author's proposed mechanism, TORC1 activity in Pib2SASA or Pib2SASA/Sch9SA backgrounds should be higher during glucose starvation compared to the control strains. However, glucose starvation shows a similar level of reduction in TORC1 activity in these backgrounds. This raises concern regarding the proposed mechanism. The authors mainly base their conclusions on Ser to Glutamate mutants. The authors should be cautious that Ser to Glutamate changes may also affect the protein structure which can confer similar phenotypes. How do the authors justify this discrepancy?

Please see our response to point 2 of reviewer #1.

Author Response

Reviewer #1 (Public Review):

The authors sequence some of the oldest maize macroremains found to date, from lowland Peru. They find evidence that these specimens were already domesticated forms. They also find a lack of introgression from wild maize populations. Finally, they find evidence the Par_N16 sample already carried alleles for lowland adaptation.

Overall I think this is an interesting topic, the study is well-written and executed for the most part. I have a variety of comments, most important of which revolve around methodological clarity. I will give those comments first.

1) The authors should say in the Results section how "alleles previously reported to be adaptive to highlands and lowlands, specifically in Mesoamerica or South America" were identified in Takuno et al. 2015. What method was used? I see this partly comes in the Discussion eventually, but it would help to have it in the Results with more detail. The answer to this question would help a skeptical reader decide the appropriateness of the resource, given that many selection scans have been performed on maize genomes, the choice would ideally not be arbitrary.

This was explained in more detail in the Material and Methods section, to keep the Results and Discussion sections more concise. However, we agree that adding a brief explanation in the Results section would be useful and we have modified the revised version accordingly. Now the relevant part of the section Specific adaptation to lowlands in Mesoamerica and South America reads as follows: “To assess this, we identified in Par_N16 all covered SNPs with alleles previously reported to be adaptive to highlands and lowlands, specifically in Mesoamerica or South America by Takuno and coworkers (Takuno et al., 2015). These authors used genome-wide SNP data from 94 Mesoamerican and South American landraces and identified SNPs with significant FST values to infer which allele was likely adaptive. For example, those SNPs showing significant FST only in Mesoamerica, were characterized as adaptive for lowlands if they were at high frequency in the lowland population and at low frequency in the highland population, and vice versa. The same was applied for South America (Takuno et al., 2015). They identified 668 Mesoamerican and 390 South American previously reported adaptive SNPs, from which 32 and 20 were covered in Par_N16, respectively.”

2) How were the covered putative adaptive SNPs distributed in the genome? Were any clustered and linked? The random sampled SNPs should be similarly distributed to give an appropriate null.

The SNPs in Takuno et al. (2015) are in general at a median distance of 353 bp from each other. The 20 adaptive sites covered in Par_N16 for South America (SA) are at a median distance of 8,301,843 bp (approximately 8.3 Mbp), while the 32 for Mesoamérica (MA) are at a median distance of 24,295,968 bp (approximately 24.3 Mbp). SNPs in five pairs from Mesoamerica are closer than 100 bp between them, but each pair is at a considerable distance (beyond 1 cM) from each other and from other SNPs covered in Par_N16. This same happens for only one SNP pair from South America. Then, in general, the covered adaptive SNPs are not clustered. For our random samples, the range of genomic distances between SNPs is similar to those of adaptive SNPs. This shows that our null distributions are adequate for our statistical purposes. The genomic positions of covered adaptive sites in Par_N16 are now included in a new Table in the revised version (Supplementary File 2). We have included these observations in the main text (section Specific adaptation to lowlands in Mesoamerica and South America), as follows: “In general, adaptive SNPs represented in Par_N16 were not clustered. The 20 South American adaptive SNPs are at a median distance of 8,301,843 bp, while the 32 Mesoamerican SNPs are at a median distance of 24,295,968 bp (Supplementary File 2). SNPs in five pairs from MA are closer than 100 bp between them, but each pair is at a considerable distance (beyond 1 cM) from each other and from other SNPs. This same happens for only one SNP pair from SA. Then, although at low proportions, the adaptive SNPs in Par_N16 are a bona fide representation of different genomic responses to selection pressures...” and “We analyzed some of these random samples and observed a similar behavior as the adaptive SNPs regarding the range of distances between SNPs (Fig, S18).”

3) How is genetic similarity calculated? It should be briefly described in the Results.

This is formally explained in the Material and Methods section, but now we have included a brief description in the Results section (Specific adaptation to lowlands in Mesoamerica and South America) as follows: “The allelic similarity is the average of the frequencies of the Par_N16 alleles in the intersected sites with each test population (see Material and Methods).”

4) It would help for the authors to state why they focus on Par_N16, I did not see this in my reading. Presumably, the analyses done are because of the higher quality data, but it would also help to mention why Par_N16 was sequenced in an additional run.

Indeed, Par_N16 has an endogenous DNA content of 1.1 %, while the other two samples presented a very low DNA content (0.2%). Therefore, we decided to invest more in the best sample, as a cost/benefit decision for additional sequencing. We have included brief explanations of this in the revised text. In the Results section Paleogenomic characterization of ancient maize samples, it reads as follows: “Due to its higher endogenous DNA content (one order of magnitude larger, we further sequenced the Par_N16 library, obtaining 459M additional reads, to generate a total of 851M for this sample (Table 2).” and “To determine if the specific elimination of C to T and G to A modifications could bias the results in favor of maize rather than teosinte alleles, an additional database was generated in which all transitions were eliminated (i.e., only transversions were included) in Par_N16 only, because it was the only sample with enough sequencing data to conduct this experiment.” While in the section Tests of gene flow from mexicana, is as follows: “Par_N16 was the only sample with enough DNA sequence data to perform this analysis. All the samples showed the same phylogenetic position; therefore, Par N 16 was considered to be representative of ancient Paredones maize.”

5) In the sections on phylogenetic analysis, introgression, and D statistics, the authors could do a better job specifically indicating how the results support their conclusions.

Precise indications of how our results support our conclusions are given in the Discussion section. Nevertheless, we added relevant sentences in the specified sections. In the section Relationship between ancient maize, extant landraces, and Balsas teosinte, we added the following: “Thus, based on genome-wide relatedness, Paredones maize clusters with extant domesticated Andean landraces, supporting both, a single origin for maize and that these Peruvian samples were already domesticated.” In the section on introgression and D-statistics (Tests of gene flow from mexicana), we improved the last sentence as follows: “These results consistently show the absence of significant gene flow between Par_N16 and mexicana, implying that the lineage that gave rise to Paredones maize left Mesoamerica without relevant introgressions from this teosinte.”

Reviewer #2 (Public Review):

In this foundational article, the authors conduct an ancient DNA characterization of maize unearthed in archaeological contexts from Paredones and Huaca Prieta in the Chicama river valley of Peru. These maize specimens were recovered by painstakingly controlled excavation. Their context would appear to be beyond reproach though the individual radiocarbon determinations should be subject to further scrutiny.

1) Radiocarbon determination for at least one of the maize cobs analyzed for aDNA is not a direct date, but dates associated material. The authors should provide a table of the direct dates on the specimens that were analyzed for ancient DNA. They should also specify the type and quantity of material sent and whether the cob, glumes, pith, or husks were submitted for dates. Include δ13C determinations for each cob with laboratory analysis numbers because there is justifiable concern that at least one of these cob dates has a δ13C value suggesting the material dated is not maize. Generally, the δ13C for maize ranges from -14 to -7. One or more of the specimens subjected to ancient DNA analysis in this paper have δ13C values far outside of this confidence interval.

The indirect radiocarbon date on a maize cob was derived from a single piece of wood charcoal in a hearth directly associated with the analyzed cob, both embedded in a thin intact floor in Unit 20 at the Paredones site. The assay on the charcoal and the floor are in an undisturbed stratigraphic context and are in agreement with assays on other maize and charcoal remains in floors both above and below the hearth. We have included this information in Table 1 in the revised version. The information sought by Reviewer 2 on the studied cobs was published previously in Grobman et al. 2012 and in Dillehay 2017. Since details of the cobs were published, we decided to submit only what we thought were pertinent data for this manuscript.

As for the δ13C reading of one cob outside of the confidence interval for maize, the dated specimen with this value is a maize husk fragment. Both the macro- and micro-morphology and the ancient DNA analysis of the husk demonstrated it was maize. We do not understand what affected the δ13C value for this specimen. Similarly, three human skeletons from deeper site levels have δ13C values greater than the expected range for human remains.

2) From the perspective of future scientists being able to repeat the analyses performed here, I would hope that all details of specimen treatment, extraction methods, read length and quality would need to be assiduously described. Routine analytical results should be reported so that comparisons with earlier and future results are facilitated, and not made difficult to decipher or search for.

The general procedures for accurate ancient DNA extraction were described in Vallebueno-Estrada et al. 2016 and we do not see the need to repeat this information in this article. Specific aspects of sample treatment and DNA extraction of the samples analyzed here are described in the Material and Methods, section on Extraction and sequencing of ancient samples. Results on quality (percentage of endogenous DNA, quality-filtered reads, mapped reads to either repetitive or unique regions, amount of sequence mapped, mapping Phred scores, estimated error rates, percentage of deamination, fragment median lengths, percentage of sites with signatures of molecular damage, number of unique genomic sites covered and their corresponding average sequencing depth) are described in the Results, section Paleogenomic characterization of ancient maize samples. This section also includes the number of SNPs in relation to the reference and the number of intersected SNPs between our samples and the HapMap3 database. In addition, complementary information to this section is included in Tables 2-4 and supplementary Figures S2-S6, as properly referenced in the last mentioned section.

3) The aDNA analysis may or may not be affected by the anomalous δ13C values but one would anticipate that standard aDNA extraction and analysis protocols would provide a means by which the specimen's preservation of the specimens could be ascertained, for example, perhaps deamination and fragmentation rates could be compared or average read length evaluated with modern-contemporary materials so that preservation of the Paredones samples relative to that of maize in the CIMMYT germplasm bank and the San Marcos specimens investigated by the same researchers can be evaluated.

Average read length from contemporary material depends more on the sequencing platform than sample preservation. For example, Illumina can only read fragments of hundreds of base pairs, while MinIon or PacBio can read fragments in the order of kb. Also, deamination is not an issue in DNA extracted from modern material (unless bisulfite is used for methylation detection). Comparison with San Marcos samples indicates that Paredones samples are heavily degraded, although this is not a function of time only (humidity, temperature, and pH are among other relevant factors). Therefore, to avoid misleading interpretations, we are not including a comparison with San Marcos samples in the revised version.

4) The size and shape of the cobs depicted are similar to specimens occurring much later in Mesoamerican assemblages. For example, the approximate rachis diameter of the San Marcos specimens depicted by Valle-Bueno et al. (2016: Fig.1) averages less than 0.5cm while the specimens depicted in Valle-Bueno et al. (this manuscript) average 1.0 cm. The former - San Marcos - specimens are dated at 5300-4970 BP cal while the larger - Paredones - specimens date roughly 6777 - 5324 BP cal. The considerable disparity among the smaller more recent specimens compared to the very much larger putatively older specimens suggests the Paredones specimen's radiocarbon determinations are equivocal. The authors point this out but repeatedly state these cobs are the most ancient; a conundrum that should be resolved.

Radiocarbon determinations in Paredones are not equivocal, on the contrary, they are perfectly in agreement with and supported by the unimpeachable stratigraphy of the site and by more than 150 other radiocarbon and OSL dates from Paredones and nearby excavated contexts. The difference in morphology between the more recent samples from Tehuacan and the more ancient samples from Paredones is exactly the paradox we try to address. Our results indicate that the rapid migration and adaptation of maize to the coast of Peru in comparison with a slower migration and adaptation to Tehuacan lands explains this apparent conundrum. This rapid movement and migration allowed the presence of more “modern” maize in Peru than in Tehuacan on the respective dates. This more rapid maize development also coincides with more rapid and advanced socio-cultural transformations in Peru, including proto-urbanism (i.e, first cities), early religious symbolism, long-distance irrigation canals, and other major innovations that far exceed what was happening in Mesoamerica at the time.

5) I would suggest the authors consider redating these three specimens and if they do, hope that they will prepare the laboratory personnel with depositional environment information. MacNeish was skeptical about late dates on maize at Tehuacan, at first. Adovasio was initially certain about maize's associated dates from Meadowcroft. One would prefer to be reasonably certain the foundation this article creates is solid; the author's repeated reference to these cobs as the most ancient in the Americas should be reaffirmed so retraction will not be necessary.

As discussed in Grobman et al. 2012 and in Dillehay 2017, we do not confide in C14 dating of unburned corn remains due to the possible intrusion of fungi in the soft cellular structure of cobs. The chrono-stratigraphically acceptable dates on cobs and other maize remains were taken on burned and hard tissue remains, such as husks. See detailed discussion in Supplementary Materials.

MacNeish and Adovasio were excavating cave and rock shelter sites, which are known to often have areas of stratigraphically disturbed deposits. Paredones, Huaca Prieta, SR-18 and other Preceramic sites excavated in the study area here contain late to early varieties of maize and radiocarbon assays that are in chrono-stratigraphic agreement. As noted in the main text and in prior publications, these sites are open air localities with clear stratigraphy defined by intact floor and fill sequences, with no tree root, animal burrowing, or other major taphonomic disturbances.There were occasional hearths and pits (i.e., human burials) that intruded into deeper floor-fill sequences but none of the assayed and studied maize samples were derived from these contexts. Once again, we encourage readers to examine the stratigraphy shown in the main text and in Grobman et al. (2012) and Dillehay (2017). Moreover, as noted in the text, there is a growing number of Preceramic sites in South America that date between 6800 and 6000 years ago and later that contain micro-maize remains (see Kistler et al., 2018). Not all of these sites are well-dated and present reliable contexts, but several have good chrono-stratigraphic settings and micro-evidence (e.g., phytoliths, starch grains) indicative of a maize presence at or prior to 6000 years ago.

Author Response

Reviewer #3 (Public Review):

The only substantial point I raise relates to the sexual selection (mate choice) part of the work. While it has no major effect on the overall conclusion, I think their interpretation needs to be reconsidered.

When reporting the results of mate choice experiment (L219ff), the authors state that males of wild and Klara type preferred wild-type females, because 75% of laid eggs belonged to wild-type females. However, another possibility is that Klara females had reduced fecundity, and the lower share of eggs had nothing to do with mate choice. In the same way, "90% of eggs were fertilized by wild-type males" (L223) is used to conclude that they were preferred by females (active mate choice). However, male success in N. furzeri is largely driven by male dominance (and not female mate choice) and it is more likely (and more precise to state) that wild-type males were more successful in male-male competition for access to females (and fertilize their eggs). This is especially so because wild-type males were larger (L. 322) and body size plays a major role in establishing dominance between N. furzeri males. This is then also pertaining to interpretation in discussion (L 318).

Concerning fecundity, we analyzed quantity and quality of eggs obtained from either klara or wild type breeding groups. As shown in Figure 3A we did not observe differences between klara and wild type fish. Thus, we conclude that fecundity is not reduced in klara females. Regarding males, we did not observe a size difference between the klara and wild type animals in this experiment (Fig. 3C), however, weight was different. As noted by the reviewer, this might influence male dominance and breeding success. We have been more explicit on this in the discussion of the revised version.

Author Response

Reviewer #1 (Public Review):

This paper presents the results of two fragment screens of PTP1B using room-temperature (RT) crystallography, and compares these results with a previously published fragment screen of PTP1b using cryo-temperature crystallography. The RT screen identified fewer fragment hits and lower occupancy compared to the cryo screen, consistent with prior publications on other proteins. The authors attempted to identify additional hits by applying two additional layers of data processing, which resulted in a doubling in the number of possible hits in one of the screens. Because I am not an expert in panDDA modeling, however, I am unable to evaluate the reproducibility and potential potency of these fragment hits as protein binders or their potential use as starting points for follow-up chemistry.

The fragment library used in this study was larger than those used in previously published RT crystallography experiments. Among the cryo hits that bound in RT, most fragments bound in the same manner as they did in cryo, while some bound in altered orientations or conformations, and two bound at different locations in RT compared to cryo. This level of variability is not surprising. However, one fragment was observed to bind covalently to lysines in RT, even though it showed no density in the cryo crystallization attempt. It is unclear from the provided information whether this fragment decayed during storage or if the higher temperatures accelerated the covalent chemistry. The authors also observed temperature-dependent changes in the solvation shell, and modifications to the protein structure upon fragment binding, including a distal modification.

We thank the reviewer for the thorough summary of our manuscript.

Regarding reproducibility of fragment hits, cryo structures are more variable than RT structures for proteins themselves (Keedy et al., Structure, 2014). Thus the variability of repeated cryo-temperature crystallography experiments is a relevant consideration when comparing cryo to RT structures for protein-ligand interactions. However, to our knowledge, no published papers have explored this issue. Our previous cryo fragment screen (Keedy, Hill, et al., eLife, 2018), as with many others, was focused on breadth (many fragments), not depth (replicates). Unpublished work by some of the authors of the present study suggests that fragment poses are robust in replicate cryo experiments; however, future studies focused on fragment reproducibility in terms of binding occupancy, pose, and site at cryo temperature would be useful contributions to the field.

Regarding follow-up chemistry, there is growing evidence from multiple successful fragment-based inhibitor design studies (COVID Moonshot Consortium et al., bioRxiv, 2022; Gahbauer, Correy, et al., PNAS, 2023; etc.) that, although fragments usually bind too weakly to impact function on their own, they offer rich information to seed the design of high-affinity, potent functional modulators of proteins. As our study is the first to report many structures of fragments bound to proteins at RT, we cannot yet comment as to whether they offer unique advantages over cryo fragments in downstream fragment-based drug design efforts, but this is an open area for future study.

Regarding the covalent lysine binder, we agree with the reviewer on this point; our manuscript includes a note to this effect. Unfortunately we were unable to obtain the original fragment sample for mass spectrometry analysis. Returning to the point above about follow-up chemistry, the path forward for this fragment hit is promising and clear, and includes confirming chemistry using the original nominal compound vs. what is observed in the electron density, fragment linking and/or expansion, functional assays, and structural biology, all hopefully leading to a potent covalent inhibitor of wildtype PTP1B.

The current version of the paper is somewhat repetitive in its presentation of the results and could be clearer in its presentation of the variations and comparisons of the two different protocols. It would be helpful to have a more concise summary of the differences between the two protocols in the current paper, as well as a discussion of how they compare to the protocol used in the previously published cryo-temperature fragment screen.

We agree that it would be helpful to cut down on any redundant text and more straightforwardly compare/contrast the different room-temperature screen methods vs. the previous cryo-temperature screen method. To address this suggestion, we deleted the Discussion paragraph about the strengths and weaknesses of the two methods relative to serial approaches, deleted the text in the Introduction that introduces the two screens, and placed new text at the start of the Results section in the subsection titled “Two crystallographic fragment screens at room temperature” to provide a concise summary in one location of the manuscript.

While I appreciate the speculative nature of the discussion at the end of the paper, the evidence presented by the authors does not instil confidence that these results will correspond to meaningful binders that could be used to train future machine learning models. However, depending on the intended use, it may be acceptable to train ML models to predict expected densities under typical experimental conditions.

Indeed, this part of the Discussion is speculative, and seeks to place our results into a possible broader context. The definition of “meaningful binders” in the context of fragment screening is a difficult one. As noted above in response to the comment about follow-up chemistry, one important measure of meaningfulfulness is the ability to successfully seed structure-based design of analogs that have potent functional effects, and many fragments do meet this definition. Regarding potential applications to machine learning, we agree it is not self-evident that structural data for small-molecule fragments will be readily translatable to AI/ML methods aimed at larger compounds. The reviewer’s point about predicting densities is an intriguing one, and is in line with the fragment screening ethos, including existing experimental as well as computational (e.g. Greisman, Willmore, Yeh*, et al., bioRxiv, 2022) approaches to mapping ligandable surface sites and regions. The number of RT structures we report here is high relative to most crystallography studies, but still is likely insufficient to explore questions about AI/ML training, and at any rate would be beyond the scope of the current report. However, it seems equally true that AI/ML methods trained on structures based on data from nonphysiological cryogenic conditions, with associated structural artifacts, may have some (previously unrecognized) limitations, and thus RT crystal structures can play a useful role in AI/ML training sets in the future. We have added new text to the Discussion paragraph in question to convey these points.

Reviewer #2 (Public Review):

The authors set out to understand how a room-temperature X-Ray crystallography-based chemical-fragment screen against a drug target may differ from a cryo screen. They carried out two room-temperature screens and compared the results with that of a cryo screen they previously performed. With a substantial set of crystallographic evidence they showed that the modes of protein-fragment binding are affected by temperature. The conclusion of the work is compelling. It suggests that temperature provides another dimension in X-ray crystallography-based fragment screening. In a practical sense, it suggests that room-temperature fragment screen is a promising new avenue for hit identification in drug discovery and for obtaining insights into the fragment binding. Room-temperature screening carries unique advantage over cryo screening. This work is confirmative to the notion, which seems not yet universally considered, that very weak protein-small molecule binding may be inherently fluid structurally, and that crystal structures of such weak binding, especially cryo structures, cannot be taken for granted without cross validation.

We thank the reviewer for their clear summary and positive comments about our manuscript.

Author Response

Reviewer #2 (Public Review):

In this study, The authors developed a mouse model to specifically investigate whether GC B cells that present nuclear protein (NucPr) could be specifically suppressed by Tfr cells. Most current mouse models that have been used in investigating Tfr functions are based on the overall readout of autoantibody production in the scenario of loss-of-function of Tfr cells. The proposed model of gain-of-function of Tfr cells is novel and valuable.

The authors mainly compared two boosting immunizations by Strepatividin (SA) alone or SA-conjugated with nuclear proteins (SA-NucPr) and demonstrated SA-NucPr boosting immunization was able to expand Tfr cells, suppress overall and SA-specific GC/memory/plasma cell responses. The results are mostly convincing.

One major concern is the conditions and controls used in the study. The control group (SA boosting immunization) would have enhanced T and B cell responses by this boosting. Unfortunately, there was no non-boosting control group so the level was unclear. It is therefore to strictly match such boosting condition in the SA-NucPr group. Notably, both SA and SA-NucPr were used at 10ug for boosting immunization. Considering NucPr were comparable or much larger (Nucleosome, about 200KDa) than SA (about 60KDa), the dose of SA in the SA-NucPr group was far less than that in the SA group. Due to this cavity, it is difficult to judge the difference between two groups was due to less SA boosting immunization or NucPr-induced Tfr function. This was a fundamental issue weakens the conclusion.

The single cell analyses clearly demonstrated the expansion of Tfr clones. It remains unclear why other Treg populations other than Tfr cells were not expanded? The Treg cells in the CXCR5intPD-1int population were recently activated and should be able to respond to the boosting immunization. On an alternative explanation, the changes in Tfr cells could be indirectly driven by the changes in Tfh cells. For example, Tfh can produce IL-21 and restrict Tfr expansion (Jandl C, et al.2017). This could be the case of the reduction in Tfr cells in the SA-OVA group as compared to the SA group.

As the reviewer, we were surprised not to detect significant increase in the levels of CXCR5intPD-1int Tregs in the original experiment after the boosting with SA-NucPrs(Fig.1). Our interpretation of this result was that the fraction of NucPr-specific CXCR5intPD-1int Tregs was small as compared to the total CXCR5intPD-1int Tregs and proliferation of this small fraction of cells would not be detectable by flow cytometry analysis of the total CXCR5intPD-1int Tregs numbers. Alternatively, the observed rapid accumulation of Tfrs was due to proliferation of the NucPr-specific Tfrs that may be abundant after a standard immunization with foreign antigen.

In single cell analysis we have used only presorted CXCR5highPD1high follicular T cells so majority of CXCR5intPD-1int Treg population was excluded from the analysis.

Author Response

Reviewer #1 (Public Review):

The authors optimize a live cell imaging method based on the detection of FAD/NAD(P)H adopted from the fast-growing field of live metabolic imaging. They build upon a method described by KreiB et al 2020 that used metabolic ratio and collagen fiber second harmonic generation imaging. They follow by combining metabolic imaging with morphologic measurements to train a machine-learning model that is able to identify cell types accurately. Upon visualization, authors detected structures hypothesized and then proven to resemble the "goblet cell associated antigen passages" previously studied in intestinal epithelia.

STRENGTHS

• The manuscript is succinct, well written, and overall done rigorously.

• The optimization of the method at multiple levels to the point of identifying both common and rare cell types is impressive.

• Describes the elegant implementation of a sorely needed method in epithelial biology.

• Provides an approach to studying the cholinergic response in epithelial cells, a poorly understood phenomenon despite broad clinical use for diagnosis and treatment.

WEAKNESSES

A) For what is in large part a methods-development paper, the methods are not explained or shared in a manner that facilitates reproducibility. For example:

A.1.) The training and validation datasets seem to come from the same sample (or the source is not clearly described). Therefore, it is not clear whether the "96% accuracy" refers to accuracy within the sample measured, or whether it can extrapolate to other samples.

In order to avoid any confusion, we further clarify that the machine learning training and validation data sets come from the same sample. We had split the total data set into 2 separate subsets for this purpose. This has been laid out in the text as follows:

“In order to assess the performance of machine learning algorithms designed to distinguish cell types, we divided our data set into training and testing subsets. We utilized 75% of the total cells (154 cells) for machine learning training, leaving 25% (52 cells) for subsequent validation.”

A.2.) It is unclear whether the model needs to be re-trained within each new sample measured, or if it's applicable to others. This has implications for method adoption by others. Either way is useful but needs to be clarified.

This is a very interesting point and one that we further clarify in the Discussion noting that in both disease and non-diseased states the model needs to be re-trained in each particular experimental regime.

A.3.) Code was only listed in a PDF file, which makes reproducing the analysis very cumbersome.

We hope that all can utilize the code made for this methodology and have uploaded it to a publicly available GitHub account:

https://github.com/vss11/Label-free-autofluorescence

B) Whereas the optimization to improve cell type detection is very well described, the implementability of the approach could benefit from exploration (using the data already obtained) of the minimal set of measurements needed to identify cell types. For example, is the FAD/NAD(P)H ratio necessary? Or could just morphologic measurements achieve the same goal?

This is an excellent point, and we appreciate the Reviewer’s suggestion for this analysis. We have added Figure 3 Supplement 5 where we perform modeling without autofluorescence data. This analysis reveals a dramatic reduction in accuracy with a Matthew’s correlation coefficient ranging from 0.66 to 0.78. This provides additional justification for the use of autofluorescence for cell type identification. Morphologic measurements are not sufficient for cell type identification alone.

We also have determined the relative contribution of each characteristic to the cell type identification by the Xgboost algorithm in Figure 3 Supplement 4, which shows that autofluorescence signatures are amongst the top contributing characteristics to cell type identification by machine learning.

C) Whereas the conclusions are overall supported by the data, need small adjustments in some cases:

C.1.) For example, P3L80: Claims autofluorescence imaging is more specific than "functional markers", however, this is done in the setting of a very specific intervention that massively affects a protein often used as a secretory cell marker (CCSP aka SCGB1A1), which is known to be secreted (and depleted) in secretory cells upon stimulation.

We agree with the Reviewer that secretory cell identification is a prime example where autofluorescence imaging may be superior to conventional staining, specifically due to the point the Reviewer makes regarding CCSP secretion. We discuss this concept in the Discussion while giving examples of CCSP staining being reduced in asthma, COPD, and smokers. It could be that these cells are missed due to depletion of CCSP. Indeed, we clarify that our methodological approach may be less affected by the loss of the category of specific markers that change with cell state. There are, of course, caveats with utilizing this approach in disease states, and we elaborate on this further below and add this point to the discussion.

C.2.) Relatedly, it is unclear how the method's accuracy would be affected in conditions that affect redox/metabolic state; the approach may be highly affected in inflammation and injury, for example.

As suggested by the Reviewer, we re-analyzed the data after Antimycin A + Rotenone and FCCP to determine if autofluorescence ratio is sufficiently different to identify ciliated and secretory cells and included this data in Figure 2 Supplement 1. This is an example where the redox/metabolic state is indeed altered. Though the autofluorescence ratio is affected, it is still useful for cell type identification after intervention as the ciliated and secretory cells have statistically different ratios.

However, different disease states, particularly infection and inflammation may result in a more profound effect on autofluorescence signatures. For instance, previous work by Dilipkumar et. al, 2019 found changes in autofluorescence over days in repeated measurements in a mouse model of inflammatory bowel disease. Therefore, it is likely that the cell type identification methodology will need to be re-optimized for different experiments and diseased tissues. We include commentary to this effect in the discussion.

D) The data used to describe "SAPs" is very cursory.

To further elaborate on our description of SAPs we have included the following:

1) SAP formation occurs in secretory cells in both stimulated and unstimulated conditions. We performed additional analysis of Figure 4C and determined that SAP formation does occur at baseline prior to stimulation in 9% of secretory cells. Methacholine addition results in 78% of secretory cells forming SAPs (Figure 4 Supplement 1). We have added Figure 5C to demonstrate that SAP formation occurs in the absence of stimulation and is enhanced after methacholine stimulation.

2) We demonstrate that SAPs can uptake both FITC-dextran and FITC-ovalbumin in Figure 5E, and Figure 5 Supplement 2. We also now show that immune cells (CD11c antigen presenting cells) associate with SAPs containing FITC-dextran and FITC-ovalbumin in Figure 5E and Figure 5 Supplement 2. We have expanded the Discussion of SAPs.

3) We now show 3 video examples and an XZ optical cross section of ALI that demonstrate uptake and secretion of FITC-dextran in Figure 5 Supplemental Videos 1-3 and Figure 5 Supplement 1.

D.1.) Unclear if FITC dextran uptake occurs in other cells too, or in secretory cells prior to methacholine stimulation, or induced nonspecifically due to epithelia manipulation. Secretory and goblet cells are very sensitive to stimulation and often considered minimal, for example, see the paper by Abdullah et al DOI:10.1007/978-1-61779-513-8_16 in which extreme care had to be applied to prevent any secretion at all.

Our autofluorescence methodology revealed the formation of “voids” of autofluorescence forming in secretory cells and we focused our experiments on this phenomenon. Based on the reviewer question, we generated Figure 5C to better characterize SAP formation. Figure 5C illustrates that SAP formation occurs in both unstimulated and methacholine stimulated conditions, but is dramatically increased following methacholine stimulation. This is analogous to the behavior of GAPs in the intestine (Knoop et al., 2015). Furthermore, we have reanalyzed Figure 4C to identify SAPs prior to stimulation and found that these structures are present in 9% of secretory cells. After methacholine stimulation this percentage increases to 78%.

D.2.) A single image is provided for the SAP timeline (Figure 5C), which appears to be the same cell shown in the supplementary video.

We now provide numerous example videos and optical XZ cross section of ALI demonstrating SAP uptake and secretion in Supplementary Videos 1-3 and Figure 5 Supplement 1.

IMPACT AND UTILITY

This is well-done work with high potential for widespread adoption within the epithelial biology community, particularly if the methods and code are shared in better detail.

We indeed hope that this methodology can be utilized by others. We have posted analysis code, raw data, MATLAB algorithm, and other necessary files onto a publicly available GitHub link. https://github.com/vss11/Label-free-autofluorescence

Reviewer #2 (Public Review):

Shah and colleagues tackle a significant impediment to exploiting tissue culture systems that enable prospective ex vivo experimentation in real-time. Namely, the ability to identify and track dynamic and coordinated activities of multiple composite cell types in response to experimental perturbations. They develop a clever label-free approach that collects biologically-encoded autofluorescence of epithelial cells by 2-photon imaging of mouse tracheal explant culture over 2 days. They report the ability to distinguish 7 cell types simultaneously, including rare ones, by developing a machine-learning approach using a combination of fluorescence and cytologic features. Their algorithm demonstrates high accuracy by Mathew's Correlation Coefficient when applied to a test set. Lastly, they show the ability of their approach to visualize the dynamic uptake and expulsion of fluorescently-tagged dextran by individual secretory cells. Overall, the results are intriguing and may be very useful for specific applications.

We thank the reviewers for their assessment and indeed hope that the methodology is useful and the discovery of the dynamics of SAP formation have important implications for airway mucosal immunology.

Author Response

Reviewer #1 (Public Review):

Animal colour evolution is hard to study because colour variation is extremely complex. Colours can vary from dark to light, in their level of saturation, in their hue, and on top of that different parts of the body can have different colours as well, as can males and females. The consequence of this is that the colour phenotype of a species is highly dimensional, making statistical analyses challenging.

Herein the authors explore how colour complexity and island versus mainland dwelling affect the rates of colour evolution in a colourful clade of birds: the kingfishers. Island-dwelling has been shown before to lead to less complex colour patterns and darker coloration in birds across the world, and the authors hypothesise that lower plumage complexity should lead to lower evolutionary rates. In this paper, the authors explore a variety of different and novel statistical approaches in detail to establish the mechanism behind these associations.

There are three main findings: (1) rates of colour evolution are higher for species that have more complex colour phenotypes (e.g. multiple different colour patches), (2) rates of colour evolution are higher on island kingfishers, but (3) this is not because island kingfishers have a higher level of plumage complexity than their mainland counterparts.

I think that the application of these multivariate methods to the study of colour evolution and the results could pave the way for new studies on colour evolution.

We appreciate this positive comment about our manuscript.

I do, however, have a set of suggestions that should hopefully improve the robustness of results and clarity of the paper as detailed below:

1) The two main hypotheses tested linking plumage complexity and island-dwelling to rates of colour evolution seem rather disjointed in the introduction. This section should integrate these two aspects better justifying why you are testing them in the same paper. In my opinion, the main topic of the paper is colour evolution, not island-mainland comparisons. I would suggest starting with colours and the challenges associated with the study of colour evolution and then introducing other relevant aspects.

We implemented this suggestion by reorganizing the introduction to introduce color/and challenges with studying it (para 1), then we discuss plumage complexity (para 2). We follow this with a paragraph about the importance of islands in testing evolutionary hypotheses (para 3), and onto kingfishers as a model system (para 4) and our hypothesis/predictions (para 5).

2) Title: the title refers to both complex plumage and island-dwelling, but the potential effects of complexity should apply regardless of being an island or mainland-dwelling species, am I right? Consider dropping the reference to islands in the title.

We removed “island” from the title.

3) The results encompass a large variety of statistical results some closely related to the main hypothesis (eg island/mainland differences) tested and others that seem more tangential (differences between body parts, sexes). Moreover, quite a few different approaches are used. I think that it would be good to be a bit more selective and concentrate the paper on the main hypotheses, in particular, because many results are not mentioned or discussed again outside the Results section.

We removed analyses that we felt were distracting from our main point (e.g., MCMCglmm) and streamlined our approach to use PGLS methods for both rates (phylolm) and multivariate color patterns (d-PGLS). The relevance of sex differences in coloration is also made more clear, as we added details about how we tested for a relationship between male and female coloration and that we use this strong correlation as a justification for averaging color by species (e.g., see lines 369-375).

4) Related to the previous section, the variety of analytical approaches used is a bit bewildering and for the reader, it is unclear why different options were used in different sections. Again, streamlining would be highly desirable, and given the novel nature of the analytical approach (as far as I know, many analytical approaches are applied for the first time to study colour evolution) it would be good to properly explain them to the reader, highlighting their strengths and weaknesses.

We appreciate the suggestion and have now included a workflow diagram, as suggested (see Figure 1). We further added considerable detail to the Methods (old length = 502 words, new length = 1355 words) and mention caveats of the approaches we have taken (e.g., line 308: “We used photosensitivity data for the blue tit (Hart et al., 2000) due to the limited availability of sensitivity data for other avian species”).

5) The Results section contains quite a bit of discussion (and methods) despite there being a separate Discussion section. I suggest either separating them better or joining them completely.

We appreciate this. We were following other eLife articles that include more discussion within the Results, therefore we would prefer to leave these aspects in place. However, we did move a considerable amount of information from the Results section to the Methods section. In addition, we also reorganized the Results to better match the logical flow of the Introduction. The end result, we hope, is a Results section that is considerably more streamlined.

6) The main analyses of colour evolutionary rates only include chromatic aspects of colour variation. Why was achromatic variation (i.e. light to dark variation) not included in the analyses? I think that such variation is an important part of the perceived colour (e.g. depending on their lightness the same spectral shape could be perceived as yellow or green, black or grey or white). I realize that this omission is not uncommon and I have done so myself in the past, but I think that in this case, it is highly relevant to include it in the analyses (also because previous work suggests that island birds are darker than their mainland counterparts). This should be possible, as achromatic variation may be estimated using double cone quantum catches (Siddiqi et al., 2004) and the appropriate noise-to-signal ratios (Olsson et al., 2018). Adding one extra dimension per plumage patch should not pose substantial computational difficulties, I think.

We incorporated this suggestion and we have now fully integrated achromatic color variation into all of our analyses. These new analyses let us compare results to previous work showing that island birds are darker than mainland counterparts. We further discuss the caveats of chromatic and achromatic channels (e.g., lines 313-317: “Although it is possible, in theory, to combine chromatic and achromatic channels of color variation in a single analysis (Pike, 2012), we opted to analyze them separately, as these different channels are likely under different selection pressures (Osorio and Vorobyev, 2005).”).

7) The methods need to be much better explained. Currently, some methods are explained in the main text and some in the methods section. All methods should be explained in detail in the methods section and I suggest that it would be better to use a more traditional manuscript structure with Methods before Results (IMRaD), to avoid repetition (provided this is allowed by the journal). Whenever relevant the authors need to explain the choice of alternative approaches. Many functions used have different arguments that affect the outcome of the analyses, these need to be properly explained and justified. In general, most readers will not check the R script, and the methods should be understandable to readers that are not familiar with R. This is particularly important because I think that the methodological approach used will be one of the main attractions of the manuscript, and other researchers should be able to implement it on their own data with ease. Judging from the R script, there are quite a few analyses that were not reported in the manuscript (e.g. multivariate evolutionary rates being higher in forest species). This should be fixed/clarified.

We clarified several methodological details in the manuscript (e.g., added package versions throughout, mention the permutation option used for compare.evol.rates, cited RPANDA) and modified the Methods section considerably to make logical connections among the sections. We also checked and cleaned up the R markdown file to ensure the analyses were in sync with the manuscript analyses.

Reviewer #2 (Public Review):

In "Complex plumages spur rapid color diversification in island kingfishers (Aves: Alcedinidae)", Eliason et al. link intraspecific plumage complexity with interspecific rates of plumage evolution. They demonstrate a correlation here and link this with the distinction between island and mainland taxa to create a compelling manuscript of general interest on drivers of phenotypic divergence and convergence in different settings.

This will be a fantastic contribution to the literature on the evolution of plumage color and pattern and to our understanding of phenotypic divergence between mainland and island taxa. A few key revisions can help it get there. This paper needs to get, fairly quickly, up to a point where the difference between plumage complexity and color divergence is defined carefully. That should include hammering home that one is an intraspecific measure, while one is an interspecific measure. It took me three reads of the paper to be able to say this with confidence. Leading with that point will greatly improve the paper if that point gets forgotten then the premise of the paper feels very circular.

We hope our considerable modifications throughout–including explicitly mentioning that complexity is an intraspecific measure whereas rates are interspecific (e.g., see lines 65, 140, 170, 667)–have made the premise of the paper more clear. We also added a new workflow figure (Figure 1) that includes example species pairs showing cases in which intraspecific plumage complexity and interspecific color divergence could show a negative relationship, rather than a positive one as we predict in the manuscript. We discuss this detail in lines 159-161 (“However, this is not necessarily the case, as there are examples within kingfishers that show simple plumages yet high color divergence, as well as complex plumages with little evolutionary divergence (Figure 1B).”).

Also importantly, somewhere early on a hypothesized causal pathway by which insularity, plumage complexity, and color divergence interact needs to be laid out. The analyses that currently follow are good ones, and not wrong, but it's challenging to assess whether they are the right ones to run because I'm not following the authors' reasoning very well here. I think it's possible a more holistic analysis could be done here, but I'll refrain from any such suggestions until I better get what the authors are trying to link.

We overhauled the Introduction. This included adding lines that connect the ideas of complexity and insularity (lines 65-58: “intraspecific plumage complexity (i.e., the degree of variably colored patches across a bird's body) could be a key innovation that drives rates of color evolution in birds and should be considered alongside ecological and geographic hypotheses.”) and insularity and color divergence (lines 69-85). We also rethought the analyses and now include PGLS analyses using tip-based rates that allow us to account for both insularity and complexity in the same analysis.

We also need something near the top that tells us a bit more about the biogeography of kingfishers. Are kingfisher species always allopatric? I know the answer is no, but not all readers will. What I know less well though is whether your insular species are usually allopatric. I suspect the answer is yes, but I don't actually know.

Great point. We have added details to the manuscript to clarify this (e.g., line 214: “The number of sympatric lineages ranged from 1–9 on islands, and 6–38 for mainland taxa.”).

In short, how do the authors think allopatry/sympatry/opportunity for competition link to mainland vs. island link to plumage complexity? And rates of color evolution? Make this clear upfront.

We believe our revised introduction makes these connections much clearer.

Author Response

Reviewer #1 (Public Review):

Causality is important and desired but usually difficult to establish. In this work, Park et al. conducted a comprehensive phenome-wide, two-sample Mendelian randomization analysis to infer the casual effects of plasma triglyceride (TG) levels on 2,600 disease traits. They identified causal associations between plasma TG levels and 19 disease traits, related to both atherosclerotic cardiovascular diseases (ASCVD) and non-ASCVD diseases. They used biobank-scale data in both discovery analysis and replication analysis.

The conclusions of this work are mostly supported by the data and analysis, but some aspects need to be clarified and extended.

(1) The datasets used in this study may not be very consistent. For example, UKB participants are aged 40-69 years old at recruitment. In addition, UKB is United Kingdom-based and FinnGen is Finland-based. So the definition of outcomes may not be identical. The authors should discuss the differences between the datasets and their potential effects.

The reviewer is correct about the differences between UKB and FinnGen and that the definition of clinical outcomes between the two datasets may not be identical due to differences in healthcare systems and population demographics. We now mention this in the discussion section as a potential limitation.

Manuscript changes:

Line 520-539: “Third, UKB and FinnGen have innate differences in participant demographics and medical coding systems, due in part to the former being based in the United Kingdom and the latter in Finland. As such, potential misclassification of participants in case-control assignment is a liability to this study. We exercised caution in mapping UKB traits to FinnGen traits, but we were unable to reliably map all “categorical” traits from UKB to corresponding traits in FinnGen, testing for replication only 221 of the 598 associations that were nominally significant in the primary analysis. We note however that, despite geographical differences, both datasets largely involve White European participants of older age, with the mean age in UKB and FinnGen being 56.5 and 59.8, respectively.”

(2) The discovery analysis and replication analysis are not completely independent because data from UKB have been used in both analyses. Although in discovery, the data were used for association with outcomes; while in replication, the data were used for association with exposure. The authors may want to explain if this may cause problems.

The reviewer is correct that UKB data were used in both the discovery and replication analyses with the caveat that the discovery analysis used UKB for outcomes while using GLGC for exposures, whereas the replication analysis used UKB for exposures while using FinnGen for outcomes. We believed this would be a creative use of three different datasets and a strength of the study; however, we agree that examining the implications of this study design is needed to acknowledge potential biases. We now expand on this in the discussion section as a potential limitation.

Manuscript changes:

Lines 539-545: “Fourth, discovery and replication analyses were not completely independent, since UKB data were used in both analyses. This could potentially exacerbate demographic and measurement biases inherent to UKB; however, we show that taking a traditional replication approach using GLGC instead of UKB for selecting exposure instruments in replication returns comparable Tier 1 results (Supplementary Files 5), while losing statistical power to highlight many of the Tier 2 and 3 results.”

(3) As stated in the manuscript, there are three assumptions for MR analysis. The validity of the results depends on the validity of the assumptions. The last two assumptions are usually difficult to validate. To the authors' credit, they conducted sensitivity analyses addressing horizontal pleiotropy, which is related to assumption 3. It would be helpful if the authors can discuss those assumptions explicitly.

We now explicitly state the assumptions of Mendelian randomization in the introduction section and discuss the validity of these assumptions in the discussion section.

Manuscript changes:

Lines 501-514: “The study has several limitations. First, MR is a powerful but potentially fallible method that relies on several key assumptions, namely that genetic instruments are (i) associated with the exposure (the relevance assumption); (ii) have no common cause with the outcome (the independence assumption); and (iii) have effects on the outcome solely through the exposure (the exclusion restriction assumption) (Hartwig et al., 2016). In MR, (i) is relatively straightforward to test, while (ii) and (iii) are difficult to establish unequivocally. As a prominent example, horizontal or type I pleiotropy has been shown to be common in genetic variation, which can bias MR estimates (Verbanck et al., 2018) (Jordan et al., 2019). This occurs when a genetic instrument is associated with multiple traits other than the outcome of interest. To detect and correct for this as best as possible, we used various MR tests as sensitivity analyses that each aim to adjust for or account for the presence of horizontal pleiotropy, including MR-PRESSO, as well as MR-Egger and weighted median methods. There is no universally accepted method that is perfectly robust to horizontal pleiotropy, but we take the best current approach by using multiple methods and examining the consistency of results.”

Reviewer #2 (Public Review):

This work conducted a Mendelian randomization analysis between TG and a large number of disease traits in biobanks. They leverage the publicly available summary statistics from the European samples from the UK Biobank and FinnGen. A solid but routine standard summary-statistics based MR study is conducted. Several significant causal associations from TG to phenotypes are called by setting p-value cutoff with some Bonferroni correction. Sensitivity statistical analyses are conducted which generate largely consistent results. The research problem is important and relevant for public health as well we drug development. Overall this is a solid execution of current methods over appropriate data source and yields a convincing result. The interpretation of the results in discussion is also well-balanced.

While the paper does have strengths in principle, a few technical weaknesses are observed.

They used UK Biobank as the discovery and FinnGen as the replication. But the two cohorts are rather used symmetrically. Especially for the Tier 3 (NB), it seems to be an attempt of reusing the replication cohort as the discovery. I wonder if that would create additional multiple testing burden as a greater number of hypotheses are considered.

We thank the reviewer for this thought-provoking comment. As the reviewer is aware, MR studies have generally not accounted for multiple testing in the past since they have usually focused on single exposures and/or single diseases. Ours is among one of the more unique MR studies taking a phenome-wide, high-throughput approach, so determining the optimal threshold for balancing true-positive vs. false-positive discovery is an important aspect of the study warranting discussion.

We agree that Tier 3 results carry the least stringent level of statistical evidence (i.e., nominally significant in discovery using UK Biobank and Bonferroni-significant in replication using FinnGen), and that these results should be interpreted with caution. As a phenome-wide study, a significant aim of this work was to generate hypotheses, and so, we decided to present our results using the three tiers of statistical evidence to highlight as many promising associations as possible for further investigation. Nevertheless, we now express extra caution in the results and discussion sections regarding Tier 2 and 3 results, and we also note as a limitation that these results especially require external replication.

Manuscript changes:

Lines 438-444: “Regarding non-ASCVDs, we present suggestive genetic evidence of potentially causal associations between plasma TG levels and uterine leiomyomas (uterine fibroids), diverticular disease of intestine, paroxysmal tachycardia, hemorrhage from respiratory passages (hemoptysis), and calculus of kidney and ureter (kidney stones). Due to the weaker statistical evidence supporting these associations, special caution is encouraged when interpreting these results to infer causality, and further replication and validation studies are essential for all Tier 2 and Tier 3 results.”

The replication p-value cutoff is a bit statistically lenient. In a typical discovery-replication setting the two stages are conducted sequentially and replication should go through the Bonferroni adjustment on the number of significant signals from discovery that is tested in the replication. For example, in this case, in tier 2, the cutoff should be 0.05/39. This may make the association of leiomyoma of the uterus slightly non-significant though. Similar cutoff should be applied to tier 3 as well.

We thank the Reviewer for highlighting this important point. We agree that in a standard two-stage discovery and replication study design, the Bonferroni adjustment should be based on the number of significant signals from discovery that is tested in the replication. We had initially considered this approach but chose the current tiered approach based on a number of factors:

First, we had initially considered performing a standard meta-analysis between UK Biobank and FinnGen datasets and using the Bonferroni adjustment of the total number of tests. However, it was not possible to reliably map the phenotypes between UK Biobank and FinnGen on a large-scale due to different classification schemes.

Second, we had noticed that if we only focus on the sequential two-stage design, then we would be ignoring strong causal relationships observed in FinnGen that passed Bonferroni adjustment but may only be nominally associated in UK Biobank. Although not as strong as Tier 1 findings, we believe that these findings warranted some consideration. This is particularly relevant since differences in the strength of the causal relationship could be attributed to the different populations studied, sample size, different health systems used to measure disease outcomes, differences in statistical power in the MR tests between the two stages (e.g., number of IVs), amongst others.

Third, we wanted to point out that the total adjustment for number of phenotypes tested using Bonferroni is a very conservative adjustment because the multiple EHR phenotypes have varying degrees of redundancy and correlation. We believe the appropriate Bonferroni-adjusted P-value cutoff is somewhere in between the Bonferroni adjustment of total number of phenotypes, and the nominal P-value (no adjustment for number of phenotypes).

Although somewhat unconventional, we came up with this tiered P-value approach to overcome the points mentioned above. We have now included text to further explain our approach and to mention that tier 2 and tier 3 results require further replication and validation.

Manuscript changes:

Lines 266-283: “This presentation is somewhat unconventional and partly arises from the study’s use of three different datasets for instrument selection. In a traditional two-stage discovery and replication design, Bonferroni adjustment is based on the number of significant signals from discovery that is tested in replication. Here, we used three tiers of statistical evidence to present results because a standard meta-analysis between UKB and FinnGen was not possible, given it was not possible to reliably map all phenotypes between the two datasets. Additionally, Bonferroni-significant results in the replication analysis would have been ignored in FinnGen in a sequential two-stage design if they were also only nominally associated in UKB. The three tiers are defined below:”

Lines 441-444: “Due to the weaker statistical evidence supporting these associations, special caution is encouraged when interpreting these results to infer causality, and further replication and validation studies are essential for all Tier 2 and Tier 3 results.”

Lines 498-500: “However, we reiterate that this Tier 3 association was only nominally significant in discovery, while Bonferroni-significant in replication, and future studies are needed to validate the statistical evidence.”

Lines 565-567: “However, caution is still warranted in inferring causality, as MR depends on specific assumptions and the validity of those assumptions must be carefully assessed. Thus, diverse study designs remain necessary to triangulate evidence on the causal effects of plasma TG levels.”

The causal effect of TG to leiomyoma of the uterus is weak, as indicated by both the sub-significant in the replication and the non-significant of MR-PRESSO. Similarly, I would recommend more caution on the weak statistical rigor when interpreting Tier 2 and Tier 3 results.

We agree with the Reviewer. We have now emphasized more caution in interpreting Tier 2 and Tier 3 results. We have also explicitly restated the weaker statistical evidence underlying these results and noted need for future validation. Please see our detailed response to the Comment above.

Manuscript changes:

Lines 498-500: “However, we reiterate that this Tier 3 association was only nominally significant in discovery, while Bonferroni-significant in replication, and future studies are needed to validate the statistical evidence.”

Another methodological choice that might need justification is the use of UKB TG GWAS loci (1,248 SNPs) are the instrument for FinnGen. This may create some subtle interference with the use of UKB as outcomes in the discovery analysis. It may be minor but some justification or at least some discussions of potential limitations should be mentioned. What about the alternative of using GLGC as instruments in replication?

We agree with the reviewer that the use of UKB TG GWAS loci (1,248 SNPs) as instruments for FinnGen outcomes needs additional justification. We now detail this decision in the text as copied below.

Additionally, we now present new data comparing MR results on FinnGen outcomes when selecting TG instruments from UKB GWAS versus GLGC GWAS. Statistical significance after Bonferroni correction was set to 0.05/221, where 221 was the number of disease traits nominally significant in UKB that were tested in FinnGen. We note that the results were fairly consistent. All Tier 1 results remained Bonferroni significant, whether using TG SNPs from UKB or GLGC. Though statistical significance decreased for the remaining diseases of interest, the direction of causality remained consistent, and three disease traits remained significant (hypertension, aortic aneurysm, and alcoholic liver disease). These results support that instrumenting TG using 1,248 SNPs from UKB might carry more power than the 141 SNPs from GLGC, allowing for the detection of associations in our initial replication analysis using UKB for exposures and FinnGen for outcomes. We now include this analysis in the text and include the figure below, as well as its underlying data, as supplementals (Supplementary File 5).

Manuscript changes:

Lines 229-236: “We selected UKB TG GWAS loci as the instruments for replication on FinnGen outcomes, rather than GLGC TG GWAS loci, to diversify the source of TG instruments and mitigate potential biases associated with one TG GWAS. Moreover, UKB GWAS included a larger study population than GLGC GWAS, providing a greater number of genetic instruments that can together explain more of the variance in plasma TG levels, and thus, greater statistical power and precision. Nevertheless, we also performed the replication analyses using TG instruments from GLGC and included these results as supplemental data (Supplementary File 5).”

For disease outcomes (line 188), UKB European sample size is ~400,000 rather than ~500,000. Can the author clarify the sample size they used?

We thank the reviewer for catching this detail. We have now clarified the sample size of UKB European participants in the Methods section, and we also included the exact sample size of each disease trait GWAS (cases and controls) in Supplementary Figure 1.

Manuscript changes:

Lines 194-201: “Pan-UKB had performed 16,131 GWASs on 7,221 phenotypes in ~420,531 UKB participants of European ancestry using genetic and phenotypic data (PanUKBTeam, 2020). A total of 7,221 total phenotypes had been categorized as “biomarker”, “continuous”, “categorical”, “ICD-10 code”, “phecode”, or “prescription” (PanUKBTeam, 2020). We filtered for outcomes to retain categorical, ICD-10, and phecode types; non-null heritability in European ancestry as estimated by Pan-UKB; and relevance to disease, excluding medications. This yielded 2,600 traits for primary analysis. The exact sample size of each GWAS for each of these traits is provided in Supplementary File 1.”

It would be reassuring to the reader if the TG measurements were measured in a treatment-naïve manner. GLGC accounted for treatment (at least LDL, check paper for TGs; if they didn’t, there must be reason). Maybe not UKB.

We now provide information about whether the lipid measurements were measured in a treatment-naïve manner in the Methods for GLGC and UKB. We also address this point in the discussion section as a potential limitation.

Manuscript changes:

Lines 179-180: “We note that the GLGC GWAS had excluded individuals known to be on lipid-lowering medications.”

Lines 187-188: “We note that the Pan-UKB GWAS study did not exclude participants based on their use of lipid-lowering medications.”

Lines 545-546: “Fifth, the GLGC GWAS used to select instruments for plasma TG levels in discovery had accounted for lipid-lowering treatment, while the UKB GWAS used in replication had not.”

"Phenome-wide MR is a high-throughput extension of MR that, under specific assumptions, estimates the causal effects of an exposure on multiple outcomes simultaneously." - I guess it is more informative to mention the specific assumptions, at least briefly, in the introduction so it is easier for the reader to interpret the results.

We agree with the reviewer that it would be informative to explicitly state the assumptions of Mendelian randomization. We now explicitly state these assumptions in the introduction.

Manuscript changes:

Lines 123-129: “Phenome-wide MR is a high-throughput extension of MR that estimates the causal effects of an exposure on multiple outcomes simultaneously. As in conventional MR, this method uses genetic variants as instrumental variables (IV) to proxy modifiable exposures (Davey Smith & Ebrahim, 2003), and importantly, it relies on three critical assumptions: (1) The genetic variant is directly associated with the exposure; (2) The genetic variant is unrelated to confounders between the exposure and outcome; and (3) The genetic variant has no effect on the outcome other than through the exposure (Davey Smith & Ebrahim, 2003).”

Reviewer #3 (Public Review):

Park and Bafna et al. applied a genetics-based epidemiological approach, the Mendelian randomization analysis (MR), to evaluate the potential causal roles of triglycerides across 2,600 disease traits (i.e., the phenome). In a typical two-sample MR framework, they utilized existing genome-wide association study (GWAS) summary statistics from two separate studies. They are Global Lipids Genetics Consortium (GLGC) and UK Biobank in the discovery analysis, and UK Biobank and FinnGen in the replication analysis. This replication design is a great strength of the study, enhancing the robustness and reproducibility of the results. For the candidate pairs of causal associations, the authors further perform multiple sensitivity analyses to evaluate the robustness of the results to possible violations of assumptions in MR. To disentangle the independent effects of triglycerides from other lipid fractions (i.e., LDL-cholesterol and HDL-cholesterol), the authors performed multivariable MR analysis. In the end, possible causal associations were revealed in three tiers, based on statistical significance in the two-stage analysis. The results support the causal effects of triglycerides in increasing the risk of atherosclerotic cardiovascular disease. They also reveal novel conditions, which are either new treatable conditions (e.g., leiomyoma, hypertension, calculus of kidney and ureter) for repurposing of triglycerides-lowering drug, or possible side effects (e.g., alcoholic liver disease) the triglyceride-lowering treatment should pay special attention to.

The analysis approaches in the paper are standard and solid. The discovery-replication study design is a great strength. Correction for multiple testing was implemented in a conservative way. The sensitivity analyses and MVMR strengthen the robustness of the results. The manuscript is very clearly written and pleasant to read. The limitations were well-presented. The conclusions and interpretations are mostly supported by the data, with one major concern as explained below. But overall, in addition to the specific findings, this study could be an exemplar study for the use of phenome-wide MR in identifying treatable conditions and side effects for most existing drugs.

1) My major concern is about reverse causation. For example, having atherosclerotic cardiovascular disease increases circulating triglycerides. Reverse causation can induce false positives in MR analysis. With the existing data in this study, the authors can perform a reverse MR to evaluate the effect of the 19 disease traits on triglycerides. Ruling out the presence of reserve causation is important to make sure that the current findings are not false positives.

We agree with the reviewer that performing reverse MR would be important to rule out reverse causation. We now present new results using reverse MR, selecting instruments for disease from UKB and instruments for TG from GLGC (i.e., reversing the discovery analysis). We provide an interpretation of these new results in the discussion section and present the underlying data, including the number of genetic variants used, in Supplementary File 6. Please note we could only perform reverse MR on 9 of the 19 diseases of interest, due to insufficient genetic data in GLGC to extract the specific exposure instruments. As expected, we observed significant associations (orange) between “disorders of lipoprotein metabolism” and “hyperlipidemia” with plasma TG levels; however, all other estimates were non-significant, suggesting unidirectional associations for the remaining seven disease traits. We now include the figure below and its underlying data as supplements (Supplementary File 6).

Manuscript changes:

Lines 258-261 “Finally, we performed bidirectional or reverse MR on significant results to examine the potential presence of reverse causation. We selected instruments for each disease as described above from Pan-UKB and instruments for plasma TG levels from GLGC, essentially reversing the discovery stage design using a fixed-effect IVW method.”

Lines 368-373: “Finally, we performed reverse MR to estimate the effects of significant disease traits on plasma TG levels, selecting instruments from UKB and GLGC, respectively. Genetic data were sufficiently available to perform this analysis for 9 of the 19 diseases of interest. These results are presented in Supplementary File 6. Expectedly, “disorders of lipoprotein metabolism” and “hyperlipidemia” had positive effects on plasma TG levels; however, no other examined disease trait showed results suggesting reverse causation.”

Author Response

Reviewer #2 (Public Review):

The molecular characteristics of OCNs in normal or ototoxic conditions are poorly understood before. The strength of this study is that it provides the first single-cell RNA-seq database of OCNs as well as surrounding facial branchial motor neurons. By thoroughly analyzing the database, they found high heterogeneities within OCN populations and identified distinct markers that are enriched in different OCN subtypes. Furthermore, a few previously unknown neuropeptides are revealed, including Npy which is more enriched in the LOC-2 located on the medial side. They also found that neuropeptide expression levels and distributions are subjected to hearing experience and noise exposure. On the other hand, the weakness of the study is that the numbers of single-cell RNA-seq are not sufficient, and may underscore the MOC heterogeneity (Figure 3A). Moreover, the physiological functions of the LOC-2 are not revealed in this study, and no specific markers in one OCN subtype are identified that can predict the morphological or projecting axon features. Those might be addressed in the following studies.

We agree that this study does not allow us to make conclusions about MOC heterogeneity or LOC2 functions. These are certainly interesting avenues to pursue in the future.

Author Response

Reviewer #3 (Public Review):

Although initially discovered as axon guidance molecules in the nervous system, Semaphorins, signaling through their receptors the Neuropilins and Plexins, regulate a variety of cell-cell signaling events in a variety of cell types. In addition, cells often express multiple Semas and receptors. Thus, one important question that has yet to be adequately understood about these important signaling proteins is: how does specificity of function arise from a ubiquitously expressed signaling family?

This study addresses that important question by investigating the role of cysteine palmitoylation on the localization and function of the Neuropilin-2 (Nrp-2) receptor. It was already known that Sema3F signaling through a complex of Nrp-2 and Plexin-A3 regulates pruning of dendritic spines in cortical neurons while Sema3A signals through Nrp-1/PlexA4 to regulate dendritic arborization. The major finding of this study which is well-supported by the data is that palmitoylation of Nrp-2 regulates its cell surface clustering and dendritic spine pruning activity in cortical neurons. Interestingly, palmitoylation of Nrp-1 at homologous residue does not appear to regulate its localization or known neuronal function.

A clear strength of this manuscript is the many techniques that are utilized to examine the question: this study represents a tour de force of biochemical, molecular, genetic, pharmacological and cell biological assays performed both in vitro and in vivo. The authors carefully dissect the function of distinct palmitoylated cysteine residues on Nrp-2 localization and function, concluding that palmitoylation of juxtamembrane cysteines predominates over C-terminal palmityolyation for the Nrp-2 dependent processes assayed in this study. The authors also demonstrate that a specific palmityl transferase (DHHC15) acts on Nrp-2 but not Nrp-1 and is required for Nrp-2 clustering and dendritic spine pruning. These findings are important because they demonstrate one mechanism by which different signaling pathways, even from a related family of proteins, can achieve signaling specificity in the cell.

A minor weakness of the paper is that one would like to see a connection between palmitoylation-dependent cell membrane clustering of Nrp-2 on the cell surface and Nrp-2 regulation of dendritic spine pruning. Although the two phenotypes frequently correlate in the data presented, there are a few notable exceptions: e.g. Nrp-2TCS forms larger clusters in cortical neurons while Nrp-2FullCS is diffuse on the cell surface; both mutants affect spine pruning. In the future, it would also be interesting to know if increased clustering of Nrp-2 was observed at spines that were eliminated, for example. Nonetheless this manuscript represents an important advance in our understanding of synaptic pruning and cellular mechanisms that constrain protein surface localization and signaling pathways.

We agree that the reviewer’s comment on the need to show a direct association between palmitoylation-dependent Nrp-2 clustering on the cell surface and Nrp-2 regulation of dendritic spine pruning is very important. This underscores the need to develop new robust tools that can directly and specifically address the effects of palmitoylation on protein localization and neuronal morphology. For example, an antibody that is specific for palmitoylated Nrp-2, perhaps including site-specific Nrp-2 palmitoylation, would allow for direct visualization of palmitoylated protein localization at subcellular resolution, and if coupled with in vivo imaging, could help address questions related to spine dynamics with respect to Nrp-2 expression and palmitoylation. However, at present we consider this approach an important future direction.

Regarding the Nrp-2 mutants TCS and Full CS, our experiments suggest the existence of a threshold for protein mislocalization beyond which Nrp-2 loses its function. In other words, the defect in protein localization imparted by the mutation of the three juxtamembrane cysteines (TCS Nrp-2 mutant) seems to be sufficient to cause Nrp-2 dysfunction. In addition, as noted above (Reviewer #1), the protein clustering assay is a useful but a more general localization assay; more sophisticated assays need to be developed to investigate palmitoylated proteins when they are mislocalized upon site-specific depalmitoylation, which could provide a more accurate association between a protein’s localization and function.

The reviewer’s idea to look at the localization of Nrp-2 at dendritic spines and correlate this with the fate of spines during postnatal development, including relating to spine maintenance vs elimination, is an excellent suggestion that could link directly Nrp-2 to spine dynamics. To address this, however, again new assays with exogenous Nrp-2 expression will need to be developed, but with very low levels of protein expression to avoid saturation of spines with exogenous tagged-Nrp-2 protein and preserve functional specificity for spine regulation. Alternatively, robust in vivo tagging of ndogenous Nrp-2 protein using CRISPR approaches also provide another avenue to achieve this goal—of note, we are trying this approach but, thus far, we have not been successful in achieving labeling that is robust enough for such experiments.

Author Response

Reviewer #1 (Public Review):

The current study melds computational and docking methods with functional measurements in a systematic approach: first, they analyze the mechanism of inhibitor binding to EAAT2; second, they mutate ASCT to resemble EAAT and show that the general binding pocket and inhibition mechanism are conserved; third, they perform an in silico screen to identify compounds that bind to the WT ASCT binding pocket; fourth, they perform electrophysiological assays showing that this novel compound allosterically modulates ASCT function. This is a complete and comprehensive study with extensive experimental support for the major conclusions. The authors identify an allosteric ASCT inhibitor, and although only partial inhibition is achieved, this study serves as proof-of-concept that this site can be targeted in diverse SLC-1 transporters as an allosteric inhibitory site.

We would like to thank Reviewer #1 for the encouraging comments.

Reviewer #2 (Public Review):

This study set out to explore the nature of a previously described non-competitive and selective inhibitor of the human glutamate transporter, EAAT1 and to explore if this mechanism was conserved across the glutamate transporter family. The non-competitive nature of UCHPH-101 inhibition of EAAT1 has previously been demonstrated with both functional analysis and structures of EAAT1. Here, the authors use detailed electrophysiology analysis to confirm this mechanism of inhibition and to demonstrate that the inhibitor slows the steps of the transport cycle associated with substrate translocation, rather than substrate or sodium ion binding. These findings agree with previous studies that have shown that the compound binds at the interface of the transport and scaffold domains in EAAT1, two domains that are required to move relative to each other for the transport process to occur. UCPH-101 also prevents the transporter from entering an anion-conducting state, which agrees with a recent structure and MD simulations of EAAT1 that demonstrate movements of the transport domain relative to the scaffold domain are required for the EAAT1 to move into the anion-conducting state and support the mechanism of UCPH-101 inhibition confirmed in this study (PMID: 35192345; PMID: 33597752).

While UCPH-101 has been shown to be selective for EAAT1 over other human glutamate transporter subtypes (notably EAAT2 and EAAT3), Dong et al., show that this inhibitor can also reduce transport by another member of the SLC1A family, a neutral amino acid exchanger, ASCT2. Using MD simulations and functional analysis, they show that UCPH-101 acts as a partial, low-affinity inhibitor of ASCT2 and identify two amino acid residues in the binding site that appear to be responsible for the different affinities for EAAT1 and ASCT2. Indeed, when these two residues are changed to the corresponding residues in EAAT1, UCPH-101 becomes a full inhibitor of ASCT2 with an increased affinity.

ASCT2 is a neutral amino acid transporter that can transport glutamine and it is known to be upregulated in several cancers. Thus, finding new compounds and novel ways to inhibit ASCT2 is worthy of investigation. In the last section of this study, the authors conduct a virtual screen of 3.8 million compounds to identify other compounds that could bind to this allosteric site in ASCT2. One compound was identified, and while it had relative low affinity it provides the basis for further exploration of this site.

We would like to thank Reviewer #2 for the thoughtful comments.

Reviewer #3 (Public Review):

Using whole-cell patch-clamp measurements, the authors nicely elaborate the competitive inhibition mechanism of UCPH-101 on EAAT1, concluding that it blocks conformational changes during transmembrane translocation, without inhibiting Na+/glutamate binding. The authors demonstrate that UCPH-101 binds to ASCT2 with strongly reduced affinity. Informed by sequence comparison between EAAT1 and ASCT2, the authors identify a pair of mutations, which makes the putative allosteric-binding pocket (which has been identified by crystallography earlier) in ASCT2 more similar to EAAT1 and restores the inhibitory effect of UCPH-101 in ASCT2. Overall, the electrophysiological experiments appear sound and convincing.

We appreciate the kind words.

Furthermore, using virtual screening against the UCPH-101 binding pocket in ASCT2, the authors identified a novel (non-UCPH-101-like) compound #302 that they experimentally demonstrate to also inhibit ASCT-2. However, the study lacks a detailed investigation of the inhibition mechanism of this compound and it remains unclear if #302 also mediates allosteric inhibition as the authors propose. Furthermore, the study lacks any experimental verification of the assumed binding site of #302.

We agree. Therefore, we have now added more detailed experiments on compound #302 inhibition mechanism, confirming allosteric inhibition (new Fig. G and I).

In addition, the study includes molecular-dynamics (MD) simulations on interactions of UCPH101 with EAAT1 and ASCT2. These simulations intend to support the interpretations of the electrophysiological experiments, i.e., relatively tight interactions of UCPH-101 with EAAT1 and weaker binding to ASCT2, which can be restored using two point-mutations in ASCT-2. Unfortunately, this is a relatively weak part of the study. Due to the lack of any convergence analysis, the statistical significance of the drawn conclusions remains unclear. Furthermore, since it is not reported how UCPH-101 has been parameterized, the chemical accuracy of these models is unclear.

We now add information on the UCPH-101 parametrization protocol, and we have extended the time of MD simulations. Also, we have created additional trajectories for the atom distances between amino acid substrate and ASCT2 side chain in the substrate binding site, providing another data point on convergence in the substrate binding site, which should be unaffected by UCPH-101 binding, according to the experimental data.

Author Response

Reviewer #1 (Public Review):

In this study, the protein composition of exocytotic sites in dopaminergic neurons is investigated. While extensive data are available for both glutamatergic and GABA-ergic synapses, it is far less clear which of the known proteins (particularly proteins localized to the active zone) are also required for dopamine release, and whether proteins are involved that are not found in "classical" synapses. The approach used here uses proximity ligation to tag proteins close to synaptic release sites by using three presynaptic proteins (ELKS, RIM, and the beta4-subunit of the voltage-gated calcium channel) as "baits". Fusion proteins containing BirA were selectively expressed in striatal dopaminergic neurons, followed by in-vivo biotin labelling, isolation of biotinylated proteins and proteomics, using proteins labelled after expression of a soluble BirAconstruct in dopaminergic neurons as reference. As controls, the same experiments were performed in KO-mouse lines in which the presynaptic scaffolding protein RIM or the calcium sensor synaptotagmin 1 were selectively deleted in dopaminergic neurons. To control for specificity, the proteomes were compared with those obtained by expressing a soluble BirA construct. The authors found selective enrichments of synaptic and other proteins that were disrupted in RIM but not Syt1 KO animals, with some overlap between the different baits, thus providing a novel and useful dataset to better understand the composition of dopaminergic release sites.

Technically, the work is clearly state-of-the-art, cutting-edge, and of high quality, and I have no suggestions for experimental improvements.

We thank the reviewer for this summary and for pointing out the high quality of the work.

On the other hand, the data also show the limitations of the approach, and I suggest that the authors discuss these limitations in more detail. The problem is that there is very likely to be a lot of non-specific noise (for multiple reasons) and thus the enriched proteins certainly represent candidates for the interactome in the presynaptic network, but without further corroboration it cannot be claimed that as a whole they all belong to the proteome of the release site.

We fully agree with the reviewer. Most importantly, we have changed the final section from “Conclusions” to “Summary of conclusions and limitations” (lines 501-518) to summarize the limitations with equal weight to the conclusions. In the revised manuscript, we also included many specific additional points in this respect throughout the discussion and the results: many hits could be noise (lines 458, 478-479), thresholding affects the inclusion of proteins in the release site dataset (lines 208-215), the seven-day time window could deliver interactors from the soma to the synapse (lines 493-495), specific oddities (for example histones, lines 482-485), iBioID does not deliver an interactome per se but is simply based on proximity (lines 505-508), and several more. We also clearly state that each specific hit needs follow-up studies (lines 501-503: ” Each protein will require validation through morphological and functional characterization before an unequivocal assignment to dopamine release sites is possible.”), and a similar statement was added on lines 374-375.

Reviewer #2 (Public Review):

The Kaiser lab has been on the forefront in understanding the mechanism of dopamine release in central mammalian neurons. assessing dopamine neuron function has been quite difficult due to the limited experimental access to these neurons. Dopamine neurons possess a number of unique functional roles and participate in several pathophysiological conditions, making them an important target of basic research. This study here has been designed to describe the proteome of the dopamine release apparatus using proximity biotin labeling via active zone protein domains fused to BirA, to test in which ways its proteome composition is similar or different to other central nerve terminals. The control experiments demonstrating proper localization as well as specificity of biotinylation are very solid, yielding in a highly enriched and well characterized proteome data base. Several new proteins were identified and the data base will very likely be a very useful resource for future analysis of the protein composition of synapse and their function at dopamine and other synapses.

We thank the reviewer for this positive assessment of our work.

Major comment:

The authors find that loss of RIM leads to major reduction in the number of synaptically enriched proteins, while they did not see this loss of number of enriched proteins in the Syt1-KO's, arguing for undisrupted synaptome. Maybe I missed this, but which fraction of proteins and synaptic proteins are than co-detected both in the Syt1 and control conditions when comparing the Venn diagrams of Fig2 and Fig 3 Suppl. 2? This analysis may provide an estimate of the reliability of the method across experimental conditions.

We thank the reviewer for proposing to be clear in the comparison of the control and Syt-1 cKODA data. A direct comparison of hit numbers is included on lines 323-324, with 37% overlap between control and Syt-1 cKODA (vs. 15% between control and RIM cKODA). A direct mapping of this overlap is included in Fig. 4E. We think that this direct comparison is complicated by a number of factors, as outlined below, and did our best to include these complications in the discussion, including the last section (lines 501-518).

First, to assess overall similarity, the initial comparison should be to assess axonal proteins identified in the BirA-tdTomato samples. These datasets are quite similar, with 671 (control) and 793 (Syt-1 cKODA) proteins detected, and a high overlap of 601 proteins. We think that this indicates that the experiment per se is quite reproducible. The comparison of the release site proteome between control and Syt-1 cKODA is more complicated. We think that the main point of this comparison is that the overall number of hits is quite similar, with 450 hits in the Syt-1 cKODA proteome and 527 hits in the control proteome, and we now show that this similarity holds across multiple thresholds (lines 298-301; ≥ 1.5: Syt-1 cKODA 602 hits, control 991, ≥ 2.0: 450/527, ≥ 2.5: 252/348). Detailed analyses of overlap reveals that known active zone proteins such as Bassoon, CaV2 channels, RIMs, and ELKS proteins are present in both proteomes, but the overlap is partial and incomplete with 191 proteins found in both proteomes. As discussed throughout and summarized on lines 501-518, the reasons for this partial overlap may be manifold. Trivially, it could be explained by noise or non-saturation (“incompleteness”) of the proteome. We also think that the Syt-1 proteome is not expected to be identical because there is a strong release deficit in these mice. If Syt-1 has a dopamine vesicle docking function (which it does at conventional synapses [4]), this could influence the proteome. We note that protein functions in the dopamine axon are not well established, but inferred from studies of classical synapses.

We have scrutinized the manuscript to not express that the control and Syt-1 cKODA proteomes are identical; we know they are not and discuss the example of α-synuclein specifically (Fig. 6, lines 347-362). Rather, the striking part is that the extent of the proteomes with high hit number, much higher than RIM cKODA, are similar. Specific hits have to be assessed in a detailed way, one hit at a time, in future studies, as expressed unequivocally on lines 501-503).

Reviewer #3 (Public Review):

In this study Kershberg et al use three novel in vivo biotin-identification (iBioID) approaches in mice to isolate and identify proteins of axonal dopamine release sites. By dissecting the striatum, where dopamine axons are, from the substantia nigra and VTA, where dopamine somata are, the authors selectively analyzed axonal compartments. Perturbation studies were designed by crossing the iBioID lines with null mutant mice. Combining the data from these three independent iBioID approaches and the fact that axonal compartments are separated from somata provides a precise and valuable description of the protein composition of these release sites, with many new proteins not previously associated with synaptic release sites. These data are a valuable resource for future experiments on dopamine release mechanisms in the CNS and the organization of the release sites. The BirA (BioID) tags are carefully positioned in three target proteins not to affect their localization/function. Data analysis and visualization are excellent. Combining the new iBioID approaches with existing null mutant mice produces powerful perturbation experiments that lead and strong conclusions on the central role of RIM1 as central organizers of dopamine release sites and unexpected (and unexplained) new findings on how RIM1 and synaptotagmin1 are both required for the accumulation of alpha-synuclein at dopamine release sites.

We thank the reviewer for assessing our paper, for summarizing our main findings, and for expressing genuine enthusiasm for the approach and the outcomes.

It is not entirely clear how certain decisions made by the authors on data thresholds may affect the overall picture emerging from their analyses. This is a purely hypothesis-generating study. The authors made little efforts to define expectations and compare their results to these. Consequently, there is little guidance on how to interpret the data and how decisions made by the authors affect the overall conclusions. For instance, the collection of proteins tagged by all three tagging strategies (Fig 2) is expected to contain all known components of dopamine release sites (not at all the case), and maybe also synaptic vesicles (2 TM components detected, but not the most well-known components like vSNAREs and H+/DA-transporters), and endocytic machinery (only 2 endophilin orthologs detected). Whether or not a more complete collection the components of release sites, synaptic vesicles or endocytic machinery are observed might depend on two hard thresholds applied in this study: (a) "Hits" (depicted in Fig 2) were defined as proteins enriched {greater than or equal to} 2-fold (line 178) and peptides not detected in the negative control (soluble BirA) were defined as 0.5 (line 175). How crucial are these two decisions? It would be great to know if the overall conclusions change if these decisions were made differently.

We agree with the reviewer that the thresholding decisions are important and have now better incorporated the rationale for these decisions in the manuscript.

Two-fold enrichment threshold. As outlined in the response to point 1 in the editorial decision letter, we now include figure supplements to illustrate the composition of the control proteome if we apply 1.5- or 2.5-fold enrichment thresholds (Fig. 2 – figure supplements 1 and 2) instead of the 2.0-fold threshold used in Fig. 2. This leads to more or less hits (991 and 348, respectively) compared to the 2.0-fold threshold (527 hits). It is noteworthy that the SynGO-overlap is the highest with the 2.0 threshold (37% vs. 31% at 1.5 and 33% at 2.5, Fig. 2 – figure supplement 3), justifying this threshold experimentally in addition to what was done in previous work [1,2]. These data are now described on lines 208-215 of the manuscript. When we apply these different thresholds to RIM and Syt-1 cKODA datasets, the finding that RIM ablation disrupts release site assembly persists. The following hit numbers were observed in the mutants at the 1.5, 2.0 and 2.5 enrichment thresholds, respectively: RIM cKODA 268, 198 and 82 hits; Syt cKODA 602, 450 and 252 hits. Hence, the extent of the release site proteome remains much smaller after RIM ablation independent of the enrichment threshold, bolstering the conclusion that RIM is an important scaffold for these release sites. This is included in the revised manuscript on lines 298301.

Undetected peptides in BirA-tdTomato. We did not express this well enough in the manuscript. The undetected proteins were set to 0.5 such that a protein that was detected with a specific bait but not with BirA-tdTomato could be illustrated with a specific circle size, not to determine inclusion in the analyses. If the average peptide count across repeats with a specific bait was 1, this resulted in inclusion in Fig. 2 and consecutive analyses with the smallest circle size. Hence, this decision was made to define circle size. It did not affect inclusion in Fig. 2 beyond the following two points. If one were to further decrease it, this might result in including peptides that only appeared once as a single peptide for some of the experiments, which we wanted to avoid. If one would set it higher (to 1), this artificial threshold would be equal to proteins that were actually detected experimentally multiple times, which we wanted to avoid as well. We have now clarified this on lines 165-167 and lines 1119-1121.

Expected proteins. In general, interpreting our dataset with a strong prior of expected proteins is difficult. The literature on release site proteins specifically characterized for dopamine is limited. We have found Bassoon, RIM, ELKS and Munc13 to be present using 3D-SIM superresolution microscopy [5,6], and we indeed found these proteins in the data as discussed on lines 227-232 and lines 423-445 in the revised manuscript. The prediction for vesicular and endocytic proteins is complicated. Release sites are sparse [5,7], and vesicle clusters are widespread in the dopamine axon, in some cases filling most of the axon (for example, see extended vesicle clusters filling much of the dopamine axon in Fig. 7E of [5]). Furthermore, docking in dopamine axons has not been characterized, and it is unclear how frequently vesicles are docked. Hence, it is not clear whether vesicular proteins should be concentrated at release sites compared to the rest of the axon (the BirA-tdTomato proteome we use for normalization). Similar points can be made for proteins for endocytosis and recycling of dopamine vesicles. Within the dopamine system, it is unclear whether the recycling pathway is close to the exocytic sites. One consistent finding across functional studies is that depletion after activity is unusually long-lasting in the dopamine system, for tens of seconds, even after only mild stimulation [5,8–13]. Hence, endocytosis and RRP replenishment might be very slow in these axons. It is not certain that endocytic factors are predeployed to the plasma membrane, and if they are, it is unclear how close to release sites they would be. As such, we agree with the reviewer that the proteome we describe is a hypothesisgenerator. With the limited knowledge on dopamine release, predictions beyond the previously characterized proteins in dopamine axons are difficult to make.

We thank the reviewer for suggesting to include a better analysis of different thresholds and for giving us the opportunity to clarify the other points that were raised.

Given the good separation of the axonal compartment from the somata (one of the real experimental strengths of this study), it is completely unexpected to find two histones being enriched with all three tagging strategies (Hist1h1d and 1h4a). This should be mentioned and discussed.

We agree with the reviewer and have addressed this point in the manuscript. This could either reflect noise, or there could be more specific reasons behind it. The manuscript now states on lines 482-485: “It is surprising that Hist1h1d and Hist1h4a, genes encoding for the histone proteins H1.3 and H4, were robustly enriched (Fig. 2A). These hits might be entirely unspecific, or their co-purification could be due to biotinylation of H1 and H4 proteins (Stanley et al., 2001). It is also possible that there are unidentified synaptic functions of some of the unexpected proteins.” Ultimately, we do not know why these proteins are enriched, and we state clearly in the section “Summary of conclusions and limitations” that each new hit has to be validated in future studies (lines 501-503).

It would also help to compare the data more systematically to a previous study that attempted to define release sites (albeit not dopamine release sites) using a different methodology (biochemical purification): Boyken et al (only mentioned in relation to Nptn, but other proteins are observed in both studies too, e.g. Cend1).

We agree with the reviewer that Boyken et al, 2013 [14] is an important resource for our paper and for the assessment of the proteomic composition of release sites. We have now introduced links and citations to this paper multiple times (for example, on lines 231, 241, 430, 443, 481) and have expanded the discussion of overlap between these proteomes, including on Cend1 (lines 479482).

We think that a systematic comparison with Boyken et al, 2013 [14] is complicated because (1) so little is known about dopamine release mechanics and (2) because the approach is very different between the two papers. In respect to (1), most prominently, it is not certain how frequently vesicles are docked in the dopamine axon. Only ~25% of the varicosities contain these release sites, and vesicle docking has not been characterized in striatal dopamine axons to the best of our knowledge. Hence, how a docking site at a classical synapse compares to a dopamine release site remains unclear at the outset. For point (2), the key difference is that “within dataset normalizations” are very different in these two studies. In our iBioID dataset, we normalize to soluble proteins defined as proximity to BirA-tdTomato. In ref. [14], the authors express enrichment over “light”, regular synaptic vesicles purified with the same approach. This has a major impact on the proteome that strongly influences a direct comparison of hits, because there are large differences in the normalization. While each normalization makes sense for the respective paper, it complicates direct comparison.

With these points in mind, we have compared hits across both datasets class-by-class. For some classes, the datasets have reasonable overlap for ≥ 2-fold enriched proteins: for example for active zone proteins (3 of 7 hits in [14] appear in our control proteome) and adhesion and cell surface proteins (8 of 18). For other classes, the overlap is limited: for example for nucleotide metabolism/protein synthesis (0 of 16 hits in [14] appear in our dataset) and cytoskeletal proteins (5 of 29). We hope the reviewer agrees, that given these factors, the analyses and discussion needed for a systematic comparison goes beyond the scope of our paper. We have instead added a number of references to Boyken et al., 2013 [14], as outlined above, when direct comparison is meaningful.

Author Response

Reviewer #2 (Public Review):

In this paper, Xiao et al. suggest that PASK is a driver for stem cell differentiation by translocating from the cytosol to the nucleus. This phenomenon is dependent on the acetylation of PASK mediated by CBP/EP300, which is driven by glutamine metabolism. Furthermore, this study showed that PASK interferes/weakens the Wdr5-APC/C interaction, where PASK interacts with Wdr5, resulting in repression of Pax7, leading to stem cell differentiation.

There exist huge interest in maintaining adult stem cells and ES cells in their pluripotent form and the work painstakingly perform several experiments to present that PASK is a good target to achieve that goal.

However, the work on the paper relies mostly on data from C2C12 cells as adult muscle stem cell models, in vivo experimental data, and primary myoblasts from mice. Using these models makes the story contextual in muscle stem cells. Authors have not tried to extrapolate similar claims in other adult stem cell models. This severely restricts the claim to muscle stem cells even though PASK is required for the onset of embryonic and adult stem cell differentiation in general. Their work could be much strengthened if it is also tried on mesenchymal stem cells as these cells are also as metabolically active as muscle cells.

We thank reviewers for their enthusiasm for our studies using PASKi. We have previously shown that PASKi prevented differentiation of 10T1/2 cells into adipogenic lineage (Kikani et al, Elife, 2016). We used stem cells from embryonic (ESC) and adult (MuSCs) origin to show broad application of PASKi in preserving self-renewal independent of stem cell origin. We believe that PASK function to be conversed across different stem cell paradigms; and our results in this manuscript would provide framework to further study PASK in other stem cell paradigms.

Reviewer #3 (Public Review):

This manuscript entitled "PASK relays metabolic signals to mitotic Wdr5-APC/C complex to drive exit from selfrenewal" by Xiao et al presents an interesting story on the role of PASK in the control of muscle stem cell fate by controlling the decision between self-renewal and differentiation. While the biochemistry presented is fairly compelling, the experiments revolving around the myogenic cells are lacking in quality and data.

Major concerns:

1) The isolation method used by this group to isolate muscle stem cells is inappropriate for the experiments used and may contribute to the misinterpretation of some of the results. It is simply a preplating method that results in a very heterogenous cell population in terms of cell type, comprised of numerous fibroblasts. While preplating can be used to isolate muscle stem cells and culture them as myoblasts, it takes days of growth and multiple rounds of passaging that are not used in this paper in order to get a more pure population of myogenic cells. This would also explain the high number of Pax7 negative cells in their primary myoblast experiments (~50% in some conditions) as they are most likely fibroblasts, which the authors could show by staining for fibroblast markers. The increase in Pax7 cells in certain conditions could also simply be due to the loss of contaminating cell types due to the treatment. Every single experiment that was performed on myoblasts must be redone using a more appropriate cell isolation method (i.e. FACS) or by culturing these isolated cells for a much longer period of time to eventually get a more pure cell population. As it stands, none of the data from the primary myoblast experiments are trustworthy.

We agree – and thus, we have reproduced our results using two different methods of purifying MuSCs from mice, as indicated above. We took care to stain each isolation method with vimentin (a marker for fibroblasts) to ensure the purity of our preparation. Data are included in the Essential revisions section.

2) The authors possess a genetic mouse model where PASK is knocked out. However, the mouse model is never described and the paper that is referenced also does not describe it. Please detail your mouse model.

3) The majority of experiments are performed on C2C12 cells. While C2C12s are adequate for biochemistry and proof of concepts, when it comes to biological significance primary myoblasts should be used. While the authors try to explain this use by claiming that primary myoblasts undergo precocious differentiation that can be avoided by using an appropriate growth media (F10, 20% FBS, 1% P/S, 5ng/mL of bFGF).

Kindly see the response for this comment in the Essential revision section.

4) The authors possess a genetic mouse model, yet performed RNA-Seq on C2C12 myoblasts that were either untreated or treated with a PASK inhibitor. It would be much more informative and valuable to sequence the primary myoblasts from WT and PASK KO mice, thereby providing a more biologically relevant model.

We used C2C12 for several reasons for initial transcriptome analysis using PASKi and validated the results from that analysis in primary myoblasts. (1) C2C12 cells are an excellent model for performing biochemical pathway characterization, including discovering new substrate targets for PASK, finding PASK interacting partners, and measuring the biochemical activity of PASK under various conditions. Thus, it would form the basis for a longer-term study of the signaling functions of PASK in one cell system (myoblasts), which can be validated and compared with the primary cell system. (2) PASKi treatment can acutely inhibit PASK catalytic activity without the genetic loss of its protein level. For many enzymatic proteins, catalytic inhibition could have a different biological effect compared with genetic loss of protein (Weiss et al.; Nat Chem Biol. 2007 Dec; 3(12): 739–744.). Thus, we chose the PASKi and C2C12 myoblasts system to study the kinase activitydependent effect on the myoblast transcriptome. However, throughout the manuscript, we used PASKi, PASK siRNA, and PASKKO primary cells to cross-validate all our data. We believe the conditional loss of PASK in MuSCs specific manner will be a great model to repeat the RNA-seq analysis in the future and compare the data obtained with PASKi in cultured myoblasts.

5) The KO mouse model is rarely used and the cells isolated from it would be very useful in determining the biological role of PASK in muscle cells. The authors should isolate WT and KO cells and perform basic muscle functional experiments such as EDU incorporation for proliferation, and fusion index for differentiation to see whether the loss of PASK has an effect on these cells.

We have published the characterization of myogenesis phenotype of PASKKO model in our previous manuscript (Kikani et al, 2016). Thus, we erred by not redoing those experiment in the previous version. We have now reproduced those results and markedly extended the chacterization of PASKKO cells in vitro, including BrdU incorporation, myogenesis, Pax7 heterogeneity, Myogenin expression and PASK subcellular distribution using WT cells. We have also characterized regeneration phenotype of PASKKO mice. We thank the reviewer for helping strengthen the biological context of our manuscript.

6) The authors never look at quiescent muscle stem cells and early activated muscle stem cells in terms of PASK protein expression and dynamics. The authors should isolate EDL myofibers and stain for PASK and PAX7 at 0, 24, 48, and 72-hour post isolation. This would allow the authors to quantify the changes in PASK expression and cell localization, as well as confirm the number of muscle stem cells in WT and KO mice, during quiescence and during the process of muscle stem cell activation, proliferation, and differentiation in a near in vivo context.

As described in Figure 1-figure supplement 2A, PASK is not expressed in quiescent MuSCs. Therefore, we do not anticipate a functional role of PASK in initial activation of QSC. We do not propose that PASK plays a role in the maintenance of the QSC state or the exit and initial activation of MuSCs following muscle injury. PASK is transcriptionally activated in proliferating myoblasts during regeneration (Kikani et al, elife 2016) and upon isolation of MuSCs (Figure S1D). Therefore, we specifically focus on studying the biochemical functional role of PASK signaling in activated (proliferating) myoblasts isolated from mice or during early regeneration. We have ongoing studies examining the precise temporal kinetics of PASK transcription regulation in Pax7+ MuSCs as they are activated, and to identify its upstream transcriptional regulators. However, we respectfully suggest that these avenues are outside of the purview of this current manuscript that specifically explores the metabolic pathway that establishes progenitor population from activated myoblasts.

7) Contrary to their claim, MyoD is not a stemness/self-renewal gene.

We agree, and have corrected the text.

8) The authors state that PASK is necessary for exit from self-renewal and establishment of a progenitor population, but this is a vast overstatement. In the genetic KO mouse model, the mice are able to regenerate their muscle after injury, therefore PASK cannot be a necessary protein for the formation of progenitor cells.

During the muscle regeneration, we observed a significant inhibition of the early regenerative response in PASKKO mice, marked by severely reduced levels of eMHC. Concomittantly, we observed increased numbers of Pax7+ MuSCs at Day 5 of regeneration compared with WT muscles. We have extensively shown requirement of PASK for myogenin induction in vitro and in vivo (Kikani et al, 2016, Kikani et al, 2019). Based on these evidence, we propose that PASK is necessary for the exit from Pax7+ self-renewing stem cells and generation of Myog+ committed progenitor populations.

9) In numerous figure panels, the y-axis represents the # of cells, rather than a percentage or ratio. This is uninformative as the number of cells will never be the same between conditions and experiments. These panels need to be replaced with a more appropriate y-axis.

We have updated the axes to % cells where appropriate.

Author Response

Reviewer #1 (Public Review):

[…] Overall, the results from these analyses are convincing and valuable, but still do not seem to be a big leap from their Unger 2021 paper […]. The methodology that they established should be described more clearly so that it can be shared with the research community. For example, they say cells how many donors were recruited for this experiment? are there differences in efficiency in B cell differentiation by individual?

Also, it would be important to assay for antibodies in the culture media. How would you suggest to improve the culture system to be used to model diseases?

We appreciate the reviewer's queries and the points raised. In response to the first set of comments, the reviewer has correctly observed that the methodology of the assay itself as employed in this paper is not new or superior to our previously published data in (Unger et al., Cells 2021), where we described a minimalistic in vitro system for efficient differentiation of human naive B cells into antibody-secreting cells (ASCs). However, the current study aims to elucidate a comprehensive evaluation of the phenotype of the cells in the in vitro system and their relationships in potential differentiation pathways. In addition, we aimed to elucidate how the detailed gene expression profiles of the differentiating cells in vitro compare to in vivo observed counterparts. In this way, we were able to uncover an antibody secreting cell phenotype in vivo that was not observed before and could only be uncovered due to our full transcriptome knowledge of these cells. In addition, we present novel findings that demonstrate that this culture system not only enables efficient ASCs generation but also recapitulates the entire in vivo B cell differentiation pathway, as evidenced by the presence of germinal-center (GC)-like and pre-memory B cells in the culture. These results have not been previously reported in the literature for human B cells in culture and represent a significant contribution to the field of human B cell biology.

In regards to the reviewer's inquiry about the cell culture protocol, its reproducibility, donors variability, and additional experimental applications, we refer to three additional recent publications from our group that have adopted the same in vitro B cell differentiation system and have provided extensive analysis of the immunoglobulin production, intracellular signaling pathways, as well as comparison with other culture systems in the field (Marsman et al., Cells 2020; Marsman et al., Eur. J. Immunol. 2022; Marsman et al., Front. Immunol. 2022). On top pf this, we now realize that the section that describes the culture system (MATERIAL AND METHODS - “In vitro naive B cell differentiation cultures”) was a bit too concise and we thank the reviewer for mentioning it. We have extended now on it and corrected an inconsistency at lines 125-127: “After six days, activated B cells were collected and co-cultured with 1 × 104 9:1 wild type (WT) to CD40L-expressing 3T3 cells that were irradiated and seeded one day in advance (as described above), together with IL-4 (100 ng/ml) and IL-21 (50 ng/ml; Invitrogen) for five days.”

As for the application of our in vitro system in disease modeling, as requested by the reviewer, this would require modifying the culture conditions to mimic the disease-specific biology background (if known). For instance, by inhibiting or enhancing specific transcriptional pathways that are known to be associated with the disease in question. However, it would also require the presence of antigen-specific B cells in the pool of naive B cells included in the culture, which can be difficult to achieve due to their low frequency. Alternatively, the system could be used to study antigen-specific recall responses using antigen-specific memory B cells as starting material. Our group has evaluated this approach in a recent publication (Marsman et al., Front. Immunol 2022).

[..] B cell differentiation may also influence to cell cycle regulation. Rather than normalize its effect, can authors analyze effect of cell cycle in B cell differentiation? [...]

We very much agree with the reviewer and know that the cell cycle plays a significant role in B cell differentiation output trajectories (Zhou et al, Front Immunol. 2018; Duffy et al., Science 2012). Preparing the manuscript, we have in fact performed a parallel analysis in which we compared both cell cycle regressed- and not cell cycle regressed-based clustering and marker gene selection. Concerning the clustering, other clusters were obtained using the not cell-cycle-regressed dataset compared to the cell-cycle-regressed dataset (figure below). However, when overlaying the clusters obtained with the cell cycle-regressed dataset, the extra clusters were the same cell population but now split based on cycling and not cycling cells: cluster 2 is now divided into the cycling cluster “c”, and the not-cycling cluster “d” while cluster 4 and 5 are now divided into the cycling clusters “e” and the not-cycling cluster “f”. A comprehensive examination of the expression of the top 50 genes associated with antibody-secreting cells in the (non)cycling clusters 4 and 5 reveals that these genes are expressed at a higher level in (non)cycling cluster 5 as compared to cluster 4. This suggests that the cells within cluster 5 are more advanced in their differentiation, regardless of their cell cycle state. This finding has led us to the decision to present the data that has undergone cell cycle regression in the manuscript. Should the reviewer so desire, we are very willing to include additional supplementary figures to the manuscript that include the un-regressed representation.

Figure legend: A-C) UMAP projection of single-cell transcriptomes of in vitro differentiated human naive B cells without cell cycle regression. Each point represents one cell, and colors indicate graph-based cluster assignments identified without cell-cycle regression (A), with cell cycle regression (B) or with cell cycle regression and additional subdivision in cycling and not cycling cells (C). D) Dotplot showing the top 50 differentially expressed genes in cycling and not-cycling cells from cluster 4 and 5. Point size indicate percentage of cell in the cluster expressing the gene, color indicates average expression

Author Response

Reviewer #1 (Public Review):

Doostani et al. present work in which they use fMRI to explore the role of normalization in V1, LO, PFs, EBA, and PPA. The goal of the manuscript is to provide experimental evidence of divisive normalization of neural responses in the human brain. The manuscript is well written and clear in its intentions; however, it is not comprehensive and limited in its interpretation. The manuscript is limited to two simple figures that support its concussions. There is no report of behavior, so there is no way to know whether participants followed instructions. This is important as the study focuses on object-based attention and the analysis depends on the task manipulation. The manuscript does not show any clear progression towards the conclusions and this makes it difficult to assess its scientific quality and the claims that it makes.

Strengths:

The intentions of the paper are clear and the design of the experiment itself is simple to follow. The paper presents some evidence for normalization in V1, LO, PFs, EBA, and PPA. The presented study has laid the foundation for a piece of work that could have importance for the field once it is fleshed out.

Weakness:

The paper claims that it provides compelling evidence for normalization in the human brain. Very broadly, the presented data support this conclusion; for the most part, the normalization model is better than the weighted sum model and a weighted average model. However, the paper is limited in how it works its way up to this conclusion. There is no interpretation of how the data should look based on expectations, just how it does look, and how/why the normalization model is most similar to the data. The paper shows a bias in focusing on visualization of the 'best' data/areas that support the conclusions whereas the data that are not as clear are minimized, yet the conclusions seem to lump all the areas in together and any nuanced differences are not recognized. It is surprising that the manuscript does not present illustrative examples of BOLD series from voxel responses across conditions given that it is stated that it is modeling responses to single voxels; these responses need to be provided for the readers to get some sense of data quality. There are also issues regarding the statistics; the statistics in the paper are not explicitly stated, and from what information is provided (multiple t-tests?), they seem to be incorrect. Last, but not least, there is no report of behavior, so it is not possible to assess the success of the attentional manipulation.

We appreciate the reviewer’s feedback on providing more information so that the scientific quality of our work can be assessed. We have now added a new figure including BOLD responses in different conditions, as well as how we expected the data to look and the interpretations. To provide extra evidence for data quality and reliability, we have included BOLD responses of different conditions for odd and even runs separately in the supplementary information.

In order to avoid any bias in presentation, we have now visualized the results from all areas with the same size and in a more logical order. However, we have also modified all results to include only those voxels in each ROI that were active for the stimuli presented in the main task based on the comment of one of the reviewers. According to the current results, there is no difference in the efficiency of the normalization model in different regions, which we have reported in the results section.

Regarding the statistics, we have corrected the problem. We have performed ANOVA tests, have corrected all results for multiple comparisons, and have added a statistics subsection in the methods section to explicitly explain the statistics.

Finally, we have added the report of the reaction time and accuracy in the results section and the supplementary information. As stated, average performance was above 86% in all conditions, confirming that the participants correctly followed the instructions and that the attentional manipulation was successful.

We hope that the reviewer would find the manuscript improved and that the new analyses, figures, and discussions would address the reviewer’s concerns.

Reviewer #2 (Public Review):

My main concern is in regards to the interpretation of these results has to do with the sparseness of data available to fit with the models. The authors pit two linear models against a nonlinear (normalization) model. The predictions for weighted average and summed models are both linear models doomed to poorly match the fMRI data, particularly in contrast to the nonlinear model. So, while I appreciate the verification that responses to multiple stimuli don't add up or average each other, the model comparisons seem less interesting in this light. This is particularly salient of an issue because the model testing endeavor seems rather unconstrained. A 'true' test of the model would likely need a whole range of contrasts tested for one (or both) of the stimuli, Otherwise, as it stands we simply have a parameter (sigma) that instantly gives more wiggle room than the other models. It would be fairer to pit this normalization model against other nonlinear models. Indeed, this has been already been done in previous work by Kendrick Kay, Jon Winawer and Serge Dumoulin's groups. So far, may concern above has only been in regards to the "unattended" data. But the same issue of course extends to the attended conditions. I think the authors need to either acknowledge the limits of this approach to testing the model or introduce some other frameworks.

We thank the reviewer for their feedback. We have taken two approaches to answer this concern. First, we have included simulations of neural population responses to attended and unattended stimuli. The results demonstrate that with our cross-validation approach, the normalization model is only a better fit if the computation performed at the neural level for multiple-stimulus responses is divisive normalization. Otherwise, the weighted sum or the weighted average models are better fits to the population response when the neurons respectively sum or average responses. These results suggest that the normalization model provides a better fit to the data because the underlying computation performed by the neurons is divisive normalization, not because of the model’s non-linearity.

In a second approach, we tested a nonlinear model, which was a generalization of the weighted sum and the weighted average models with an extra saturation parameter (with even more parameters than the normalization model). The results demonstrated that this model was also a worse fit than the normalization model.

Regarding the reviewer’s comment on testing for a range of contrasts, as we have emphasized now in the discussion, here, we have used single-, multiple-, attended- and unattended-stimulus conditions to explore the change in response and how the normalization model accounts for the observed changes in different conditions. While testing for a range of contrasts would also be interesting, it would need a multi-session fMRI experiment to test for a range of contrasts with isolated and paired stimulus conditions in the presence and absence of attention. Moreover, the role of contrast in normalization has been investigated in previous studies, and here we added to the existing literature by exploring responses to multiple objects, and investigating the role of attention. Finally, since the design of our experiment includes presenting superimposed stimuli, the range of contrasts we can use is limited. Low-contrast superimposed stimuli cannot be easily distinguished, and high-contrast stimuli block each other.

We hope that the reviewer would find the manuscript improved and that the new models, simulations, analyses, and discussions would address the reviewer’s concerns.

Reviewer #3 (Public Review):

In this paper, the authors model brain responses for visual objects and the effect of attention on these brain responses. The authors compare three models that have been studied in the literature to account for the effect of attention on brain responses to multiple stimuli: a normalization model, a weighted average model, and a weighted sum model.

The authors presented human volunteers with images of houses and bodies, presented in isolation or together, and measured fMRI brain activity. The authors fit the fMRI data to the predictions of these three models, and argue that the normalization model best accounts for the data.

The strengths of this study include a relatively large number of participants (N=19), and data collected in a variety of different visual brain regions. The blocked design paradigm and the large number of fMRI runs enhance the quality of the dataset.

Regarding the interpretation of the findings, there are a few points that should be considered: 1) The different models that are being studied have different numbers of free parameters. The normalization model has the highest number of free parameters, and it turns out to fit the data the best. Thus, the main finding could be due to the larger number of parameters in the model. The more parameters a model has, the higher "capacity" it has to potentially fit a dataset. 2) In the abstract, the authors claim that the normalization model best fits the data. However, on closer inspection, this does not appear to be the case systematically in all conditions, but rather more so in the attended conditions. In some of the other conditions, the weighted average model also appears to provide a reasonable fit, suggesting that the normalization model may be particularly relevant to modeling the effects of attention. 3) In the primary results, the data are collapsed across five different conditions (isolated/attended for preferred and null stimuli), making it difficult to determine how each model fares in each condition. It would be helpful to provide data separately for the different conditions.

We thank the reviewer for their feedback.

Regarding the reviewer’s concern about the number of free parameters, we have introduced a simulation approach, demonstrating that with our cross-validation approach, a model with a higher number of parameters is not a good fit when the underlying neural computation does not match the computation performed by the model. Moreover, we have now included another nonlinear model with 5 parameters that performs worse than the normalization model. Besides, we have used the AIC measure in addition to cross-validation for model comparison, and the AIC measure confirms the previous results.

Regarding the difference in the efficiency of the normalization model across conditions, after selecting the voxels that were active during the main task in each ROI (done according to the suggestion of one of the reviewers to compensate for the difference in size of localizer and task stimuli), we observed that the normalization model was a better fit for both attended and unattended conditions. However, since the weighted average model results were also close to the data in unattended conditions, we have discussed the unattended condition separately and have discussed the relevance of our results to previous reports of multiple-stimulus responses in the absence of attention.

Finally, concerning model comparison for different conditions, we have calculated the models’ goodness of fit across conditions for each voxel. The reason for calculating the goodness of fit in this manner was to evaluate model fits based on their ability in predicting response changes with the addition of a second stimulus and with the shifts of attention. Since correlation is blind to a systematic error in prediction for all voxels in a condition, calculating the goodness of fit across voxels would lead to misinterpretation. We have now included a figure in the supplementary information illustrating the method we used for calculating the goodness of fit.

We hope that the reviewer would find the manuscript improved and that the new analyses, simulations, figures, and discussions would address the reviewer’s concerns.

Author Response

Reviewer #1 (Public Review):

In this manuscript, Braet et al provide a rigorous analysis of SARS-CoV-2 spike protein dynamics using hydrogen/deuterium exchange mass spectrometry. Their findings reveal an interesting increase in the dynamics of the N-terminal domain that progressed with the emergence of new variants. In addition, the authors also observe an increase in the stabilization of the spike trimeric core, which they identify originates from the early D614G mutation.

Overall this is a timely and interesting exploration of spike protein dynamics, which have so far remained largely unexplored in the literature.

What I find a bit missing in this manuscript is a link between how the identified changes in protein dynamics lead to increased viral fitness. While there are some possibilities listed in the discussion, I think these should be elaborated upon further. In addition, it should also be discussed how understanding the changes in the spike protein dynamics could have implications for the development of small molecule inhibitors for the virus.

We have included information in the introduction and conclusion to make the connection more clearly between our observations, function, and viral fitness of spike protein. We have also connected specific mutations to observed function. We have re-organized the discussion for increased clarity and to improve the correlation of our observations to viral fitness.

Reviewer #2 (Public Review):

The study systematically looks at dynamic differences across variants longitudinally and the authors appropriately only limit their analyses to peptides that are conserved across the different variants.

There are some concerns listed below, particularly related to the ensemble heterogeneity that is reported and need considerable revision.

1) The authors explain that cold-temperature treatment of the S trimer ectodomain constructs has been shown to lead to instability and heterogeneity. They also show this with a comparison of untreated vs. 3-hour 37 ℃ treated samples. I'm confused as to why "During automated HDXMS experiments protein samples were stored at 0 ℃". Will this not cause issues in protein heterogeneity, where the longer the protein sits at 0 ℃ the more potential heterogeneity there will be, and thus greatly confound the analysis?

We thank the reviewer for highlighting this point. We have carefully examined and reevaluated our analysis of both wild -type and variant spike HDXMS. During automated HDXMS experiments, protein samples are indeed maintained at 0 ℃, in between runs and replicates for fixed periods of time (4 h per replicate). In the case of WT S, we did observe conformational heterogeneity between replicates (Figure 2- figure supplement 6), as correctly pointed out by the reviewer. We have repeated analysis of WT S without 0 ℃ incubation in automated HDXMS experiments. In the revised manuscript, Figure 2 shows the more homogenous conformation of WT S, when not incubated at 0 ℃ in between replicates. Extension of these analyses to D614G (Figure 2- figure supplement 7) and all subsequent variants that each contain D614G, showed almost no conformational heterogeneity.

We have included a detailed description (lines 237-244) of the revised manuscript to describe in greater detail effects of 0 ℃ incubation on HDXMS of WT S.

Our results revealed that WT S was more sensitive to cold denaturation as described previously [Costello et al. 2021] where the reported half-life for conformational transitions after 0 ℃ incubation was 17 hours. We had not anticipated conformational heterogeneity revealed by deuterium exchange when using an automated HDXMS setup. Upon further review, we see a significant ensemble shift in trimer stalk peptides for the second and third replicates which sat at 0 ℃ for 4 and 8 hours respectively. This is only observed in WT but not any of the other variant S samples. We thank the reviewer for pointing this out and strengthening our conclusions.

2) The authors presume that the bimodal spectra that are observed reflect EX1 kinetics, however, there can be multiple reasons for an apparent bimodal distribution in the spectra. I agree that some of the spectra indicate that more than a single species is present, but what the two populations represent is murky. In Figure 2D, the apparent size of the highly deuterated population gets larger going from the 60 sec to the 600-sec spectra, as expected for an EX1 transition. However, in Figure 3D the WT highly deuterated population gets smaller going from the 60-sec to the 600-sec spectra. Were bimodal examples observed beyond those shown in Figure 2?

We agree with the reviewer. The appearance of bimodal spectra in deuterium exchange of S protein peptides in WT S are not a result of EX1 kinetics alone. We have revised the explanation for the presence of the bimodal spectra. These are largely a consequence of automated HDXMS workflows, that included 0° C incubations for short periods of time in between replicates. We report new experiments where we have eliminated 0 °C incubations by incubating at 20 °C between replicates and observed a lot lower conformational heterogeneity.

Consequently, the shifts in bimodal spectra in figure 3D for WT S are also likely a consequence of automated HDX MS experiments with 0 ℃ incubation. We have carried out new experiments without 0 ℃ incubation, and these are shown in a revised figure 3. Even without 0 ℃ incubation, we do see bimodal spectra for certain peptides [figure 2 – S5]. These reflect an ensemble of prefusion and splayed conformations of WT S. Lack of baseline resolution precludes application of HDexaminer to resolve spectral envelopes quantitatively.

3) How were the spectra that appeared broadened analyzed? There is no description of this in the methods, and the only data shown for this is in table 1. The left/right percentages are reported without any description of how they were obtained. Are these solely from a single spectrum? The most alarming issue is that Table 1B reports 9.4% for the right population of the 988-998 peptide, but the corresponding spectra in Figure 3D doesn't seem to have any highly deuterated population at all.

We agree with the reviewer. We have removed HD examiner analysis of spectral broadening. Some of the spectral broadening was a consequence of 0 ℃ incubation in automated HDX analyses. These have been revised in new supplemental figures for wild -type HDX MS. Baseline resolution precludes effective quantitation of spectral envelopes, Figure 2-figure supplement 5 highlights qualitatively the spectral broadening for the reader’s benefit.

4) The authors state on page 12: "Replicate analysis of stabilized S trimers with incubation at 4C prior to deuterium exchange (see methods) showed a time-dependent reversal of stabilization as reported previously (Costello et al., 2022), most evident at the same peptides." Is this data shown anywhere? If not then it should be included somewhere, possibly in table 1 as I would expect the cold treatment to offset the left/right population sizes.

We note that this statement was misleading and have revised the text. The time-dependent reversal of stabilization has previously been described (Costello et al., 2022 paper) and is not part of this study.

5) The authors state that peptide 899-913 'exhibits a slow conformational interconversion (time scale ~ 15-30 min)'. Where did this estimated rate come from? From the data shown and the limited number of time points, I don't think there is sufficient sampling of this conformational transition to really narrow down the exact timescale, especially since the ratio of left/right populations is so dependent on the pre-treatment of the sample prior to deuterium exchange. (See 1st comment)

We thank the reviewer. The heterogeneity in deuterium exchange is attributable to the variable 0 °C incubation times in our automated HDXMS workflow. We have removed any explanations of conformational interconversion occurring in our experimental timescales.

6) The woods plots presented in the Supporting information: (Figures 2-S4, 2-S5, 3-S4, 4-S2, 5-S2, 6-S2) are not conventional Woods plots. Normally the plots would indicate a global threshold for what is deemed to be significant based on the overall error in the dataset. From what I gather the authors used error within an individual peptide to establish significance for each specific peptide, which would be okay, but the authors don't describe the number of replicates or how the p-value was calculated. I would strongly recommend that the authors instead rely on a hybrid significance testing approach, as described recently: (PMID 31099554). What's really alarming with the current approach is that several of the Woods plots shown have data points found to be significantly different that are right at zero on the y-axis.

We thank the reviewer. We have replaced all of the Woods plots with volcano plots. We have now applied a hybrid significance testing approach as recommended by the reviewer.

7) Table 1: The summary of the peptides with observed bimodal behavior should include data from the replicates, particularly for assessment of how consistent the left/right population sizes are across replicates. Instead of just a percentage, the table should report an average and the standard deviation from the replicate measurements. Furthermore, the table should also include peptides that are overlapping with those presented. Based on Figure 2-figure supplement 1, there are at least two other peptides that cover the 899-913 region. These additional peptides should show a similar trend with bimodal profiles and will be important for showing how reproducible the apparent EX1 kinetics are in the dataset.

All available replicates and overlapping peptides should be analyzed to ensure that these percentages reported are consistent across the data. It is also odd that the authors choose to use the 3+ charge state of the WT, but the 2+ for the D614G mutant. If both charge states were present, then both of them should be analyzed to ensure the population distributions are consistent within different charge states.

We thank the reviewers for their suggestion. We have removed Table 1 since bimodal spectra are not resolvable for quantitation as described previously. We instead show spectra of overlapping peptides in these regions for interpretation by the reader.

We show charge states that provide highest intensity for the peptides (Figure 2-figure supplement 5, Figure 3-figure supplement 3, Figure 4-figure supplement 3, Figure 5-figure supplement 3, Figure 6-figure supplement 3).

8) The method for calculating p-values used to assess the significance of a difference in observed deuterium uptake is not described. The manuscript mentions technical replicates, but no specific information as to how many replicates were collected for each time point. These details should be included as they are also part of the summary table that is recommended for the publication of HDX data.

We have utilized hybrid significance testing as suggested by the reviewers to determine significance as outlined by Hageman et al. We have included this in table S3 and in the text.

Author Response

Reviewer #1 (Public Review):

Major points:

1) How STC1 controls changes in MSCs' ability for hampering CAR-T cell-mediated anti-tumor responses is unclear.

In this study, we demonstrated that the presence of STC1 is critical for MSCs to exert their immunosuppressive role by inhibiting cytotoxic T cell subsets, activating key immune suppressive/escape related molecules such as IDO and PD-L1, and crosstalking with macrophages in the TME. These immunosuppressive functions of MSC could be significantly hampered when the STC1 gene was knockdown. Considering that staniocalcin-1 is glycoprotein hormone that is secreted into the extracellular matrix in a paracrine manner, we would conclude that the role of STC-1 is not to alter the function of MSCs intracellularly. Rather, it facilitates the immunosuppressive capabilities of MSCs through extracellular secretion into the TME as a pleiotropic factor, thus impacting the functioning of T cells, cancer cells and other immune cells.

The reviewer's question is well taken, and we have added the points mentioned above to the Discussion section to ensure a more comprehensive conclusion. Moreover, a recent study published in Cancer Cell, which was suggested by the other reviewer, is consistent with our results. It has provided further mechanistic information on how stanniocalcin-1 impacts immunotherapy efficacy and T cell activation. The reference has been cited and discussed as shown below.

"In this model, activated macrophages or stress signals during CAR-T therapy may prompt MSCs to secret staniocalcin-1 into the extracellular matrix of TME, serving as a pleiotropic factor to negatively impact the function of T cells and stimulate the expression of molecules that inactivate immune responses, ultimately providing an immunosuppressive effect of MSC." (page 22, highlighted). "In line with our study, it was recently reported that stanniocalcin-1 negatively correlates with immunotherapy efficacy and T cell activation by trapping calreticulin, which abrogates membrane calreticulin-directed antigen presentation function and phagocytosis [50]." (Page 20, highlighted)

2) Is ROS important? It is not tested directly.

ROS plays an important role during immune response, which are released by neutrophils and macrophages. Not only do they act as key mediators of the adaptive immune response, but they also have the ability to modulate the activation of B-cells and T-cells. In our study, we suggest that ROS may be involved in NLRP3 inflammasome activation and the expression and secretion of STC1. Although we did not pursue this line of inquiry further as it was beyond the scope of our paper, we have included additional relevant research in Discussion and a reference is provided.

"It has been proved that the expression and secretion of STC1 in multiple cell lines can be stimulated by external stimuli, including cytokines and oxidative stress [26]." (Page 21, highlighted)

3) The changes in CD8 and Treg are not convincing. Moreover, it is not tested how these changes can be elicited by the presence of MSCs.

We have included additional in vivo data to assess the levels of Treg cells and CD8+ in this revised manuscript. This not only confirms the alterations of CD8 and Treg, but also offers additional line of evidence to further analyze the influence of MSCs on CAR-T in vivo. The findings are presented in Figure 4B, and the corresponding discussion can be found on Page 17 (highlighted).

Reviewer #2 (Public Review):

Major points:

1) STC-1 is expressed and secreted by many human cancer cells. This should be discussed in the introduction or discussion with more inter-related background info on both its regulation in cancer cells and secretion pattern into TME. It is important because you state that the STC-1 secreted by MSC has such strong functions, then how about those produced and secreted by cancer cells? Are those also stimulated by macrophages or other components in TME? Do they have possible functions in helping cancer cell to escape the immune surveillance mechanisms?

Thanks for the suggestion. We have added more details about the regulation and secretion of STC-1 in cancer cells (see below). The information is added to both the introduction and discussion (highlighted on pages 4 and 21), and all the above questions are addressed.

"It was proved that STC1 is involved in several oxidative and cancer-related signaling pathways such as NF-κB, ERK, and JNK pathways [26,27]. The expression and secretion of STC1 in cancer tissue can be stimulated by external stimulus including external cytokines and oxidative stress [26]. Under hypoxia conditions, STC1 could be modulated by HIF-1 to facilitate the reprogramming of tumor metabolism from oxidative to glycolytic metabolism [28]. STC1 was also reported to participate in the process of epithelial-to-mesenchymal transition (EMT), which is associated with tumor invasion and the reshape the tumor microenvironment, as well as increasing therapy resistance [29]." (Page 4)

"It has been proved that the expression and secretion of STC1 in multiple cell lines can be stimulated by external stimuli including cytokines and oxidative stress [26]." (Page 21)

2) In Figure 4B, using a single marker of IL-1β to show the immune suppressive capability of MSC in vivo is not sufficient, staining for CD4+ and CD8+ should also be included to demonstrate whether MSC could modulate T cell compositions, which can give more direct evidence about MSC's impacts on CAR-T cell.

The above experiments were done as suggested, and the data were presented in figure 4B. Explanations of the results are shown on page 17 Results section and page 21 Discussion section (highlighted).

3) One of the major risks associated with CAR-T therapy is an excessive immune response that causes cytokine release syndrome. MSCs have been used in clinics as a way to suppress immune response including post-CAR-T. What does the author think about using MSC with STC-1 knockout? Can it still help reduce toxicity while maintaining CAR-T efficacy? This might be a potential application.

This is definitely an interesting idea. Based on the data presented in the current study, it is clear that knockdown of STC-1 would abrogate the immune-suppressive impact of MSC, and therefore affect CAR-T efficacy. However, whether the presence of MSC can help reduce cytokine release syndrome when losing the function of STC-1 requires further study. We agree with the reviewer, and we had briefly discussed this possibility at the very end of the discussion as shown below (Page 22, highlighted).

"… the findings we presented here are no doubt that would have potential clinical applications toward improving the efficiency of CAR-T therapy as well as reducing the excessive toxicity by modulating the level of STC1 in TME".

4) There was a recent study published in Cancer Cell (Lin et al. Stanniocalcin 1 is a phagocytosis checkpoint driving tumor immune resistance. 2021), and they also reported that STC1 negatively correlates with immunotherapy efficacy and patient survival. It should be cited, and in fact, it provided support to the authors' present study with completely different experimental settings.

Thanks for providing this important information. It is an excellent study and consistent with our findings. The reference was added and discussed on page 20 (highlighted) as shown below.

"In line with our study, it was recently reported that stanniocalcin-1 negatively correlates with immunotherapy efficacy and T cell activation by trapping calreticulin, which abrogates membrane calreticulin-directed antigen presentation function and phagocytosis [50]"

Author Response

Reviewer #1 (Public Review):

This theoretical (computational modelling) study explores a mechanism that may underlie beta (13-30Hz) oscillations in the primate motor cortex. The authors conjecture that traveling beta oscillation bursts emerge following dephasing of intracortical dynamics by extracortical inputs. This is a well written and illustrated manuscript that addressed issues that are both of fundamental and translational importance.

We are pleased by the reviewer’s judgement about the importance of the question that we consider and about the presentation of our manuscript.

Unfortunately, existing work in the field is not well considered and related to the present work. The rationale of the model network follows closely the description in Sherman et al (2016). The relation (difference/advance) to this published and available model needs to be explicitly made clear. Does the Sherman model lack emerging physiological features that the new proposed model exhibits?

We view the work of Sherman et al (2016) and ours as complementary. Sherman et al propose a model of a single E-I module, using the terminology of our manuscript, that is much more detailed than ours since it approximately accounts for the layered structure of the cortex using two layers of multi-compartment spiking neurons, each comprising 100 excitatory neurons and 35 inhibitory neurons. This allows a detailed comparison of the model with local MEG signals. We used a much simpler description and only describe the population behavior of local E and I neurons populations in each module. However, contrary to Sherman’s model, this allows us to address the spatial aspect of beta oscillations which is the main target of our work. Our simple description of a local E-I module allows us to consider several hundred E-I modules with a spatially-structured connectivity and to analyze the spatio-temporal characteristics of beta activity. We have now described the relation of our work with Sherman et al (2019) in the discussion section (lines 540-547).

The authors may also note the stability analysis in: Yaqian Chen et al., “Emergence of Beta Oscillations of a Resonance Model for Parkinson’s Disease”, Neural Plasticity, vol. 2020, https://doi.org/10.1155/2020/8824760

We thank the reviewer for pointing out this paper that had escaped our notice. It presents the stability analysis of a single E-I module with propagation delay (and instantaneous synapses). At the mathematical level, the analysis brings little as compared to the much older article of Geisler et al., J Neurophys (2005) that we cite. However, the model specifically proposes to describe beta oscillations in the motor cortex as arising from the interaction between excitatory and inhibitory neurons, as we do. Therefore, we included this reference as well as a reference to the previous work of Pavlides et al., PLoS Comp Biol (2015) where the model was developed.

The model-based analysis of the traveling nature of the beta frequency bursts appears to be the most original component of the manuscript. Unfortunately, this is also the least worked out component. The phase velocity analysis is limited by the small number (10 x 10) of modeled (and experimentally recorded) sites and this needs to be acknowledged.How were border effects treated in the model and which are they?

We thank the reviewer for these points which gave us the opportunity to clarify them and improve our manuscript. As described in Methods: Simulations (line 847 and seq.) and shown in Fig. S2 (Fig. S10 in the original submission), we actually simulated our model on a 24 × 24 grid and did all our measurements in a central 10×10 grid to take into account that the electrode covers only part of the motor cortex. In addition to minimize border effects, we added on each side of the 24×24 grid two rows of E-I modules kept at their (non-oscillating) fixed points of stationary activity, as depicted in Fig. S2. In order to address the concern of the reviewer, and to check that indeed border effects had a minimal impact on our results, we have performed a new set of simulations on a 24×24 grid with periodic boundary conditions. The results are shown in the new supplementary Fig. S9 and are indistinguishable from those reported in the main text and figures. In particular, the proportion of the different wave types and the wave speeds are unaffected by this change of boundary conditions. A paragraph has been added in the revised version (lines 371-378) to discuss this point.

How much of the phase velocities are due to unsynchronized random fluctuations? At least an analysis of shuffled LFPs needs to be performed.

The phase velocities are indeed due to unsynchronized random fluctuations (coming from the finite number of neurons in each of our modules as well as, and more importantly, from the uncorrelated local external inputs). In order to check that the spatial-structure of connectivity was important, we followed the suggestion of the reviewer and also performed a new set of simulations to provide a further test. As proposed by the reviewer, after performing the simulations we shuffled in space the signal of the different electrodes and also did a parallel analysis where we shuffled the signal from different electrodes in the recording. We then reclassified the shuffled simulations/recordings in exactly the same way as the original ones. As shown in the new additional Fig. S16, this resulted in the full elimination of time frames classified as “planar waves” both in the model and in the experimental recordings. Additionally, it little modified the proportion of “synchronized” or “random” episodes which is intuitively understandable since shuffling does not change the nature of these states. In order to further assess the impact of connections between modules, we also decided to suppress them, namely to put their range l to zero. In order to avoid modifying the working point of a local module by this manipulation, we focused on the case without propagation delay. Without long-range connection, the local dynamics of each module is little modified. However, as shown in the new Fig. S18a, synchronization between neighboring modules is strongly decreased and the proportion of the different wave types is entirely changed: synchronized states and planar waves disappear and are replaced by random states. These results are described in two new paragraphs (lines 401-414 and lines 431-435).

Is there a relationship between the localizations of the non-global external input and the starting sites of the traveling waves?

This is also an interesting question that parallels some asked by the other reviewers and which we did our best to address. As described in the “Essential revisions” point 5) above, we aligned all “planar wave events” in space and time with the help of the spatio-temporal phase maps of the oscillations. We did find that planar waves were preceded by an increase in the global synchronization index σp, both in simulations and in experiments. In simulations this increase also corresponded to a shift of the global inputs away from their mean, as depicted in the new Fig. 4 in the main manuscript. However, no significant average spatio-temporal profile of the local inputs emerged when we used these temporal alignments. This is presumably due to the large variability of local inputs that can give rise to planar waves. We have described these results in the new section “Properties of planar waves and characteristics of their inputs”.

In summary, this work could benefit from a widening of its scope to eventually inspire new experimental research questions. While the model is constructed well, there is insufficient evidence to conclude that the presented model advances over another published model (e.g. Sherman et al., 2016).

As described in the “Essential revisions” and the discussion section of the manuscript, our work highlights a number of questions that can (and hopefully will) inspire new experimental research. We also hope that we have clarified above that our model complements Sherman et al.’s model and advances it as far as the spatial aspects of beta oscillations in motor cortex are concerned.

Reviewer #2 (Public Review):

Kang et. al., model the cortical dynamics, specifically distributions of beta burst durations and proportion of different kind of spatial waves using a firing rate model with local E-I connections and long range and distance dependent excitatory connections. The model also predicts that the observed cortical activity may be a result of non stationary external input (correlated at short time scales) and a combination of two sources of input, global and local. Overall, the manuscript is very clear, concise and well written. The modeling work is comprehensive and makes interesting and testable predictions about the mechanism of beta bursts and waves in the cortical activity. There are just a few minor typos and curiosities if they can be addressed by the model. Notwithstanding, the study is a valuable contribution towards developing data driven firing rate.

We really appreciate the positive comments of the reviewer and thank her/him for them. We have done our best to correct the typos and to address the questions raised by the reviewer.

1) The model beautifully reproduces the proportion of different kind of waves that can be seen in the data (Fig 3), however the manuscript does not comment on when would a planar/random wave appear for a given set of parameters (eg. fixed v ext, tau ext, c) from the mechanistic point of view. If these spatio-temporal activities are functional in nature, their occurrence is unlikely to be just stochastic and a strong computational model like this one would be a perfect substrate to ask this question. Is it possible to characterize what aspects of the global/local input fluctuations or interaction of input fluctuations with the network lead to a specific kind of spatio-temporal activity, even if just empirically ?

This is an important question that parallels some asked by the other reviewers and which we did our best to address. As described in the “Essential revisions” paragraph above, we aligned all “planar wave events” either in phase or at their starting time points. We did find that planar waves were preceded by an increase in the global synchronization index σp, both in simulations and in experiments. In simulations this increase also corresponded to a shift of the global inputs away from their mean, as depicted in the new Fig. 4 in the main manuscript. When we used the same alignment to average spatio-temporal local inputs, we did not see the emergence of any significant patterns. This presumably reflects the high variability of local inputs able to produce a planar wave.

Do different waves appear in the same trial simulation or does the same wave type persist over the whole trial? If former, are the transition probabilities between the different wave types uniform, i.e probability of a planar wave to transit into a synchronized wave equal to the probability of a random wave into synchronized wave?

In the same trial simulation, different types of waves indeed successively appear. The curiosity of the reviewer led us to investigate this interesting point. Since time frames classified as random or synchronized are much more numerous than the planar (and radial) wave ones, it is much more probable that a planar wave transits into a synchronized or a random pattern than the reverse process (i.e., synchronized and random patterns preferentially transit into each other). Nonetheless, we considered questions related to the one of the reviewer. What are the states preceding a planar wave event? Given that a planar wave episode is preceded by a random (or synchronous) episode, is it more likely to be followed by a random or by a synchronous event? We actually find that the entry state is prominently a synchronized state. Furthermore, when the entry state is synchronized, the exit state is also synchronized much more often than would be expected by chance. This shows that most often, planar waves are created from an underlying synchronized persistent state. This has been described in the revised manuscript (lines 443-451).

2) Denker et al 2018, also reports a strong relationship between the spatial wave category, beta burst amplitude, the beta burst duration and the velocity (Fig 6E - Denker et. al), eg synchronized waves are fastest with the highest beta amplitude and duration. Was this also observed in the model ?

We had long exchanges with Michael Denker about his analysis since there are some differences between his code and what is described in Denker et al. (2017), possibly because of several typos in the Method section of Denker et al (2017). We have checked that the results of our code agree with his but there are some differences with the results obtained on the available datasets and those reported in Denker et al from other data sets. We have now provided the detailed statistics of the different wave types as obtained by our analysis in the simulation of model SN (Fig. S9) and SN’ (Fig. S11) and in the recordings for monkey L (Fig. S10) and monkey N (Fig. S12). In the recording data, the amplitude and speed of the synchronized and planar waves are comparable and higher than in the radial and random wave types. The duration of synchronized events is longer than the one of planar waves and of the other waves types. Comparable results are obtained in the simulations with nonetheless a few differences: the mean amplitude of planar waves is somewhat larger than those of synchronized states, the hierarchy of duration in the different states is respected but the duration themselves are longer in the simulations than in the recordings (about 40 % for the planar waves and almost two times longer for the synchronized states). We attribute these differences to the fact synchronization is slightly less effective in the recordings than in the model. Long synchronization episodes in the recordings are often cut-off by a few time frames where the synchronization index goes below the threshold value for a synchronized pattern. This happens rarely enough not to affect much the global statistics of the different states but it as a much more visible effect on the measured duration of the synchronized states.

Reviewer #3 (Public Review):

In this manuscript, the authors consider a rate model with recurrently connections excitatory-inhibitory (E-I) modules coupled by distance-dependent excitatory connections. The rate-based formulation with adaptive threshold has been previously shown to agree well with simulations of spiking neurons, and simplifies both analytical analysis and simulations of the model. The cycles of beta oscillations are driven by fluctuating external inputs, and traveling waves emerge from the dephasing by external inputs. The authors constrain the parameters of external inputs so that the model reproduces the power spectral density of LFPs, the correlation of LFPs from different channels and the velocity of propagation of traveling waves. They propose that external inputs are a combination of spatially homogeneous inputs and more localized ones. A very interesting finding is that wave propagation speed is on the order of 30 cm/s in their model which is consistent with the data but does not depend on propagation delays across E-I modules which may suggest that propagation speed is not a consequence of unmylenated axons as has been suggested by others. Overall, the analysis looks solid, and we found no inconsistency in their mathematical analysis.

We thank the reviewer for his comments and for his expert review.

However, we think that the authors should discuss more thoroughly how their modeling assumptions affect their result, especially because they use a simple rate-based model for both theory and simulations, and a very simplified proxy for the LFPs.

In the revised manuscript, we have performed additional simulations to test different modeling assumptions as suggested by the reviewer and discussed further below.

The authors introduce anisotropy in the connectivity to explain the findings of Rubino et al. (2006), showing that motor cortical traveling waves propagate preferentially along a specific axis. They introduce anisotropy in the connectivity by imposing that the long range excitatory connections be twice as long along a given axis, and they observe waves propagating along the orthogonal axis, where the connectivity is shorter range. Referring specifically to the direction of propagation found by Rubino et al, could the authors argue why we should expect longer range connections along the orthogonal axis? In fact, Gatter and Powell (1978, Brain) documented a preponderance of horizontal axons in layers 2/3 and 5 of motor cortex in non-human primates that were more spatially extensive along the rostro-caudal dimension as compared with the medio-lateral dimension, and Rubino et al. (2006) showed the dominant propagation direction was along the rostro-caudal axis. This is inconsistent with the modeling work presented in the current manuscript.

This is an important comment and we thank the reviewer for pointing out these data in Gatter and Powell (1978). Since the experimental data show that planar wave propagation directions are anisotropically distributed, we have tried and investigated what the underlying mechanism of this anisotropy could be in the framework of our model. Anisotropy in connectivity is an obvious possibility. Given our result, and the data of Gatter and Powell, it appears however that it is not the underlying cause of the observed anisotropy direction in the motor cortex (in the framework of our model). We have thus investigated another possibility, namely that the local external inputs are anisotropically targeting the motor cortex, being more spread out along a given axis (lines 510-529 and new Fig. 5g-l). We find that planar waves propagate preferentially along the orthogonal axis. This leads us to conclude that the observed propagation anisotropy could be of consequence of the external input being more spread out along the medio-lateral axis. Data addressing this issue could be obtained using retroviral tracing techniques.

The clarity and significance of the work would greatly improve if the authors discussed more thoroughly how their modeling assumptions affect their result. In particular, the prediction that external inputs are a combination of local and global ones relies on fitting the model to the correlation between LFPs at distant channels. The authors note that when the model parameter c=1, LFPs from distant channels are much more correlated than in the data, and thus have to include the presence of local inputs. We wonder whether the strong correlation between distant LFPs would be lower in a more biologically realistic model, for example a spiking model with sparse connectivity and a spiking external population, where all connections are distant dependent. While the analysis of such a model is beyond the scope of the present work, it would be helpful if the authors discussed if their prediction on the structure of external inputs would still hold in a more realistic model.

This is a legitimate question that we indeed asked ourselves. In a previous work with a simpler chain model, we only considered finite size fluctuations. We found good agreement between our simplified description of finite size fluctuations and simulations of a spiking network with fully connected modules and sparse distance-dependent connectivity. This leads us to believe that our description of finite-size fluctuations is reliable in this setting. Assuming that it is the case, we find that with 104 neurons or more per module finite size noise is not strong enough to replace our local external inputs. Even with 2000 neurons per modules the intrinsic fluctuations the network is very synchronized (new Fig. S15e-g). With 200 neurons per module, the intrinsic fluctuations are strong enough to replace the fluctuating local inputs (Fig. S15a-d) but this is quite a low number. Our description of local noise would have to underestimate the fluctuation in a more sparsely connected network by a significant amount for agreement with the data to be obtained without local inputs. Moreover, it seems to us quite plausible that different regions of motor cortex receive different inputs but, of course, this can only settled by further experiments. Together with the new Fig. S15, we have added a paragraph to address this question in the manuscript (lines 379-400).

Author Response

Reviewer #2 (Public Review):

Weaknesses (major)

1) Adding control groups (sham stimulation) to Experiment 5 and Experiment 8 would be needed to increase confidence that NITESGON's memory-enhancing effects do not depend on sleep but do depend on dopamine receptor activity.

Thank you for highlighting this major weakness within our research; we will be sure to include control groups in future research if we conduct replication studies. Additionally, upon review of your comment, we have addressed the lack of control/sham groups in Experiment 5 and 8 in the Discussion section when acknowledging the limitations of the research.

Please see the newly added text from the Discussion section on pages 21-22 below:

“Moreover, it must also be acknowledged that Experiments 5 and 8 did not include a control-sham stimulation group, thus limiting the interpretation of these two experimental findings. Control-sham stimulation groups would increase our confidence in our findings that NITESGON’s memory-enhancing effects depend not on sleep but on DA receptor activity.”

2) Task order in the interference study in Experiment 4 was randomized during the first visit for task training as well as during the memory test, however, the word-association and spatial navigation tasks used in Experiments 3 and 4 were not counterbalanced during training or memory testing. Thus, the authors cannot rule out the possibility of order effects.

Upon reading your comment and reviewing the paper, we have decided to add a limitations paragraph to the paper which highlights the concern of Experiments 3 and 4 not being counterbalanced during training or memory testing. Additionally, the new section provides an explanation of how not counterbalancing Experiments 3 and 4 introduced the possibility of order effects being present in the results.

Please see the new addition from the Discussion section on page 21 below:

“When interpreting the current findings, it must be considered that some limitations exist within the research; limitations on experimental design are noted below, followed by a discussion of utilizing indirect proxy measures. The task order for Experiment 4 was randomized during the first visit for training and the recall-only memory test 7-days later; however, the word association and spatial navigation task used in Experiments 2 and 3 were not counterbalanced; therefore, the findings of Experiments 2 and 3 could have been impacted by a potential order effect.”

3) It is unclear how Experiment 3 and Experiment 4 differ. Percent of words recalled is the measure of memory performance, however, there is not a clear measure of interference in Experiment 4 (i.e., words recalled during Memory task II that were from Memory task I).

Thank you for highlighting the difficulty in distinguishing the differences between Experiment 3 and Experiment 4. To clarify what the differences are between Experiment 3 and Experiment 4, we explained in Experiment 4’s introductory paragraph that the object-location task used in Experiment 3 was replaced with a Japanese-English verbal associative learning task in Experiment 4.

Please see the paragraph from the Experiment 4 subsection on page 10 below:

“Experiments 2 and 3 revealed both retroactive and proactive memory effects 7-days after initial learning of the two tasks. To further explore if NITESGON is linked to behavioral tagging and evaluate if interference impacts NITESGON as the strong stimulus, Experiment 4 removed the object-location task used in Experiments 2 and 3 and replaced it with a Japanese-English verbal associative learning task similar to the Swahili-English verbal associative task. Considering how memory formation and persistence are susceptible to interference occurring pre-and post-encoding(37-39) and are heavily influenced by commonality amongst the learned and intervening stimuli(40); it is believed that conducting two consecutive, like-minded word-association (i.e., Swahili-English and Japanese-English) tasks will result in one’s consolidation process interfering with that of the other(41). Considering how our previous experiments suggest the effect obtained by NITESGON improves the consolidation of information via behavioral tagging, it is possible that NITESGON on the first task might help reduce the overall interference effect on the second task.”

Additionally, we explained in further detail that comparing the percentage of correctly recalled word pairs on the second task 7-days after learning from the percentage of correctly recalled word pairs on the first task 7-days after learning was done to measure for an interference effect.

Please see the adapted text from the Experiment 4 subsection on page 11 below:

“Upon assessment for a potential interference effect, the active group displayed no significant difference in how many words participants were able to recall between the first and the second task (difference: .76 4.93) (F = .29, p = .60), whereas the sham group demonstrated the first task rendered an interference effect on the second task (difference: 5.16 5.99) (F = 14.11, p = .001).”

Lastly, in the methods section describing how the interference effect was calculated was changed. The newly edited text better explains that the percentage of words pairs learned were subtracted from one another to measure the significance of interference one may have potentially had on the other.

Please see the amended text in the Methods section on page 38 below:

“In addition, an interference effect was calculated by subtracting the percentage of correctly recalled word pairs on the second task 7-days after learning from the percentage of correctly recalled word pairs on the first task 7-days after learning. This number gave a proxy of interference.”

4) In Experiment 5 the learning and test phases for the two sleep groups were conducted at different times of day (sleep group: training at 8pm and testing the next morning at 8am, sleep deprivation group: training at 8am and testing at 8pm) which introduces the possibility of circadian effects between the two groups. Additionally, the memory test occurred at the 12h point for this experiment instead of the 7-day point. Therefore, the authors' conclusions are not addressed by this experiment, and it remains unclear whether the 7-day long-term memory effects of NITESGON are sleep-dependent.

Upon reading your comment and reviewing the paper, we have decided to add a limitations paragraph to the paper which highlights the two sleep groups being conducted at different times of day and the memory test occurring at the 12-hour point as opposed to 7-days after initial learning. In addition to acknowledging these limitations, we have also provided explanations regarding what potential effects are introduced by having the sleep groups learn and test at different times of day, such as circadian effects between the two groups, and the memory tests occurring at 12-hours rather than 7-days after initial learning.

Please see the new addition from the Discussion section on page 21 below:

“Additionally, in Experiment 5, the learning and test phases for the two groups were conducted at different times of day (i.e., sleep group: training at 8 p.m. and testing at 8 a.m., sleep deprivation group: training at 8 a.m. and testing at 8 p.m.), thus introducing the potential for circadian effects between the two groups. Furthermore, the recall-only memory testing occurred at the 12-hour point rather than 7-days later, allowing us to conclude that the observed effect seen 12-hours later was not affected by sleep; however, it remains unclear whether the 7-day long-term memory effects of NITESGON are sleep-dependent.”

Weaknesses (minor)

1) Salivary amylase is being used as a proxy of noradrenergic activity; however, salivary amylase levels increase with stress as well, which impacts memory performance. It would be helpful if the authors addressed this and whether they measured other physiological indicators of stress/sympathetic nervous system activation.

Upon review of your comment, we have edited the paper so that it includes text in the Discussion section that brings attention to the fact that stress can enhance salivary amylase and advises readers that this should be considered when interpreting results. We also add an additional measure which measure pupil size, a measure well-know for sympathetic measure. In addition we add also a VAS score to ask people about their stress levels.

Please see the added new addition from page 22 below.

“Although the use of indirect proxy measures, such as sAA for NA activity and sEBR for DA activity, enabled the tracking of LC-NA activity changes from baseline measurements and demonstrated the potential of an LC-DA relationship, caution must be advised when interpreting results considering these proxy measures are affiliated with limitations, such as being substantially variable, as well as the potential of other brain regions and monoamine neurotransmitters being associated with changes seen in sAA concentration levels(80), an enzyme that is provoked by both central parasympathetic and sympathetic nervous system activation, including acute stress responses(81). Additionally, although sEBR has been increasingly linked to DA, it has been defined as a more viable measure of striatal DA activity(52, 82). At the same time, some evidence suggests that sEBR and DA levels may be unrelated(83, 84), thus requiring further validation as a behavioral proxy measure.”

2) Insufficient details of how the blinding experiment was conducted make it difficult to determine whether participants had awareness or subjective responses during the NITESGON stimulation. Adding physiological indicators of heart rate, skin conductance, and respiration would provide a better indicator of a sympathetic nervous system response. Additionally, a series of randomized stimulation and sham trials delivered to the participant would provide a more objective measure of the detectability of the stimulation.

Thank you for your comment regarding the portion of the experiments that were included to determine the efficacy of the measures taken to ensure the experiments were well blinded. After reviewing the comment and reading over the paper, we were concerned that it was not clear enough to the reader that the efficacy of blinding was determined by having each participant of every experiment complete the same single-answer questionnaire after all NITESGON and testing had been experienced. Therefore, we edited the wording below to elucidate that there was not an individual blinding experiment but that there was a questionnaire for every participant in every experiment to help determine the efficacy of blinding for each experiment and the research.

Please see the text from the Blinding section on pages 17-18 below:

“Blinding. To determine if the stimulation was well blinded, all participants in Experiments 1-7 were asked to guess if they thought they were placed in the active or control group (i.e., what stimulation participants received compared to what participants expected). Our findings demonstrated that participants could not accurately determine if they were assigned to the active or sham NITESGON group in each experiment, suggesting that our sham protocol is reliable and well-blinded (see fig. 8).”

Additionally, please see the text in the Methods section that has been reworded to clarify how the questionnaire of blinding was conducted on page 47 below:

“Blinding: To determine if the stimulation for all experiments was well blinded, all participants who participated in Experiments 1-7 were asked to complete a single-response questionnaire after the conclusion of the NITESGON procedure. Here, participants were asked to guess if they thought they were placed in the active or control group. A χ2 analysis was used to determine if there was a difference between what stimulation participants received compared to what participants expected.”

3) It would be appreciated if the authors could speak to the possible role of the amygdala in the memory-enhancing effects of NITESGON, as this region is a well-known modulator of many types of memory consolidation and is implicated in noradrenergic-related memory enhancement.

Upon consideration of your comment, we added text providing the reader with insight into how NITESGON has activated the amygdala in previous research, similar to the VTA in the current study, and how the LC and amygdala were shown to be activated during emotionally arousing stimuli in another study. Furthermore, we have acknowledged that the amygdala is understood to have modulatory implications in long term memory and how future investigations are needed to establish the amygdala’s role with NITESGON.

Please see the text from the Discussion section on page 20 below:

“Additionally, it is well-known that the amygdala is not the final place of memory storage, but rather has major modulatory influences on the strength of a memory(74). Similar to the VTA in the current study, prior research has shown that the amygdala is activated during NITESGON but ceased post-stimulation; however, NITESGON was not accompanied by a task during the experiment(14). Moreover, a recent fMRI study spotlights the dynamic behavior of the LC during arousal-related memory processing stages whereby emotionally arousing stimuli triggered engagement from the LC and the amygdala during encoding; however, during consolidation and recollection stages, activity shifted to more hippocampal involvement(75). Considering the impact the VTA and amygdala can have on memory, future experimental investigations are needed to establish their role in the memory-enhancing effects of NITESGON.”

Author Response

Reviewer #1 (Public Review):

In this manuscript, Cover et al. examine the role of thalamic neurons of the rostral intralaminar nuclei (rILN) that project to the dorsal striatum (DS) in mice performing a reinforced action sequence task. Using patch-clamp electrophysiology, they find that neurons from the three rILN (CM, PC, and CL) have similar electrophysiological properties. Using fiber photometry recordings of calcium activity from rILN neurons that project to DS, they show that these neurons increase in activity at the first lever press and reward acquisition in mice performing a lever pressing operant task. They additionally demonstrate that this action initiation and reward-related activity exists more generally in mice performing other movements or rewarded tasks. Building on their lab's previous work, the authors further find that by optogenetically activating or inhibiting these rILN-DS neurons, mice will increase or decrease task performance, respectively. Lastly, the authors show that a variety of cortical and subcortical areas have input to rILN-DS neurons suggesting that these neurons might act as an integrator of signals from such areas during task performance.

• The authors beautifully show that the electrophysiological properties of CM, PC, and CL neurons are similar and go on to treat the rILN as one homogenous nucleus for functional fiber photometry recordings and optogenetic stimulations. It seems that these recordings and stimulations were only performed in CL, as indicated in the images (Fig. 2A, 4A). Is this the case, or were CM, PC, and CL neurons sampled? It would be helpful to clarify if DS projecting neurons from all rILN nuclei show the reported action initiation and reward acquisition activity or only CL neurons.

The arrangement of the rILN nuclei presents a technical challenge for experiments attempting to selectively record from or manipulate a single nucleus in this grouping. Based on our findings that the three nuclei do not differ in electrophysiological properties, we approached the in vivo experiments with the intent to target the rILN as a unit. As the reviewer points out, the medial-lateral coordinate for optic fiber placement tended to align above the CL and PC nuclei. However, variability in fiber placement and spread of light within tissue resulted in inclusion of CM activity as well. Given the spread of light through tissue (Shin, et al., 2016; PMID: 27895987), it would be very difficult to confidently determine from histology which photometry recordings were primarily obtained from CL vs PC vs CM neuronal activity. We agree with the reviewer that these three nuclei may differently signal during reward-driven behavior. Our di-synaptic tracing study supports this possibility as it revealed unique afferent connectivity to rILNDS projecting neurons. We now mention this limitation of our approach in the discussion (lines 324 - 330).

• Along similar lines, to what extent of rILN was targeted for optogenetic activation and inhibition? It seems that the authors implanted a total of 4 optic fibers, two on each side (please clarify in methods). What was the reasoning behind this? Please show that only rILN and not PF was activated/inhibited.

We apologize for the confusion in our description of this method. For our optogenetic experiments, we infused viruses at four locations (bilateral striatum and rILN) and implanted only two fibers (bilateral rILN) to selectively target striatally-projecting rILN neurons. We have added clarification on this detail to the methods section.

To prevent inadvertent modulation of Pf neurons, we used virus injection coordinates and volumes that prevented viral spread to the Pf and furthermore implanted the optic fibers in the more rostral regions of the rILN. We histologically confirmed viral expression and fiber placement for all mice and excluded any mice with viral spread to the Pf or off-target fiber placement. We include these criteria for post-hoc exclusion in the methods.

• While AAV1 is becoming a popular tool for transsynaptic labeling, performing confirmatory patch-clamp recordings with optogenetic activation of inputs, would provide better evidence for the synaptic connection between upstream regions, such as ACC and OFC, and rILN neurons.

We agree that electrophysiological confirmation of these inputs to the rILN would complement our tracing study. As our focus for this experiment was to specifically identify inputs that synapse on striatally-projecting rILN neurons, we interrogated putative afferents that were already established to project to the rILN. There are several studies that demonstrate the physiological circuits from some of these afferent projections to the rILN (without di-synaptic specificity), such as the SNr  rILN projection (Rizzi & Tan, 2019; PMID: 31091455).

• In addition, the transsynaptic tracing experiments would benefit from showing the cell count quantifications in CM, PC, and CL. It seems that the authors have already performed this quantification for constructing their diagrams on the right. To make any point about the relative strength of afferent innervation to rILN-DS neurons showing such quantification would be necessary.

Thank you for this suggestion, we now include cell counts for 2 cases per investigated afferent (Supplemental Table S2).

• Why is the injection site for the retrograde cre-dependent tdTomato AAV (Fig. 5 middle left panels) showing expression? Is the cre coming through transsynaptic AAV1 from direct projections of each AAV1 injection site (AAV1 is not supposed to spread across a second synapse)? The diagrams suggest that not all regions (e.g. SUM or SC) have direct projections to DS.

We apologize for this confusion. The tdTomato fluorophore expression observed in the striatum may arise from several possible circuit configurations. To survey just a couple: 1) tdTomato expression in the DS arises from direct projections from the afferent bypassing the thalamus (e.g. ipsilateral ACC→Striatum), which would result in labeled striatal somata (ACC pyramidal neurons delivering AAV1-cre to an MSN, and those local MSN collaterals retrogradely picking up rAAV-DIO-tdtomato) and ACC labeled axon terminals in the DS (ACC interneurons delivering AAV1-cre to DS-projecting ACC pyramidal neurons that pick up rAAV-DIO-tdtomato); 2) terminal projections arising from the labeled rILN neurons shown in the middle-right panels (i.e. ACC→rILN→Striatum).

Reviewer #2 (Public Review):

This manuscript details the role of the rILN to the DS pathway in the onset of operant behavior that promotes the delivery of a reward and in the ultimate acquisition of that reward. The strengths of the paper are in the detailed fiber photometry study that encompasses several behavioral domains that correlate to the signal observed in the rILN to DS pathway. I am especially interested in how the "encoding" shifts across time as the animals refine their behavior both in a temporal sense and in the magnitude of the signal. Further, the authors demonstrate then that this is dependent on action, as they do not observe signals in a Pavlovian behavioral task, but do observe reward-based signals in a "free consumption" task (the strawberry milk). The examination into devaluation also enhances the understanding of this pathway, even though there were no differences between a valued and devalued task. Finally, the authors examine bi-directional optogenetic manipulation of the pathway, and its impact on how the trials are completed, omitted, or incomplete. They find that manipulation alters the % completed trials and regulates trial omission. This paper really does not have any glaring weaknesses to point out, however, the physiological assessment does seem to have a few strong trends and even though the studies are well powered, and included both sexes, sex as a biological variable was not commented on that I could find. My estimation of the data doesn't suggest strong sex differences in any metric measured. Additionally, the data that included projections to the rILN were very interesting, and future studies looking into the physiology of these neurons, and/or how the physiology of these neurons adapt after operant training may be very interesting to understand plasticity within the adaptation across the training from FR1 to FR5 with time limits.

Thank you for your review. We analyzed our data for sex differences but did not identify any significant differences between male and female subjects for any of the experiments.

Public Review

Reviewer #1 (Public Review):

1) “In fact, it is not surprising that the collagen mutants display a detached cuticle, because the extracellular domains of MUP-4 and MUA-3 (the transmembrane receptors of apical hemidesmosomes that are primarily responsible for tethering the epidermis to the cuticle) both contain vWFA collagen-binding domain (Hong et al., JCB 2001; Bersher et al., JCB 2001). Hence loss of certain collagens in the cuticle directly affects cuticle-epidermis attachment due to defective ligand-receptor interactions is a much more plausible explanation.”

We agree with the reviewer that a specific molecular interaction likely mediates the attachment of the cuticle to the epidermis, not only in the area above the hemidesmosomes, but also in the area of the meisosomes. The collagens that potentially associate with MUP-4 and/or MUA-3 in the muscle regions have not been identified, nor in the main epidermal region, where the putative receptor is not known. We have modified the text accordingly.

“Likewise, it is more resonable to propose that lack of certain collagens in the cuticle directly affects cuticle stiffness, rather than working indirectly through epidermal meisosomes.”

We agree with the reviewer that the loss of specific structural components of the cuticle could well affect stiffness directly, especially if the furrows are affected; non-furrow collagen mutants do not show this phenotype. An analogy might be the increased stiffness that corrugation provides. We have modified the text accordingly. Our future research aims precisely at modelling these physical aspects.

2) “VHA-5::GFP does not co-localize with fluorescent markers for MVB, recycling endosomes and autophagolysosomes. By claiming this, the authors made a huge assumption that the overexpressed VHA-5::GFP fusion protein can only possibly associate with four types of organelles (meisosomes, MVB, recycling endosomes and autophagolysosomes) but not any other known or to-be-identified subcellular structures. In addition, a previous study did report that VHA-5 is localized in several other places besides the apical membrane stacks (Liegeois et al., JCB 2006).”

The reviewer cites the Liegeois paper that we mention above, which, in our opinion, and that of reviewer 2 (“VHA-5 is well known to localise to the apical membrane stacks (Liegeois 2006) and could be served as marker of apical membrane structure”), provides extremely strong support for our position. In Liegeois et al., 2006, there is a quantification of immunogold staining that shows that >85% of VHA-5 is found in meisosomes (Fig S5D). By providing the results of co-localisation analyses with 3 cytoplasmic vesicular markers, we simply wanted to illustrate the specificity of the signal to the non-initiated. Importantly, we now provide strong evidence that VHA-5::GFP marker co-localises with apical plasma membrane macrodomains revealed by both a PH domain of PLCδ and a CAAX marker. As our ultrastructural analyses demonstrate that meisosomes are composed by apical membrane folds, this again is wholly consistent with VHA-5 being a bonafide marker of meisosomes.

Reviewer #2 (Public Review):

The reviewer questioned the need to give another name to the “apical membrane stacks”. We made this proposition after consultation with a broad community of researchers in the field. We believe that this simpler name provides a link to an analogous structure in yeast, the eisosome, also at the interface between the aECM and the cell.

The reviewer wrote, “The major problem of this paper is that there is not much new information”, that it was known, for example, that “"furrowless" dpy mutants result in complete disorganization of the epidermis”. In addition to demonstrating that the furrowless Dpy mutants have very particular and specific phenotypes, without affecting the presence of hemidesmosomes (PMID: 33033182), nor different vesicular markers (FIgure 6S2), we would like to point out that reviewer #1 commented, “the work presented by Aggad et al. is rich in novelty”, and Reviewer #3, “The major strengths of the paper are the novelty”. We have re-written and reorganised the text and hope Reviewer #2 appreciates the novelty more in the revised version.

Author Response

Reviewer #2 (Public Review):

Wu Yang et al. investigated how exophers (large vesicles released from neuronal somas) are degraded. They find that the hypodermal skin cells surrounding the neuron break up the exophers into smaller vesicles that are eventually phagocytosed. The neuronal exophers accumulate early phagosomal markers such as F-actin and PIP2, and blocking actin assembly suppressed the formation of smaller vesicles and the clearance of neuronal exophers. They show the smaller vesicles are labeled with various markers for maturing phagosomes, and inhibiting phagosome maturation blocked the breakdown of exophers in to smaller vesicles. Interestingly, they discover that GTPase ARF-6, effector SEC-10/Exocyst, and the phagocytic receptor CED-1 in the hypodermis are required for efficient production of exophers by neurons.

Strength

The study clearly demonstrates that exophers are eliminated via hypodermal cellmediated phagocytosis. Exophers are broken down into smaller vesicles that accumulate phagocytic markers, and inhibiting this process shows that exophers are not resolved. The paper does a thorough examination of various markers and mutants to demonstrate this process.

The hypodermal cells not only engulf these small vesicles, but they also play a role in the formation of exophers. Exopher production is reduced when ARF-6, SEC-10, or CED-1 are knocked down in the hypodermis. This is intriguing because phagocytosis is a critical step in the final elimination of cells, but in this unique situation, it appears that the neuron fails to extrude the exopher without phagocytes.

Weakness

Non-professional phagocytes engulfing cell corpses and many other types of cellular debris (e.g. degenerating axons) have been shown in multiple systems and the observations here are not surprising. Many of the markers used in the study are wellestablished phagocytic markers and do not bring forward a new technological advance.

What's interesting is that the breakdown of exophers into smaller vesicles and eventual clearance follows a different sequence of events than macrophages. Exophers appear to undergo phagosomal fission before interacting with lysosomes. This would be difficult to appreciate by a general reader.

While the paper has strengths, it appears that the message is not clear. The title suggests that the reader will learn about how ARF-6 and CED-1 control exopher extrusion. Although this observation is intriguing and maybe the main point of the paper, there does not appear to be a substantial amount of data to support this claim. The only data to back this up is in the final figure and the majority of the paper is focused on how hypodermal cells phagocytose exophers.

The title has been revised.

To show exopher secretion is dependent on the hypodermal cells-

1) Could authors induce exopher production through other means? And test any involvement of CED-1? For example, authors note exopher production increases under stress conditions including expression of mutant Huntingtin protein. It would be intriguing if loss of CED-1 would be sufficient to block or reduce exopher production in that context and would highlight an exciting role for phagocytic cell types.

We interpreted this question as an inquiry into whether the neuron intrinsic exopher inducer was relevant to reliance on hypodermal interaction for exophergenesis, given our use of aggregating mCherry as the inducer. Unfortunately, our Huntingtin expressor lines now display high levels of transgene silencing, precluding their use in this experiment. To address this concern, we switched to a low toxicity GFP expressing transgene from the Chalfie lab, uIs31[Pmec17::GFP]. We found that arf-6 mutations suppressed exophers in this background as effectively as they did in previous mCherry experiments, indicating that our results are not dependent upon the particular transgene marking the touch neurons, or the specific protein they express (Fig 6E).

2) It is not clear if the CED-1 localization to the exopher is due to CED-1 expression during phagocytosis or is it involved in the extrusion. Perhaps the basal level of CED-1 is important for the extrusion but the strong expression is important for recognition of the exopher.

In the experiments we performed we used a constitutively expressed hypodermisspecific CED-1::GFP to show localization to exophers, so the recruitment of CED1::GFP in hypodermal membranes to the site where the neighboring neuron is producing an exopher is not caused by changes in expression, but rather is more likely to reflects protein recruitment. We now point this out more explicitly in the text. Added text: “Since the hypodermal CED-1DC::GFP we used is constitutively expressed, we attribute the exopher surrounding CED-1DC::GFP signal to CED-1 recruitment by exopher-surface signals."

3) While the data with ttr-52 and anoh-1 alleles is compelling, do we know that exophers actually expose PS? Especially since at a certain point, the exopher is still attached to the neuronal soma. Is PS still exposed by exopher in CED-1 background?

We are also very interested in this. Unfortunately, we have had difficulty obtaining sufficient MFGE8 PS-biosensor expression in the adult to test this question directly.

4) What is the fate of a neuron that is unable to produce exophers? Could one look at lifespan of ALMR neuron in CED-1, ARF-6 or Sec-10 allele (potentially with specificity to hypodermis)?

To address this question we measured the function of the mechanosensory touch neurons, using the classic gentle touch response assay in mCherry expressing animals, comparing controls to arf-6 and ced-1 mutants. For both arf-6 and ced-1 alleles, we found reduced response to gentle touch in older adults (Ad10), indicating a deficit in neuronal function. These results are consistent with exopher production maintaining neuronal health into old age, but interpretation is limited since neither ced-1 or arf-6 act specifically in exophergenesis and therefore also affect the animals in additional ways. Currently, there are no known genetic perturbations that act specifically in exophergenesis, so there is no better approach to do the analysis. We had already published similar results in our 2017 Nature paper that first described exophers, showing that gentle touch response is better preserved in a touch neuron HttQ128::CFP strain that produced a touch neuron exopher than in the same mutant background in which the touch neurons that had not produced an exopher.

Author Response

Reviewer 2 (Public Review):

The authors’ coarse-grained mathematical model is based upon proteome partitioning constraints. Similar models have been developed in the past, although the authors do an excellent job distinguishing their work. The interdependence among growth rate, growth yield, and carbon transport (together with the comparatively few state variables) makes the proposed model an attractive general framework for predictive metabolic engineering and strain optimization in bio-manufacturing.

Strengths:

1) The recognition that the constant biomass concentration (1/beta) can be used to recast the growthrate versus growth yield trade-off in terms of a growth rate versus carbon uptake trade-off (lines 147-155, Eq. 2), and coupling of the growth- and carbon uptake-rates through proteome partitioning, are powerful ideas. They transform the traditional (false) dichotomy of a negative correlation between growth and yield into a feasible space of growth-yield combinations (e.g. Figs 2BC).

2) The authors calibrate the model for E. coli (BW25113) grown in glycerol/glucose, batch/continuousculture (lines 157-164), then apply the model to an impressive variety of E. coli strains. This is not typically done with semi-mechanistic models and elevates the authors’ approach by implying that their model is sufficiently-general so as to apply across strains, yet sufficiently-constrained so as to provide quantitative predictions.

Weaknesses:

1) The tension between generality and constraint leads to some category errors where strain-specific empirical invariants are taken as general strain-independent operating conditions. This happens at least twice: a minor case involving the growth-rate threshold for acetate overflow, and a serious case where the magnitude of the ’housekeeping’ proteome fraction φq is taken to be strain- and condition-independent.

a) (lines 82-86) The growth-rate threshold for the acetate overflow switch in E. coli was observedin ’studies with a single strain in different conditions’ [i.e. different carbon sources in batch]. The interpretation provided in the references cited (lines 83-84) is that the threshold is a manifestation of a tipping point between carbon uptake rate and the costs of energy generation. The carbon uptake rate is implicitly strain-dependent; there is no reasonable expectation that all strains growing in glucose will be fermenting (or all respiring). The conclusion (line 84) that ’the model predicted no correlation between growth rate and acetate secretion rate in the case of different strains growing in the same environment’ is tautological when the carbon uptake rate (vmc) is used by the authors to distinguish among strains. This error is easily fixed by simply changing the wording, but it serves to illustrate how constraints operating at the strain level can be tacitly (and erroneously) applied at the genus level.

The emphasis we put on the comparison between batch growth on glucose of different strains vs batch growth in different environments of a single strain may have been misleading. The point we wanted to make was that the occurrence of fermentation (acetate overflow) during fast growth on glucose is not a necessary consequence of intrinsic physical constraints on metabolism, but the consequence of strain-specific regulatory mechanisms. This is demonstrated by the existence of E. coli strains that do not ferment while growing on glucose, but that have essentially the same metabolic capacities as strains that do. When we started this study, we did expect (perhaps naively) that growth on glucose at a high rate necessarily comes with low yield due to the higher relative acetate overflow, that is, the ratio of the acetate secretion and glucose uptake rates (Supplementary Figure 4 in the revised manuscript).

In the new version of the manuscript, we have modified the analysis of the glucose uptake and acetate secretion data, by plotting them against growth rate and growth yield in separate 2D plots, as suggested by Reviewer 1. This has led to a perspective that is more in line with the comment of this reviewer that the model explores different ways in which a carbon uptake rate can be converted into a growth rate, depending on the selected resource allocation strategy, and that this gives rise to trade-offs between growth rate and growth yield. In the context of this analysis, we do come back to the original point we wanted to make, but phrased differently (and hopefully more clearly this time).

Changes in manuscript: The comparison between batch growth on glucose of different strains and batch growth on different carbon sources of a single strain is less emphasized. We have rewritten the section and rephrased our claims accordingly throughout the paper (notably in the Abstract, Introduction, and Discussion).

b) The second example of this strain-genus confusion is more serious, and perhaps is enough to unravel the model. One of the strengths of the current framework is that although there are four degrees of freedom via the proteome allocation parameters, the model is sufficiently-constrained that the behavior can be meaningfully projected onto lower-dimensional observables like growth rate and yield (e.g. Figs 2BC).

One of the main constraints in the model that allows this meaningful projection is the assumption that the fraction of ’housekeeping’ proteins φq is constant irrespective of strain and growth conditions (line 172) and that these proteins carry flux synthesizing non-protein macromolecules (lines 141-142). Neither of these claims is supported by the references provided.

The ’housekeeping’ fraction φq was inferred in Scott et al. 2010 (line 172) from a nearly-growthmedium-independent maximum in the RNA/protein ratio under translation limitation of strain MG1655. The magnitude of that intercept is highly strain-dependent and can vary nearly 2-fold, especially in ALE strains. Furthermore, subsequent proteomic data (e.g. Hui et al. 2015 cited by the authors) has clarified that this ’housekeeping’ fraction is, for the most part, composed of growth-rate independent offsets in the metabolic proteins.

The origin of these offsets is thought to be related to substrate-saturation (Eqs. 1 and 2 of Dourado et al. 2021 cited by the authors) and consequently, these offsets (and by extension most of φq) carry no flux. Substrate saturation is perhaps at the root of the discrepancy in the Fig. 4 fits that necessitates adjustment of the catalytic constants (line 338). It is not correct to say that ’external substrate concentration S is assumed constant’ (bottom p. 25) therefore the catabolic rate vmc is an environment-dependent [i.e. substrate-concentration-independent] parameter. The ’mc’ proteins include carbon uptake and metabolism (e.g. Fig 1, or Table 2) so that intracellular changes in S could arise from strain differences thereby affecting vmc and the magnitude of the ‘housekeeping’ fraction.

It is not clear to me how the predictive power of the model will be affected by relaxing the constant φq assumption and replacing it with the more justifiable assumption that all metabolic proteins contribute some small fraction to φq based upon substrate saturation.

The reviewer criticizes two assumptions made in the construction and analysis of the model: (i) the fraction of housekeeping proteins is constant irrespective of strain and growth conditions, and (ii) the housekeeping proteins carry flux because they synthesize macromolecules other than proteins. Below, we summarize how we have tried to clarify these assumptions and which additional work we have performed to build model variants relaxing the assumptions.

We identified the housekeeping protein category with the Q-sector in the original paper of Scott et al. [13], which was misleading. The Hwa group indeed defines the Q-sector as not carrying flux [7], whereas we do allow this for the housekeeping protein category. Our housekeeping protein category, which we refer to as ”other proteins” or ”residual proteins” (Mu) in the new version of the manuscript, consists of all proteins not labelled as proteins in the categories of ribosomes and translation-affiliated proteins (R), enzymes in central carbon metabolism (Mc), or enzymes in energy metabolism (Mer+Mef). Mu carries flux, because it includes (among other things) the machinery for DNA and RNA synthesis (DNA polymerase, RNA polymerase, ...). When plotting the proteome fraction of this category determined from the data of Schmidt et al. [12], we found that the fraction remains approximately constant over a large range of growth conditions. This motivated the simplifying assumption to keep the proteome fraction for Mu constant in the simulations.

The reviewer is right, however, that this may not be the case when considering a variety of E. coli strains growing on glucose, especially the strains resulting from laboratory evolution experiments. We have therefore redone the simulations while allowing the Mu category to vary, by a percentage corresponding to experimentally-observed variations of this category over the range of growth conditions considered by Schmidt et al. [12] (Supplementary Figure 1). In comparison with the original results, the relaxation of this condition enlarges the attainable range of growth rates by about 10%, but the overall shape of the cloud of rate-yield phenotypes remains the same. These new simulation results are shown in the main figures of the revised manuscript.

In parallel, we have developed a model variant that includes a Q category in the sense of Scott et al., defined by the (growth-rate independent) offsets of the linear relations between growth rate and protein fractions [7]. We have retained an Mu category of other proteins in the model, interpreted as consisting of the growth-rate dependent fraction of other proteins, including the molecular machinery responsible for the synthesis of other macromolecules. Whereas the Mu category carries a flux, this is not the case for the Q category. We have calibrated the model variant from the same data as the original model, and predicted the admissible rate-yield phenotypes. While the cloud of predicted rate-yield phenotypes is slightly displaced in comparison with the reference model, the overall qualitative shape is the same. We explain this robustness by the fact that, despite the different interpretation of the protein categories, the models are structurally very similar and calibrated from data for the same reference strain. This gives rise to different values of the catalytic constants, which compensate for the differences in protein concentrations. Note that more data are needed for the calibration of the model with the Q category, because it requires estimation of the growth-rate-independent proteome fraction for all individual protein categories. In particular, in addition to carbon limitation, conditions of nitrogen and sulfur limitation are necessary [7]. In the absence of such data, additional assumptions need to be made, as we have explained in the new version of the manuscript.

We could not find a discussion of the relation between substrate saturation and growth-rate independent offsets in proteomics data in the paper by Dourado et al. [2]. In the revised version of the manuscript, however, we have exploited their idea to compare substrate saturation for different predicted and observed rate-yield phenotypes. As a prerequisite, this has required a refinement of the estimation of the half-saturation constants during model calibration, for which we have used the dataset of Km values collected by Dourado et al. [2]. The finding that high-rate, high-yield growth comes with high substrate saturation, indicating an efficient utilization of proteomic resources, has been given more emphasis in the revised manuscript. Note that each resource allocation strategy will give rise to a different concentration of metabolites, and therefore to a different level of substrate saturation of the enzymes.

The reviewer is right that the phrase ”the external substrate concentration S is assumed constant” is not correct for batch growth, although it approximately holds for continuous growth in a chemostat. In the case of balanced growth in batch, the external substrate concentration S is much higher than the half-saturation constant ), so that the kinetic equation for the macroreaction can be approximated by vmc = mc es, where es = kmc. In the revised manuscript, we have explicitly distinguished between these two situations (batch and continuous growth). Note that S is not the intracellular, but the extracellular concentration of substrate.

Changes in manuscript: We have better explained the meaning of the residual protein category Mu and corrected the misleading identification of this category with the Q-sector of Scott et al. [13] in the section Coarse-grained model with coupled carbon and energy fluxes and in Appendix 1. In new subsections of Appendix 1 and Appendix 2, we discuss the construction and calibration of a model variant with an additional growth-rate independent protein category corresponding to the Q-sector of Scott et al.. In the Discussion, we explain that the rate-yield predictions obtained from this model and the reference model are essentially the same, indicating the robustness of the model predictions.

We have redone all simulations using a resource allocation parameter for the housekeeping protein fraction Mu that is allowed to vary within experimentally-determined bounds (Coarsegrained model with coupled carbon and energy fluxes and Methods). The bounds are determined from the data of Schmidt et al. [12], as shown in the new Supplementary Figure 1. These simulations also include refined estimates for the half-saturation constants in the metabolic macroreactions.

In the final Results section, Resource allocation strategies enabling fast and efficient growth of Escherichia coli, we develop the point that higher saturation of enzymes and ribosomes is key to high-rate, high-yield growth of E. coli, in agreement with observations from other recent studies [2, 5, 9]. In Appendix 1, we emphasize that S is the extracellular substrate concentration and we distinguish between simplifications of vmc for batch and continuous growth.

Author Response

Reviewer #1 (Public Review):

Castelán-Sánchez et al. analyzed SARS-CoV-2 genomes from Mexico collected between February 2020 and November 2021. This period spans three major spikes in daily COVID-19 cases in Mexico and the rise of three distinct variants of concern (VOCs; B.1.1.7, P.1., and B.1.617.2). The authors perform careful phylogenetic analyses of these three VOCs, as well as two other lineages that rose to substantial frequency in Mexico, focusing on identifying periods of cryptic transmission (before the lineage was first detected) and introductions to and from the neighboring United States. The figures are well presented and described, and the results add to our understanding of SARS-CoV-2 in Mexico. However, I have some concerns and questions about sampling that could affect the results and conclusions. The authors do not provide any details on the distribution of samples across the various Mexican States, making it hard to evaluate several key conclusions. Although this information is provided in Supplementary Data 2, it is not presented in a way that enables the reader to evaluate if lineages were truly predominant in certain regions of the country, or if these results are attributable purely to sampling bias. Specifically, each lineage is said to be dominant in a particular state or region, but it was not clear to me if sampling across states was even at all-time points. For example, the authors state that most B.1.1.7 genome sampling is from the state of Chihuahua, but it is not clear if this was due to more sequenced samples from that region during the time that B.1.1.7 was circulating, or if the effects of B.1.1.7 were truly differential across the country. The authors do mention sequencing biases several times, but need to be more specific about the nature of this bias and how it could affect their conclusions. It is surprising to see in this manuscript that the B.1.1.7 lineage did not rise above 25% prevalence in the data presented, despite its rapid rise in prevalence in many other parts of the world. This calls into question if the presented frequencies of each lineage are truly representative of what was circulating in Mexico at the time, especially since the coordinated sampling and surveillance program across Mexico did not start until May 2021.

We thank the reviewer for the constructive comments. We recognize the need to better explain how the sequencing efforts in the country were set up and carried out, and this has now been clarified throughout the main text (L43-51, L95-105). A new figure comparing the overall cumulative proportion of genomes generated per state between 2020-2021 is now available as Supplementary Figure 1 c. The cumulative proportion of genomes sampled across states per lineage of interest, and corresponding to the period of circulation of the given lineage, were originally provided as maps in Figures 2-4. This has been further clarified in the Results section and in the corresponding figure legends. We also now provide additional maps representing the geographic distribution of the clades identified per lineage, integrating in the figures the information previously available in Supplementary Data 2, Supplementary Figures 4 and 5. As a note, for our analyses, we used the total cumulative genome data available from the country (and not only that generated by CoViGen-Mex, representing one third of the SARS-CoV-2 genomes from Mexico). This is expected to improve any sampling biases related to the scheme adopted by CoViGenMex, and is now clearly stated in the main text.

However, we believe that there has been a misunderstanding related to the genome sampling scheme adopted by CoViGen-Mex, as ‘coordinated sampling and surveillance program across Mexico did not start until May 2021’. Although it is true that further improvements were implemented after this date (enabling genome sampling and sequencing to become more homogenous across the country), the overall virus genome sequencing in Mexico was already sufficient from February 2021. This is represented by the cumulative number of viral genomes sequenced throughout 2020-2021 (both by CoViGen-Mex and other contributing institutions) correlating to the number of cases officially reported in the country during this time (see Supplementary Figure 1 a). This has now been clarified in the Results section (L94-105). Therefore, we hold that “SARS-CoV-2 sequencing in Mexico has been sufficient to explore the spatial and temporal frequency of viral lineages across national territory, and now to further investigate the number of lineage-specific introduction events, and to characterize the extension and geographic distribution of associated transmission chains, as we present in this study” (L102-105). In this context, “a more homogenous sampling across the country is unlikely to impact our main findings, but could i) help pinpoint additional clades we are currently unable to detect, ii) provide further details on the geographic distribution of clades across other regions of the country, and iii) deliver a higher resolution for the viral spread reconstructions we present” (discussed in L466-470).

For the B.1.1.7 lineage in Mexico, we have clarified the issue raised as follows: “during its circulation period, most B.1.1.7 genomes from Mexico were generated from the state of Chihuahua, with these representing the earliest B.1.1.7-assigned genomes from the country. However, our phylodynamic analysis revealed that only a small proportion of these grouped within a larger clade denoting an extended transmission chain (C2a), with the rest falling within minor clusters, or representing singleton events. Relative to other states, Chihuahua generated an overall lower proportion of viral genomes throughout 2020-2021. Thus, more viral genomes sequenced from a particular state does not necessarily translate into more well-supported clades denoting extended transmission chains, whilst the geographic distribution of clades is somewhat independent to the genome sampling across the country.” (L202-211). Again, these observations are supported by a sufficient overall genome sampling from Mexico.

We would further like to make clear that “our results confirm that the B.1.1.7 lineage reached an overall lower sampling frequency of up to 25% (relative to other virus lineages circulating in the country), as was noted prior to this study (for example, see Zárate et al. 2022)” (L189-193). As similar observations were independently made for other Latin American countries such as Brazil, Chile, and Peru (some with better genome representation than others, like Brazil https://www.gisaid.org/), it is possible that “the overall epidemiological dynamics of the B.1.1.7 in Latin America may have substantially differed from what was observed in the USA and UK. Such differences could be partly explained by competition between cocirculating lineages, exemplified in Mexico by the regional co-circulation of B.1.1.7, P.1 and B.1.1.519. Nonetheless, the lack of a representative number of viral genomes for most of these countries prevents exploring such hypothesis at a larger scale, and further highlights the need to strengthen genomic epidemiology-based surveillance across the region” (now discussed in L372-379). We hope the reviewer considers that the issues raised have now been resolved.

Reviewer #2 (Public Review):

The authors use a series of subsampling methods based on phylogenetic placement and geographic setting, informed by human movement data to control for differences in sampling of SARS-CoV-2 genomes across countries. Of note, the authors show that 2 variants likely arose in Mexico and spread via multiple introductions globally, while other variant waves were driven by repeat introductions into Mexico from elsewhere. Finally, they use human mobility data to assess the impact of movement on transmission within Mexico. Overall, the study is well done and provides nice data on an under-studied country. The authors take a thoughtful approach to subsampling and provide a very thorough analysis. Because of the care given to subsampling and the great challenge that proper subsampling represents for the field of phylodynamics, the paper would benefit from a more thorough exploration of how their migration-informed subsampling procedure impacts their results. This would not only help strengthen the findings of the paper, but would likely provide a useful reference for others doing similar studies. Additionally, I would suggest the authors provide a bit more discussion of this subsampling approach and how it may be useful to others in the discussion section of the paper.

We thank the reviewer for the constructive comments, and appreciate the recognition of our sub-sampling scheme as a valuable tool with potential application in other studies. We acknowledge the need for a ‘more thorough exploration and discussion of how a different migration-informed subsampling approach could impact our results’. To address this issue, “we further sought to validate our migration-informed genome subsampling scheme (applied to B.1.617.2+, representing the best sampled lineage in Mexico). For this, an independent dataset was built using a different migration sub-sampling approach, comprising all countries represented by B.1.617.2+ sequences deposited in GISAID (available up to November 30th 2021). In order to compare the number of introduction events, the new dataset was analysed independently under a time-scaled DTA (as described in Methods Section 4).” (L517-524). In the new dataset, <100 genome sequences from the USA were retained for further analysis (Supplementary Figure 2b), compared to approximately 2000 ‘USA’ genome sequences included in the original B.1.617.2+ alignment. Thus, we expected a lower number of inferred introduction events into Mexico, as an undersampling of viral genome sequences from the USA is likely to result in ‘Mexico’ clades not fully segregating (particularly impacting C5d).

Our original results revealed a minimum number of 142 introduction events into Mexico (95% HPD interval = [125-148]), with 6 clades identified as denoting extended transmission chains. The DTA results derived from the new dataset (subsampling all countries) revealed a minimum number of 84 introduction events into Mexico (95% HPD interval = [81-87]), with again 6 major clades identified. Thus, a significantly lower number of introduction events into Mexico were inferred, as was expected. On the other hand, the number of clades identified were consistent between both datasets, supporting for the robustness of our phylogenetic methodological approach. However, in the new dataset, we observe that C5d displayed a reduced diversity (represented by the AY.113 and AY.100 genomes from Mexico, but excluded the B.1.617.2 genome sampled from the USA). This highlights the relevance of our genome sub-sampling using migration data as a proxy.

In further agreement with these observations, publicly available data on global human mobility (https://migration-demography-tools.jrc.ec.europa.eu/data- hub/index.html?state=5d6005b30045242cabd750a2) shows that migration into Mexico is mostly represented by movements from the USA, followed by Indonesia, Guatemala, Belize and Colombia and Belize. However, the volume of movements from the USA into Mexico is much higher (up to 6 orders of magnitude above the volumes recorded into Mexico from any other country).

Given time constraints related to performing additional analyses, we decided to exclude the subsampling scheme for ‘top ten countries’ suggested by the reviewer. However, we consider that the results derived from the comparison between the original and the new dataset (top-5 vs all countries) is sufficient to support for our migration-informed subsampling approach. A full description of the methodology and the result obtained, as well as a short discussion, is now available as Supplementary Text 2, and Supplementary Figure 2b and 2c. We hope the reviewer considers that the issues raised has been addressed.

Author Response

Reviewer #1 (Public Review):

The authors sought to identify the relationship between social touch experiences and the endogenous release of oxytocin and cortisol. Female participants who received a touch from their romantic partner before a stranger exhibited a blunted hormonal response compared to when the stranger was the first toucher, suggesting that social touch history and context influence subsequent touch experiences. Concurrent fMRI recordings identified key brain networks whose activity corresponded to hormonal changes and self-report.

The strengths of the manuscript are in the power achieved by collecting multi-faceted metrics: plasma hormones across time, BOLD signal, and self-report. The experiment was cleverly designed and nicely counterbalanced. Data analysis was thorough and statistically sophisticated, making the findings and conclusions convincing.

This work sheds new light on potential mechanisms underlying how humans place social experiences in context, demonstrating how oxytocin and cortisol might interact to modulate higher-level processing and contextualizing of familiar vs. stranger encounters.

Thank you very much for this generous evaluation of the study.

Reviewer #2 (Public Review):

To test how oxytocin impacts the brain and the psychological, neural, and hormonal response to touch, the authors tested human females during two counterbalanced fMRI sessions wherein females were stroked on the arm or the palm, by a real-world romantic partner or a stranger, while blood levels of oxytocin and cortisol were collected at multiple time points.

This combination of measures, and the number of hypotheses that could be tested with them, is remarkable - virtually unheard of. This impressive, difficult, and more ecological design than is typical for the field is a major strength of the study, which allowed the authors to test many important hypotheses concurrently and to show contextual effects that could not otherwise be observed. The only potential drawback perhaps is that with such a large design, including many measures, the authors produced so many significant interactions and results that it could be hard for the casual reader to appreciate the importance of each.

The authors supported their hypothesis that oxytocin effects are context-sensitive, as they found a key interaction wherein experiencing the partner first increased oxytocin for the partner relative to when they came first the OT levels were low but then increased if they were preceded by the partner (excepting one timepoint). Cortisol responses (which reflect hormonal stress) were also higher when the stranger came first than when he was preceded by the partner). In addition, touch was experienced more positively on the arm than on the palm, supporting the role of c-fibers in conveying specifically felt responses to warm, tender touch.

These data indicate significant context sensitivity with real-world implications. For example, experiencing warm touch on the arm can make us more receptive to other people in subsequent encounters. Conversely, when strangers try to approach and get close to us "out of the blue" people experience this as stressful, which reduces the pleasantness of the interaction and may reduce trust in the moment...perhaps even subsequently.

This research is critical to the basic science of neurohormonal modulation, given that most of this research occurs in rodents or in simplified studies in humans, usually through intranasal oxytocin administration with unclear impacts on circulating levels in the brain and blood. Oxytocin in particular has suffered from oversimplification as the "love drug" - wherein people assume that it always renders people more loving and trusting. The reality is more complex, as they showed, and these demonstrations are needed to clarify for the field and the public that neurohormones adaptively shift with the context, location, and identity of the social partner in an adaptive way. These results also help us understand the many null effects of oxytocin on trusting strangers in human neuroeconomic studies. In a modern world that is characterized by significant loneliness, interactions with strangers and outsiders, and touch-free digital interactions, our ability to understand the human need for genuine social contact and how it impacts our response to outsiders (welcomed in versus a source of stress) is critical to human health and the wellbeing of individuals and society.

Thank you very much for this nice summary of the study and its implications.

As you pointed out, the design was ambitious and involved a broad range of measures and levels of hypothesis-testing. This presented challenges in reporting the results. In this paper we have tried to provide interpretation of the basic results, such as that social encounters (even in the scanner environment) are sufficient to evoke changes in endogenous oxytocin levels over the course of the experimental session, and that various interactions arise due to an influence of contextual factors such as the familiarity of the person and the recent social interaction history. For the more complex results, such as the nature of relationships between BOLD signal change and the degree of change in individuals’ plasma oxytocin levels, we have tried to outline provisional interpretations.

We hope that the picture will gradually become more filled-in by work from ours and others’ labs—maybe these findings and interpretations will look very different in a few years’ time. We consider this study a starting point for future research into the dynamics and function of human endogenous oxytocin.

Reviewer #3 (Public Review):

In an ambitious, multimodal effort, Handlin, Novembre et al. investigated how the endogenous release of oxytocin and cortisol as well as functional brain activity are modulated by social touch under different contextual circumstances (e.g. palm vs. arm touch, stranger vs. partner touch) in neurotypical female participants.

Using serial sampling of plasma hormone levels in blood during concurrent functional MRI neuroimaging, the authors show that the familiarity of the interactant during social touch not only impacts current hormonal levels but also subsequent hormonal responses in a successive touch interaction. Specifically, endogenous oxytocin levels are significantly heightened (and cortisol levels dampened) during touch from a romantic partner compared to touch from an unfamiliar stranger, at least during the first touch interaction. During the second touch interaction, however, oxytocin levels plummeted when being touched by a stranger following partner touch (although a recovery was made), whereas the normally elevated oxytocin responses to partner touch were dampened when following stranger touch. These results are paralleled by similar familiarity- and order-related effects in neural regions involving the hypothalamus, dorsal raphe, and precuneus.

However, an important distinction to be made is that, although a significant main effect of familiarity was encountered in several brain regions when taking peak plasma oxytocin levels into account, subsequent t-tests showed no activation differences in the BOLD response between partner and stranger touch within the same subjects. Significant interaction maps seem thus mainly driven by between-subject effects at the different time points, which is arguably due to differences between subjects in their initial calibration of neural/hormonal responses, and not session-to-session changes within the same subjects.

A similar comment can be made for the reported covariance between (changes in) maximal oxytocin levels and (changes in) BOLD activity for the hypothalamus.

In an effort to delineate the complex cascade of responses induced by afferent tactile stimulation, the authors report an exploratory regression analysis to identify BOLD activation that precedes the pattern of serial plasma changes in oxytocin levels (looking backwards; i.e. implying changes in brain activation drive changes in hormonal plasma levels). Although the authors are appropriately modest about the significance of the encountered effects, additional control analyses could bring further clarifications about the temporal (e.g., can similar covariations also be found when looking forward) and hormonal specificity (e.g. can similar findings be found for cortisol-variations) of the encountered results. Nevertheless, despite the 'dynamically' covarying relationships between BOLD and max plasma oxytocin levels (i.e. dynamic as in the sense across conditions, not across timepoints), claims about the directionality of this effect (i.e. 'hormonal neuromodulation' vs. 'neural modulation of hormonal levels') remain speculative.

A particular strength of this study is the employment of a "female-first" strategy since experimental data concerning endogenous oxytocin levels in women are sparse. Adequate control analyses are reported to take potential variability due to differences in contraception and phase in the hormonal cycle into account.

Thank you for your attentive reading of the study, and for raising several very important points.

You are right that the BOLD activation maps showing interactions between the change in OT levels and other factors (familiarity, order) reflect differences between subjects in the two runs of the experiment. The effect of familiarity emerged from the full model for the whole group (all participants, whether they started with partner or stranger), as an interaction between the partner/stranger factor and the change in OT. As you point out, this reflects interindividual-level covariation between OT changes and BOLD changes. For example, individuals showing greater OT increase were also more likely to show higher BOLD in certain clusters during partner compared to stranger touch. Similarly, the partner vs stranger contrast showing hypothalamus and Raphe reflects greater OT-BOLD covariance in the stranger first compared to the partner fist groups: in the stranger first group, BOLD was greater the lower the mean OT was across individuals.

The t-tests with OT as covariate further indicate that the interaction was driven by group differences in the second run. As you point out, within groups (partner or stranger first), there was no significant change in the OT-BOLD covariance from the first to the second run, though these relationships were different between groups. We agree with you that this lack of difference in within-group OT-BOLD covariance from the first to the second run is likely because responses in the first run biased responses in the second run—but in different ways depending on whether the partner or the stranger was presented first. Both groups did show a meaningful correlation in mean OT levels between the first and the second run (we have now included this information in the paper).

In general, we agree that it is very important to make clear that, as in many covariation/correlation effects in fMRI studies, the effects are driven by interindividual differences for a given covariant relationship, rather than the within-subject BOLD response increasing or decreasing.

We also agree that it is not possible to determine the direction of modulation from these results. The creation of the temporal OT regressor as “backward-looking” was informed by evidence from animal models for central-to-peripheral effects from hypothalamus to pituitary to bloodstream. We assumed this directionality in the analysis. Given the exploratory nature of this regressor, “looking forward” from temporal OT sample patterns to BOLD patterns with different time intervals would be an equally valid approach. It could reveal activation related to any systematic influence of peripheral OT levels on cortical responses. As the premise of the temporal OT regressor analysis in the present study was any assumed central-to-peripheral modulation, we have kept this as the focus but will explore any specific peripheral-to-central covariation in future work.

We believe that the full causal picture is likely to involve bidirectional modulation: a modulatory loop (or even loops) in which peripheral and central changes influence one another. Unfortunately, it is difficult to address such temporal feedback with the poor time resolution of fMRI.

Author Response

Reviewer #1 (Public Review):

This is one of the most careful analyses of sexual dimorphism in dinosaurs, based on a remarkable assemblage of 61 ornithomimosaur fossils from the Early Cretaceous of western France. The dimorphism is expressed in variations in the shaft curvature and the distal epiphysis width, analysed appropriately here and plausible because these are the kinds of morphological features that vary between males and females among birds and crocodilians, among others.

In the Introduction, it is right to highlight the shortage of convincing cases of demonstrated sexual dimorphism (SD) in dinosaurs. But note the points made by Hone, Saitta and others that SD can exist in many species today without major morphological differences, making it hard to demonstrate in fossils with such types of dimorphism. Also, some proposed statistical tests to ensure that SD has been convincingly demonstrated in fossils are so stringent they would be hard ever to pass (requiring enormous and constant morphological distinctiveness). In other words, we are conditioned not to find SD in dinosaurs, and yet may be massively under-reporting it because of preservation difficulties (of course) but also because of some overly rigorous demands for proof. These issues help argue that the current study is especially valuable because the data set is large (itself a rarity), and 3D bone shape analysis and proper statistical testing have been applied.

We are grateful that Reviewer 1 raised this point regarding the occurrence of many subtle sexual dimorphism among modern populations, and added a sentence in the introduction, to further emphasize the importance of a large dataset composed of coeval organisms.

It's interesting the dinosaur example shows the same two dimorphic traits (femoral obliquity = bicondylar angle; width of distal epiphysis = bicondylar breadth) seen in mammals (MS, lines 117-123), where the femur angle may vary because of the need for broader hips in the female to accommodate the birth canal, and yet dinosaurs laid eggs. These are small dinosaurs, so perhaps their eggs were relatively large in proportion to body size. Perhaps the authors could comment on this. There is some discussion with regard to modern birds at MS lines 187-199.

We agree with comments from Reviewer 1 and we raise the question of egg possibly constraining the pelvic and proximal hindlimb morphology from line 170 to 189 and how it relates to modern archosaurs from line 189 to 202. We also originally intended to discuss how the Kiwi hindlimb morphology accommodates large eggs, but no significant dimorphism was demonstrated in the pelvic and hindlimb morphology of this bird.

Author Response

Reviewer #2 (Public review):

Ansari et al. describe a web-based software for the design of guide RNA (gRNA) sequences and primers for CRISPR-Cas-based identification of single nucleotide variants (SNVs). The use of CRISPR-Cas to rapidly identify specific mutations in both cancer and infection is an evolving field with good potential to play a role in future research and diagnostics.

The software described by Ansari et al. is easy to use for the design of guide RNAs. The most important question is how good the gRNAs that the software suggests are. As such, the manuscript would benefit from better describing the parameters used for the gRNA design as well as including more validation experiments. Clearly, the scope of the manuscript is not about developing different detection methods, but I would argue that performing more wet lab experiments is needed to support the usability of the software.

We thank the reviewer for taking interest in this manuscript and raising an important point about increasing the number of targets for our wet lab experiments. To address this, we have tried to include more supporting data in the updated version of the manuscript.

Reviewer #3 (Public review):

This manuscript by Ansari and coworkers describes CriSNPr, a tool for designing gRNAs for CRISPR-based diagnostics for SNP detection. CriSNPr allows one to design assays to detect human and SARS-CoV-2 mutations, positioning the mismatches for optimal detection based on results from the literature. Designs can be generated for six different CRISPR effector proteins. The authors test their approach by designing assays to detect a single SNV using three different CRISPR effectors. A strength of the manuscript is that the method does appear to work, at least for the E484K mutation, for multiple CRISPR effector proteins.

The weaknesses of this manuscript are the lack of data demonstrating that the method works. There is only one very small experimental demonstration using a single mutation (Figure 4) and some very high-level analyses using two SNP/SNV databases (Figure 5). The authors do not provide any data to answer any basic questions about how well their designs work, how fast and easy it is to run their method, or which designs are predicted to work better than others. These weaknesses ultimately limit the impact of the work on the field, as it is not clear what the benefits of using the author's approach are versus simply applying the rules for the individual CRISPR effector proteins outlined in Figure 1 of the manuscript.

We thank the reviewer for taking interest in this manuscript and appreciate the constructive feedback and suggestions. In the new version of this paper, we've added more data to back up other SNVs with different CRISPR systems and the CriSNPr pipeline for sgRNA design. Even in these datasets, we see that for particular SNVs, the choice of the CRISPR system used might affect the sensitivity of detecting the mutation (Figures 5 and 6). This would be a huge task to do again for multiple targets and targeting systems, which is outside the scope of this study. Importantly, such large datasets are currently missing for the different CRISPRDx systems since we have not come across studies where users have comparatively determined the best methodology for their assay. In our opinion, criSNPr gives users this opportunity by providing a unified platform, and our validation assays show how this can be done in a relatively fast manner.

A stand-alone version of the server is made available for download at https://github.com/asgarhussain/CriSNPr to increase its speed and accessibility for the end user.

Addressing the point of determining which crRNAs work best for a given assay requires a large amount of data on target SNPs for individual Cas systems, which is currently scarce. In the current version of CriSNPr, we have considered prioritizing crRNA mismatch-sensitive positions based on original published studies. For example, for AaCas12b, mismatch positions are ranked as follows: 1&4 > 1&5 > 4&11 > 4&16 > 5&8 > 5&11 > 16&19. Similarly, crRNA mismatch-sensitive positions for individual Cas systems (as shown in Figure 1) have been used to prioritize crRNAs. Improving on these design principles further would require studying the biology of individual Cas:DNA/RNA interactions, which is beyond the scope of this study. However, in the updated version of the CriSNPr, we attempted to improve the scoring algorithm by taking into account off-targets for a crRNA design, and priority is given to the combinatorial positions with the fewest off-targets as well as the weightage of their efficacy.

Author Response:

We would like to thank both reviewers and editors for their time and effort in reviewing our work, and the thoughtful suggestions made.

Reviewer #1 (Public Review):

[…] The experiments are well-designed and carefully conducted. The conclusions of this work are in general well supported by the data. There are a couple of points that need to be addressed or tested.

1) It is unclear how LC phasic stimulation used in this study gates cortical plasticity without altering cellular responses (at least at the calcium imaging level). As the authors mentioned that Polack et al 2013 showed a significant effect of NE blockers in membrane potential and firing rate in V1 layer2/3 neurons during locomotion, it would be useful to test the effect of LC silencing (coupled to mismatch training) on both cellular response and cortical plasticity or applying NE antagonists in V1 in addition to LC optical stimulation. The latter experiment will also address which neuromodulator mediates plasticity, given that LC could co-release other modulators such as dopamine (Takeuchi et al. 2016 and Kempadoo et al. 2016). LC silencing experiment would establish a causal effect more convincingly than the activation experiment.

Regarding the question of how phasic stimulation could alter plasticity without affecting the response sizes or activity in general, we believe there are possibilities supported by previous literature. It has been shown that catecholamines can gate plasticity by acting on eligibility traces at synapses (He et al., 2015; Hong et al., 2022). In addition, all catecholamine receptors are metabotropic and influence intracellular signaling cascades, e.g., via adenylyl cyclase and phospholipases. Catecholamines can gate LTP and LTD via these signaling pathways in vitro (Seol et al., 2007). Both of these influences on plasticity at the molecular level do not necessitate or predict an effect on calcium activity levels. We will expand on this in the discussion of the revised manuscript.

While a loss of function experiment could add additional corroborating evidence that LC output is required for the plasticity seen, we did not perform loss-of-function experiments for three reasons:

1. The effects of artificial activity changes around physiological set point are likely not linear for increases and decreases. The problem with a loss of function experiment here is that neuromodulators like noradrenaline affect general aspects neuronal function. This is apparent in Polack et al., 2013: during the pharmacological blocking experiment, the membrane hyperpolarizes, membrane variance becomes very low, and the cells are effectively silenced (Figure 7 of (Polack et al., 2013)), demonstrating an immediate impact on neuronal function when noradrenaline receptor activation is presumably taken below physiological/waking levels. In light of this, if we reduce LC output/noradrenergic receptor activation and find that plasticity is prevented, this could be the result of a direct influence on the plasticity process, or, the result of a disruption of another aspect of neuronal function, like synaptic transmission or spiking. We would therefore challenge the reviewer’s statement that a loss-of-function experiment would establish a causal effect more convincingly than the gain-of-function experiment that we performed.

2. The loss-of-function experiment is technically more difficult both in implementation and interpretation. Control mice show no sign of plasticity in locomotion modulation index (LMI) on the 10-minute timescale (Figure 4J), thus we would not expect to see any effect when blocking plasticity in this experiment. We would need to use dark-rearing and coupled-training of mice in the VR across development to elicit the relevant plasticity ((Attinger et al., 2017); manuscript Figure 5). We would then need to silence LC activity across days of VR experience to prevent the expected physiological levels of plasticity. Applying NE antagonists in V1 over the entire period of development seems very difficult. This would leave optogenetically silencing axons locally, which in addition to the problems of doing this acutely (Mahn et al., 2016; Raimondo et al., 2012), has not been demonstrated to work chronically over the duration of weeks. Thus, a negative result in this experiment will be difficult to interpret, and likely uninformative: We will not be able to distinguish whether the experimental approach did not work, or whether local LC silencing does nothing to plasticity.

   Note that pharmacologically blocking noradrenaline receptors during LC stimulation in the plasticity experiment is also particularly challenging: they would need to be blocked throughout the entire 15 minute duration of the experiment with no changes in concentration of antagonist between the ‘before’ and ‘after’ phases, since the block itself is likely to affect the response size, as seen in Polack et al., 2013, creating a confound for plasticity-related changes in response size. Thus, we make no claim about which particular neuromodulator released by the LC is causing the plasticity.

3. There are several loss-of-function experiments reported in the literature using different developmental plasticity paradigms alongside pharmacological or genetic knockout approaches. These experiments show that chronic suppression of noradrenergic receptor activity prevents ocular dominance plasticity and auditory plasticity (Kasamatsu and Pettigrew, 1976; Shepard et al., 2015). Almost absent from the literature, however, are convincing gain-of-function plasticity experiments.

Overall, we feel that loss-of-function experiments may be a possible direction for future work but, given the technical difficulty and – in our opinion – limited benefit that these experiments, would provide in light of the evidence already provided for the claims we make, we have chosen not to perform these experiments at this time. Note that we already discuss some of the problems with loss-of-function experiments in the discussion.

2) The cortical responses to NE often exhibit an inverted U-curve, with higher or lower doses of NE showing more inhibitory effects. It is unclear how responses induced by optical LC stimulation compare or interact with the physiological activation of the LC during the mismatch. Since the authors only used one frequency stimulation pattern, some discussion or additional tests with a frequency range would be helpful.

This is correct, we do not know how the artificial activation of LC axons relates to physiological activation, e.g. under mismatch. The stimulation strength is intrinsically consistent in our study in the sense that the stimulation level to test for changes in neuronal activity is similar to that used to probe for plasticity effects. We suspect that the artificial activation results in much stronger LC activity than seen during mismatch responses, given that no sign of the plasticity in LMI seen in high ChrimsonR occurs in low ChrimsonR or control mice (Figure 4J). Note, that our conclusions do not rely on the assumption that the stimulation is matched to physiological levels of activation during the visuomotor mismatches that we assayed. The hypothesis that we put forward is that increasing levels of activation of the LC (reflecting increasing rates or amplitude of prediction errors across the brain) will result in increased levels of plasticity. We know that LC axons can reach levels of activity far higher than that seen during visuomotor mismatches, for instance during air puff responses, which constitute a form of positive prediction error (unexpected tactile input) (Figures 2C and S1C).  The visuomotor mismatches used in this study were only used to demonstrate that LC activity is consistent with prediction error signaling. We will expand on these points in the discussion as suggested.

Reviewer #2 (Public Review):

[…] The study provides very compelling data on a timely and fascinating topic in neuroscience. The authors carefully designed experiments and corresponding controls to exclude any confounding factors in the interpretation of neuronal activity in LC axons and cortical neurons. The quality of the data and the rigor of the analysis are important strengths of the study. I believe this study will have an important contribution to the field of system neuroscience by shedding new light on the role of a key neuromodulator. The results provide strong support for the claims of the study. However, I also believe that some results could have been strengthened by providing additional analyses and experimental controls. These points are discussed below.

Calcium signals in LC axons tend to respond with pupil dilation, air puffs, and locomotion as the authors reported. A more quantitative analysis such as a GLM model could help understand the relative contribution (and temporal relationship) of these variables in explaining calcium signals. This could also help compare signals obtained in the sensory and motor cortical domains. Indeed, the comparison in Figure 2 seems a bit incomplete since only "posterior versus anterior" comparisons have been performed and not within-group comparisons. I believe it is hard to properly assess differences or similarities between calcium signal amplitude measured in different mice and cranial windows as they are subject to important variability (caused by different levels of viral expression for instance). The authors should at the very least provide a full statistical comparison between/within groups through a GLM model that would provide a more systematic quantification.

We will implement an improved analysis in the revised version of the manuscript.

Previous studies using stimulations of the locus coeruleus or local iontophoresis of norepinephrine in sensory cortices have shown robust responses modulations (see McBurney-Lin et al., 2019, https://doi.org/10.1016/j.neubiorev.2019.06.009 for a review). The weak modulations observed in this study seem at odds with these reports. Given that the density of ChrimsonR-expressing axons varies across mice and that there are no direct measurements of their activation (besides pupil dilation), it is difficult to appreciate how they impact the local network. How does the density of ChrimsonR-expressing axons compare to the actual density of LC axons in V1? The authors could further discuss this point.

In terms of estimating the percentage of cortical axons labelled based on our axon density measurements: we refer to cortical LC axonal immunostaining in the literature to make this comparison. In motor cortex, an average axon density of 0.07 µm/µm2 has been reported (Yin et al., 2021), and 0.09 µm/µm2 in prefrontal cortex (Sakakibara et al., 2021). Density of LC axons varies by cortical area, with higher density in motor cortex and medial areas than sensory areas (Agster et al., 2013): V1 axon density is roughly 70% of that in cingulate cortex (adjacent to motor and prefrontal cortices) (Nomura et al., 2014). So, we approximate a maximum average axon density in V1 of approximately 0.056 µm/µm2. Because these published measurements were made from images taken of tissue volumes with larger z-depth (~ 10 µm) than our reported measurements (~ 1 µm), they appear much larger than the ranges reported in our manuscript (0.002 to 0.007 µm/µm2). We repeated the measurements in our data using images of volumes with 10 µm z-depth, and find that the percentage axons labelled in our study in high ChrimsonR-expressing mice ranges between 0.012 to 0.039 µm/µm2. This corresponds to between 20% to 70% of the density we would expect based on previous work. Note that this is a potentially significant underestimate, and therefore should be used as a lower bound: analyses in the literature use images from immunostaining, where the signal to background ratio is very high. In contrast, we did not transcardially perfuse our mice leading to significant background (especially in the pia/L1, where axon density is high - (Agster et al., 2013; Nomura et al., 2014)), and the intensity of the tdTomato is not especially high. We therefore are likely missing some narrow, dim, and superficial fibers in our analysis.

We also can quantify how our variance in axonal labelling affects our results: For the dataset in Figure 3, there doesn’t appear to be any correlation between the level of expression and the effect of stimulating the axons on the mismatch or visual flow responses for each animal (Figure R1: https://imgur.com/gallery/Yl60hnT), while there is a significant correlation between the level of expression and the pupil dilation, consistent with the dataset shown in Figure 4. Thus, even in the most highly expressing mice, there is no clear effect on average response size at the level of the population. We will add these correlations to the revised manuscript.

To our knowledge, there has not yet been any similar experiment reported utilizing local LC axonal optogenetic stimulation while recording cortical responses, so when comparing our results to those in the literature, there are several important methodological differences to keep in mind. The vast majority of the work demonstrating an effect of LC output/noradrenaline on responses in the cortex has been done using unit recordings, and while results are mixed, these have most often demonstrated a suppressive effect on spontaneous and/or evoked activity in the cortex (McBurney-Lin et al., 2019). In contrast to these studies, we do not see a major effect of LC stimulation either on baseline or evoked calcium activity (Figure 3), and, if anything, we see a minor potentiation of transient visual flow onset responses (see also Figure R2). There could be several reasons why our stimulation does not have the same effect as these older studies:

1. Recording location: Unit recordings are often very biased toward highly active neurons (Margrie et al., 2002) and deeper layers of the cortex, while we are imaging from layer 2/3 – a layer notorious for sparse activity. In one of the few papers to record from superficial layers, it was been demonstrated that deeper layers in V1 are affected differently by LC stimulation methods compared to more superficial ones (Sato et al., 1989), with suppression more common in superficial layers. Thus, some differences between our results and those in the majority of the literature could simply be due to recording depth and the sampling bias of unit recordings.

2. Stimulation method: Most previous studies have manipulated LC output/noradrenaline levels by either iontophoretically applying noradrenergic receptor agonists, or by electrically stimulating the LC. Arguably, even though our optogenetic stimulation is still artificial, it represents a more physiologically relevant activation compared to iontophoresis, since the LC releases a number of neuromodulators including dopamine, and these will be released in a more physiological manner in the spatial domain and in terms of neuromodulator concentration. Electrical stimulation of the LC as used by previous studies differs from our optogenetic method in that LC axons will be stimulated across much wider regions of the brain (affecting both the cortex and many of its inputs), and it is not clear whether the cause of cortical response changes is in cortex or subcortical. In addition, electrical LC stimulation is not cell type specific.

3. Temporal features of stimulation: Few previous studies had the same level of temporal control over manipulating LC output that we had using optogenetics. Given that electrical stimulation generates electrical artifacts, coincident stimulation during the stimulus was not used in previous studies. Instead, the LC is often repeatedly or tonically stimulated, sometimes for many seconds, prior to the stimulus being presented. Iontophoresis also does not have the same temporal specificity and will lead to tonically raised receptor activity over a time course determined by washout times.

4. State specificity: Most previous studies have been performed under anesthesia – which is known to impact noradrenaline levels and LC activity (Müller et al., 2011). Thus, the acute effects of LC stimulation are likely not comparable between anesthesia and in the awake animal.

Due to these differences, it is hard to infer why our results differ compared to other papers. The study with the most similar methodology to ours is (Vazey et al., 2018), which used optogenetic stimulation directly into the mouse LC while recording spiking in deep layers of the somatosensory cortex with extracellular electrodes. Like us, they found that phasic optogenetic stimulation alone did not alter baseline spiking activity (Figure 2F of Vazey et al., 2018), and they found that in layers 5 and 6, short latency transient responses to foot touch were potentiated and recruited by simultaneous LC stimulation. While this finding appears more overt than the small modulations we see, it is qualitatively not so dissimilar from our finding that transient responses appear to be slightly potentiated when visual flow begins (Figure R2). Differences in the degree of the effect may be due to differences in the layers recorded, the proportion of the LC recruited, or the fact anesthesia was used in Vazey et al., 2018.

Note that we only used one set of stimulation parameters for optogenetic stimulation, and it is always possible that using different parameters would result in different effects. We will add a discussion on the topic to the revised manuscript.

In the analysis performed in Figure 3, it seems that red light stimulations used to drive ChrimsonR also have an indirect impact on V1 neurons through the retina. Indeed, figure 3D shows a similar response profile for ChrimsonR and control with calcium signals increasing at laser onset (ON response) and offset (OFF response). With that in mind, it is hard to interpret the results shown in Figure 3E-F without seeing the average calcium time course for Control mice. Are the responses following visual flow caused by LC activation or additional visual inputs? The authors should provide additional information to clarify this result.

This is a good point. When we plot the average difference between the stimulus response alone and the optogenetic stimulation + stimulus response, we do indeed find that there is a transient increase in response at the visual flow onset (and the offset of mismatch, which is where visual flow resumes), and this is only seen in ChrimsonR-expressing mice (Figure R2: https://imgur.com/gallery/cqN2Khd). We therefore believe that these enhanced transients at visual flow onset could be due to the effect of ChrimsonR stimulation, and indeed previous studies have shown that LC stimulation can reduce the onset latency and latency jitter of afferent-evoked activity (Devilbiss and Waterhouse, 2004; Lecas, 2004), an effect which could mediate the differences we see. We will add this analysis to the revised manuscript.

Some aspects of the described plasticity process remained unanswered. It is not clear over which time scale the locomotion modulation index changes and how many optogenetic stimulations are necessary or sufficient to saturate this index. Some of these questions could be addressed with the dataset of Figure 3 by measuring this index over different epochs of the imaging session (from early to late) to estimate the dynamics of the ongoing plasticity process (in comparison to control mice). Also, is there any behavioural consequence of plasticity/update of functional representation in V1? If plasticity gated by repeated LC activations reproduced visuomotor responses observed in mice that were exposed to visual stimulation only in the virtual environment, then I would expect to see a change in the locomotion behaviour (such as a change in speed distribution) as a result of the repeated LC stimulation. This would provide more compelling evidence for changes in internal models for visuomotor coupling in relation to its behavioural relevance. An experiment that could confirm the existence of the LC-gated learning process would be to change the gain of the visuomotor coupling and see if mice adapt faster with LC optogenetic activation compared to control mice with no ChrimsonR expression. Authors should discuss how they imagine the behavioural manifestation of this artificially-induced learning process in V1.

Regarding the question of plasticity time course: Unfortunately, owing to the paradigm used in Figure 3, the time course of the plasticity will not be quantifiable from this experiment. This is because in the first 10 minutes, the mouse is in closed loop visuomotor VR experience, undergoing optogenetic stimulation (this is the time period in which we record mismatches). We then shift to the open loop session to quantify the effect of optogenetic stimulation on visual flow responses. Since the plasticity is presumably happening during the closed loop phase, and we have no read-out of the plasticity during this phase (we do not have uncoupled visual flow onsets to quantify LMI in closed loop), it is not possible to track the plasticity over time.

Regarding the behavioral relevance of the plasticity: The type of plasticity we describe here is consistent with predictive, visuomotor plasticity in the form of a learned suppression of responses to self-generated visual feedback during movement. Intuitive purposes of this type of plasticity would be 1) to enable better detection of external moving objects by suppressing the predictable (and therefore redundant) self-generated visual motion and 2) to better detect changes in the geometry of the world (near objects have a larger visuomotor gain that far objects). In our paradigm, we have no intuitive read-out of the mouse’s perception of these things, and it is not clear to us that they would be reflected in locomotion speed, which does not differ between groups (manuscript Figure S5). Instead, we would need to turn to other paradigms for a clear behavioral read-out of predictive forms of sensorimotor learning: for instance, sensorimotor learning paradigms in the VR (such as those used in (Heindorf et al., 2018; Leinweber et al., 2017)), or novel paradigms that reinforce the mouse for detecting changes in the gain of the VR, or moving objects in the VR, using LC stimulation during the learning phase to assess if this improves acquisition. This is certainly a direction for future work. In the case of a positive effect, however, the link between the precise form of plasticity we quantify in this manuscript and the effect on the behavior would remain indirect, so we see this as beyond the scope of the manuscript. We will add a discussion on this topic to the revised manuscript.

Finally, control mice used as a comparison to mice expressing ChrimsonR in Figure 3 were not injected with a control viral vector expressing a fluorescent protein alone. Although it is unlikely that the procedure of injection could cause the results observed, it would have been a better control for the interpretation of the results.

We agree that this indeed would have been a better control. However, we believe that this is fortunately not a major problem for the interpretation of our results for two reasons:

1. The control and ChrimsonR expressing mice do not show major differences in the effect of optogenetic LC stimulation at the level of the calcium responses for all results in Figure 3, with the exception of the locomotion modulation indices (Figure 3I). Therefore, in terms of response size, there is no major effect compared to control animals that could be caused by the injection procedure, apart from marginally increased transient responses to visual flow onset – and, as the reviewer notes, it is difficult to see how the injection procedure would cause this effect.

2. The effect on locomotion modulation index (Figure 3I) was replicated with another set of mice in Figure 4C, for which we did have a form of injected control (‘Low ChrimsonR’), which did not show the same plasticity in locomotion modulation index (Figure 4E). We therefore know that at least the injection itself is not resulting in the plasticity effect seen.

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Author Response

Reviewer #2 (Public Review):

Weaknesses: The authors do not make a direct link between TOR and REPTOR2 signalling. This seems important since REPTOR2 is a novel gene that arose from the duplication of REPTOR.

We have added several experiments to strengthen the connection between TOR and REPTOR2, and determined the effect of co-silencing of TOR and REPTOR2 on autophagy and proportion of the winged morph. Please see the details below in your comments point 3.

Author Response

Reviewer #2 (Public Review):

This paper has collected an impressive data set of the visual response properties of neurons in the visual layers of the mouse superior colliculus. There are 3 main findings of the study. First, the authors identify 24 functional classes of neurons based on the clustering of each neuron's visual response properties. Second, unlike in the retina where each cell type is regularly spaced, functional classes in the superior colliculus appear to cluster near each other. Third, visual representation has a lower dimensionality in the superior colliculus compared to the retina. The dataset has the potential to support the conclusions of the paper, but further analysis is required to make the claims convincing.

Strengths:

The main strength of the paper is its impressive dataset of more than 5000 neurons from the visual layers of the superior colliculus. This data set includes recordings from both an interesting set of genetically labelled classes of cells and from a reasonably large portion of the superior colliculus. This dataset offers the opportunity to support the major claims of the paper. This includes i) the identification of 24 functional classes of neurons, ii) the intriguing possibility that functional classes form local patches within the superior colliculus and iii) that the representation of visual information in the superior colliculus has a lower dimensionality compared to the retina.

Weaknesses:

The weakness of the paper is that its main claims are not adequately supported by the presented data or analysis. First, support for the existence of 24 functional classes is not clear enough. Our major concern is that it is not clear that each class of neurons was distributed across different mice. Are certain cell types overrepresented in individual animals, or do you find examples of each cell type in most animals?

The new Supplementary Figure 7G shows how individual mice contribute to the functional types for all neurons. Further, the new Supplementary Figure 12 shows the receptive field locations derived from recordings in each of the animals.

In addition, it should be made explicit how the responses of each genetically labeled class of neurons are distributed among the 24 functional clusters.

We have added a new Figure 5D to show this.

Second, the analysis of the spatial clustering of functional cell types is not complete. Do the same functional clusters sample the same retinotopic locations in different mice? How are clusters of the functional type distributed in visual space?

Please see our point-by-point responses below to the concerns.

Third, the lower dimensionality of representation in the superior colliculus may be the result of selective projections of retinal ganglion cells, not all retinal ganglion cell types project to the superior colliculus. Please estimate the dimensionality of the visual representation of those retinal ganglion cell types that projects to the superior colliculus.

Certainly part of the dimensionality reduction may come from the incomplete retino-geniculate projection; we have added discussion on this topic.

Author Response

Reviewer #1 (Public Review):

In this manuscript, the authors describe a one-step genome editing method to replace endogenous EB1 with their previously-developed light-sensitive variant, in order to examine the effect of acute and local optogenetic inactivation of EB1 in human neurons. They then attempt to assess the effects of EB1 inactivation on microtubule growth, F-actin dynamics, and growth cone advance and turning. They also perform these experiments in neurons that are lacking EB3, in order to determine whether EB1 can function in a direct and specific way without possible EB3 redundancy.

First, the experiments depicting the methodology are rigorous and compelling. Most previous studies of +TIP function use knockout or knockdown studies in which the proteins are inactivated over many hours or days in non-human systems. This is the first study to acutely and locally inactivate a +TIP in human neurons. While this group previously published the effects of replacing endogenous EB1 with the light-sensitive variant, the novelty in this current study is that they use a one-step gene editing replacement method (using CRISPR/Cas9) along with using human neurons derived from iPSCs. After proving their new experimental system works, the authors next seek to test the effect that acutely inactivating EB1 (alongside chronic EB3 knockdown) has on microtubule dynamics, and they observe a marked reduction in MT growth and MT length. They then seek to investigate whether F-actin dynamics are immediately affected by EB1 inactivation.

While measured F-actin flow rates are not significantly affected, which leads the authors to conclude that EB1 inactivation does not have any immediate effect, the included figures and movies show a different phenotype, which is not discussed. Finally, they examine the effect of EB1 inactivation on growth cone advance and growth cone turning, and find that both are affected. However, the lack of certain controls in these final experiments (specifically for Figures 3, 4, and 5) reduces the strength of their findings.

Thus, the first part of this paper describing the new methodology is very compelling and should be of interest to a wide readership, while the second part describing the functional analysis is mostly solid, with very high-quality imaging data. However, additional analysis and controls would be needed to increase confidence in their conclusions.

1) Analysis of F-actin dynamics is not thorough, and their claim is not completely supported by the data. Figure 3 only depicts F-actin dynamics data from growth cones of π-EB1 EB3-/- i3Neurons and does not [include] control growth cones (to compare dark and light conditions). While their conclusion is that F-actin dynamics are not affected, there do appear to be immediate changes in the F-actin images, other than flow rates. For example, the F-actin bundles do not appear to emanate straight out with the light condition, compared to the dark condition. There also appears to be more F-actin intensity in the transition domain of the growth cone, compared to the dark condition. If the reason is due to the effects of four minutes of blue light exposure, this would be made clear by doing this experiment with control growth cones as well.

In Figure 3, we wanted to specifically test if π-EB1 photoinactivation has an immediate effect on growth cone leading edge actin polymerization (for example because of rapid changes in Rho GTPase activity) by measuring F-actin retrograde flow. Because of photobleaching, these experiments are limited to relatively short time-lapse data sets, and within 4-5 min of blue light exposure, we found no significant difference between the dark and light conditions. As requested by this and another reviewer, we added a few more data points as well as a wild-type control. Statistical analysis by ANOVA shows no difference in retrograde flow between any of the four groups.

We did not see a consistent difference in overall F-actin organization after a few minutes of blue light, and we now include control and π-EB1 growth cones in Fig. 3 that are more similar to one another with the dark image shown more immediately before blue light exposure. The growth cone that we had in the original figure (and that remains in Video 5 to illustrate retrograde flow and how dynamic these growth cones are) was a poor choice for this figure as it undergoes quite dramatic F-actin reorganization before the blue light is turned on, and the morphology immediately before blue light exposure is much more similar to the growth cone during blue light compared with the -5 min time point that we had originally shown.

Lastly, the apparent relocalization of F-actin to the growth cone center is seen in both control and experimental conditions and we believe that has to do with photobleaching of the F-actin probe at the relatively high frame rates required to observe retrograde flow. We agree with the reviewer that it is important to know this, and we included a note in the figure legend.

2) Analysis of the effect of EB1 inactivation on growth cone advance and growth cone turning. Figure 4C, showing the neurite unable to cross the blue light barrier, is potentially quite compelling data, but it would be even more convincing if there were also data showing that the blue light barrier has no effect on a control neurite. Given that a number of previous recent studies have shown a detrimental effect of blue light on neurons, it seems important to include these negative controls in this current study.

The experiment growing neurites on a micropatterned laminin surface in combination with photoinactivation in (now) Figure 4D is incredibly low throughput but serves to illustrate repeated retraction from blue light over many hours of imaging. To show that blue light barriers do not affect control cells we have instead included a quantification of the retraction response of control and π-EB1 neurites growing randomly on a laminin-coated surface (not micropatterned stripes) in new Fig. 4C. It is also worth noting that the dose of blue light used for π-EB1 photoinactivation is much lower than what is typically used for fluorescence imaging (we analyzed and discussed this in great detail in our original π-EB1 publication), and especially in experiments with a blue light barrier, cells are not exposed to any blue light before they hit the barrier.

3) This concern also holds true for the final experiment, in which the authors examine whether localized blue light would lead to growth cone turning. The authors report difficulty with performing this technically challenging experiment of accurately targeting the light to only a localized region of the growth cone. Thus, the majority of the growth cones (72%) were completely retracted, and so only a small subset of growth cones showed turning. However, this data would be more compelling if there were also a control condition of blue light with neurons that are not expressing the light-inactivated EB1. Another useful control would be to examine whether precise region-of-interest blue light leads to localized loss of EGFP-Zdk1-EB1C on MT plus-ends within the growth cone, or if the loss extends throughout the growth cone. Either outcome would be helpful to potential readers.

We modified Fig. 5 to include control i3Neurons in this experiment. We also included a supplement to Fig. 5 showing that π-EB1 photodissociation remains localized to the blue light-exposed region. However, because in our π-EB1 line the C-terminal π-EB1 half is EGFP-tagged, we cannot show before and after images of local π-EB1 photodissociation.

Reviewer #3 (Public Review):

The major strength of the study was the approach of using photosensitive protein variants to replace endogenous protein with the 1-step Crispr-based gene editing, which not only allowed acute manipulation of protein function but also mimicked the endogenous targeted protein. However, the same strategy has been used by the same first author previously in dividing cells, somewhat reducing the novelty of the current study. In addition, the results obtained from the study were the same as those from previous studies using different approaches. In other words, the current study only confirmed the known findings without any novel or unexpected results. As a result, the study did not provide strong evidence regarding the advantage of the new experimental approach in our understanding of the function of EB1. Some specific comments are listed below.

1) In Figure 1, to show that the photosensitive EB1 variant did not affect stem cell properties and their neuronal differentiation, Oct4 staining and western blot of KIF2C and EB3 were not strong evidence. Some new experiments more specifically related to stem cell properties or iPSC-derived neurons are necessary.

While we did not attempt to fully characterize stemness in our π-EB1 edited i3N lines, we believe, most importantly, we show that π-EB1 i3N hiPSCs differentiate normally into i3Neurons. We show this morphologically as well as by immunoblotting and RT-qPCR experiments looking at marker proteins also including DCX, a well-established neuronal differentiation marker. Although not directly related to stemness, we included one additional RT-qPCR experiment more carefully analyzing the expression level of π-EB1 in the edited lines compared with EB1 in control i3N hiPSCs (new Fig. 1E).

In addition, the effect of EB1 inactivation on microtubule growth was quantified in stem cells but not in differentiated neurons, which supposed to be the focus of the study.

Quantification of MT dynamics in the hiPSCs parallels our previous experiments in cancer cell lines to demonstrate that π-EB1 photoinactivation had a similar inhibitory effect on MT growth in interphase cells. This serves as an additional control that our new system works as expected. Because of our inability to efficiently transfect i3Neurons, we could not measure MT growth in i3Neurons with the same method (i.e. automated EB1N tracking). However, as further outlined below we have added a quantification of MT growth rates in i3Neuron growth cones by additional manual tracking of SPY555-tubulin-labelled growth cone MTs after at least one minute of blue light exposure.

In Figure S2D, quantification is needed to show the effect of blue light-induced EB1 inactivation in growth cones.

Fig. 1 – supplement 2D (together with Video 3, and Fig. 2A) is simply to illustrate that the C-terminal π-EB1 half dissociates in blue light as expected. We previously characterized the kinetics of π-EB1 photodissociation and do not think redoing this would add substantially to the current manuscript. The remainder of the manuscript, however, examines the functional consequences of π-EB1 photoinactivation in i3Neurons.

2) In Figure 2, the effect of blue light on microtubule retraction in the control cells was examined, showing little effect. However, it is still unclear if the blue light per se would have any effect on microtubule plus end dynamics, a more sensitive behavior than that of retraction. In Figure 2C, the length of individual microtubules in different growth cones was presented, showing microtubule retraction after blue light. Quantification and statistical analysis are necessary to draw a strong conclusion.

Figure 2 shows that growth cone MTs in π-EB1 lines shorten in response to blue light and we did this by analyzing MTs that were visible in a short time window before and after blue light exposure. In response to another reviewer’s comment, we have redesigned this figure to better illustrate this result. We have now included statistical analysis comparing relative MT length 20 s before and during blue light exposure. In control cells that was not statistically significantly different. We also report statistical difference between control and π-EB1 lines at the 20 s by ANOVA in the text. Lastly, we also measured MT growth rates after at least one minute of blue light exposure showing that MT growth is greatly attenuated in π-EB1 lines (new Fig. 2D).

The results showed that EB3 did not seem to contribute to stabilizing microtubules in growth cones. It was discussed that EB3 might have a different function from that of EB1 in the growth cone, although they are markedly up-regulated in neurons. In the differentiated neuronal growth cones examined in the study, does EB3 actually bind to the microtubule plus ends? In the EB3 knockout cells without the blue light, the microtubules were stable, indicating that EB3 had no microtubule stabilization function in these cells. Is such a result consistent with previous studies? If not, some explanation and discussion are needed.

Other papers have shown that EB3 localizes to growth cone MT ends; for example, in rat cortical neurons (Poobalasingam et al., 2022). We did not test if endogenous EB3 is present on MT ends in i3Neurons, but transfected EB3 certainly is. Interestingly, it was reported by multiple groups that EB1 and EB3 do not bind to the exact same place near MT ends. EB3 trails behind EB1, which would be consistent with functional differences especially in controlling MT growth. We have expanded the discussion of such differences in the text, and thank Phillip Gordon-Weeks, who reminded us of this in a comment on the bioRxiv preprint.

3) In Figure 3, for the potential roles of EB1 on actin organization and dynamics, only the rates of retrograde flow were measured for 5 min. and no change was observed. However, based on the images presented, it seemed that there was a reduced number of actin bundles after blue light and the actin structure was somewhat disrupted. Some additional examination and measurement of actin organization are necessary to get a clear result.

This point was also raised by reviewer #1, and we now include images and quantification of retrograde flow in control growth cones and we increased the number of data points. We still see no difference in retrograde flow between all these groups. The original π-EB1 growth cone in Fig. 3A was a poor example because it underwent large morphological changes before the blue light was even turned on and just before light exposure is a lot more like the end point image. We therefore replaced this image with a different growth cone that is more similar to the wild-type growth cone shown, and also show images more immediately before blue light exposure. The bottomline is that we do not see a consistent difference in overall F-actin organization after a few minutes of blue light.

4) In Figure 4, the effect of blue light and EB1 inactivation on neurite extension need to be quantified in some way, such as the neurite length changes in a fixed time period, and the % of growth cones passing the blue light barrier compared with growth cones of the control cells.

We have included a statistical comparison (by ANOVA) at the 15 min time point, and a quantification of neurite retraction of growth cones encountering a blue light barrier.

5) For the quantification of growth cone turning, a control condition is needed to show that blue light itself has no effect on turning.

We have also added a control experiment to Fig. 5.

Author Response

Reviewer #1 (Public Review):

1) The role of increased temperature on immunity and homeostasis in cold-blooded vertebrates is an understudied yet important field. This work not only examines how immunity is impacted by fever, but also incorporates an infection model and examines resolution of the response. This work can serve as a model for other groups interested in the study of hyperthermia and immunity.

Thank you very much.

2) Generally speaking, I agree with the authors' strategy and interpretations of the data.

• In the Introduction, the authors chose to begin with how fever in endotherms impact the immune system. Considering that this work exclusively examines the response of a teleost (goldfish), the authors might consider flipping the way they present this work. After all, cold-blooded vertebrates rely on this response because of their basic physiology.

We chose to begin with a description of fever in endotherms because we know less about those immune mechanisms impacted by fever in ectotherms. The goal was to provide points of comparison based on published datasets. Indeed, we also expect differences between cold- and warm-blooded vertebrates based on their basic physiologies. However, it is interesting that despite different physiologies and thermoregulatory strategies, common biochemical pathways appear to regulate fever across cold- and warm-blooded vertebrates. This is now captured more clearly in the Introduction section (lines 134-136). Added support also comes from the work that we present in this study, including fever inhibition experiments using ketorolac tromethamine (lines 244-253; Figure 3C).

3) I thought the set up of the work in figure 1 was innovative and could provide an example of how to study such a problem.

Thank you. Very much appreciated.

4) Figure 2 was (to me) unexpected. One would not expect such tight response to hyperthermia and infection. This experiment in and of itself was quite interesting, and worth following up in future experiments (by the authors and other groups).

The level of homogeneity in the behavioural responses shown in Figure 2 was a big part of why we pursued this work. It was striking that fish would display such consistency in behaviour during the febrile window, regardless of whether they were evaluated in groups or individually. To us, this suggested that the temperature chosen and the kinetics of this thermal preference are central for modulation of downstream biological processes. Added support for the importance of precise thermal selection comes from "failed" experiments during this study where incoming aquatic facility water temperatures fluctuated due to factors outside of our control. This caused temporary disruption to the temperatures available to these fish in the annular thermal preference tank. In these cases, we noted disruption of both classical behaviours shown in Figure 2 as well as downstream benefits.

• The other work, on the response to infection and the resolution of infection were unique to this paper, and (sorry to be repetitive) can be an example of how to devise such studies.

Thank you.

• On the other hand, I am not sure this is a study of "fever." That implies how increased temperature impacts immunity and resolution in endotherms. Perhaps the authors could temper the comparisons between cold- and warm-blooded vertebrates regarding the response to hyperthermia.

We believe that for those mechanisms that are evolutionarily conserved, the teleost system will offer an opportunity for novel insights into the effects of fever induction and disruption. Indeed, this animal model offers multiple advantages. But we agree that much work remains to establish the extent of this conservation and now highlight this issue more clearly (lines 454-455).

An additional note on hyperthermia versus fever: although both terms are sometimes used interchangeably in the literature, we make a distinction between them. Hyperthermia captures an increase in core body temperature. However, this alone is not sufficient to engage the CNS (representative results shown in Figure 3-figure supplement 1). Consistent with prior descriptions of fever (e.g. Nat Rev Immunol (2015)15:335-49; Arch Intern Med (1998)158:1870-81), we also show that our model results in CNS engagement (Figure 3A), induces systemic pyrogen release (Figure 3B), triggers classical sickness behaviours (Figure 2), and promotes immune function (Figures 4-7).

Author Response

Reviewer 1 (Public Review):

The authors in this manuscript investigate the effect of co-substrate cycling on the metabolic flow. The main finding is that this cycling can limit the flux through a pathway. The authors examine implications of this effect in different simple configurations to highlight the potential impact on metabolic pathways. Overall, the manuscript follows logical steps and is accessible. Once the main point-reduction in flux of a pathway with limited pool of a cycled co-substrate-is established, some of the following steps become expected (e.g. the fraction of the flux in a branched pathway). Nevertheless, it is understandable that the authors have picked a few simple examples of the metabolic network motifs to highlight the implications. The results presented in the manuscript overall support the conclusions. One weakness is that some of the details of the assumptions (e.g. the choices of rates) are not explicitly spelt out in the manuscript. This work is impactful because it brings into light how cycling of some of the intermediates in a pathway can influence metabolic fluxes and dynamics. This is a factor in addition to (and separate from) reaction rates which are often considered as the main driver of metabolic fluxes.

We thank the reviewer for this accurate summary. Regarding the effect of parameters on the presented results, we note that the first part of the results are based on analytical solutions provided in the Appendix (formerly the SI). These results are given as inequalities comprising parameters, allowing direct evaluation of parameter effects. We have now made this point explicit in the presentation of the results.

In the second part of the results, we utilise numerical simulations and in this case, the observed results can possibly depend on parameters. We have explored effects of key parameters, that is kin and total substrate concentration through presented 'phase diagram' style figures - see Figure 2 and 4. For additional parameters, we have now included additional simulations exploring their effects - e.g. see Appendix - Figure 11 and Appendix – Figure 13.

Reviewer 2 (Public Review):

The cycling of "co-substrates" in metabolic reactions is possibly a very important but often overlooked determinant of metabolic fluxes. To better understand how the turnover dynamics of co-substrates affect metabolic fluxes the authors dissect a few metabolic reaction motifs. While these motifs are necessarily much simpler than real metabolic networks with dozens or hundreds of reactions, they still include important characteristics of the full network but allow for a deeper mathematical analysis. I found this mathematical approach of the manuscript convincing and an important contribution to the field as it provides more intuitive insights how co-substrate cycling could affect metabolic fluxes. In the manuscript, the authors stress particularly how the pool sizes of co-substrates and the enzymes involved in the cycling of those can constrain metabolic fluxes but the presented results also go substantially beyond this statement as the authors further illustrate how turnover characteristics of substrates in branches/coupled reactions can affect the ratio of produced substrates.

The authors further present an analysis of previously published experimental data (around Figure 3). This is a very nice idea as it can in principle add more direct proof that the cycling of co-substrates is indeed an important constraint shaping fluxes in real metabolic networks and (instead of being merely a theoretical phenomena which occurs only in unphysiological parameter regimes). However, the way currently presented, it remained unclear to which extent the data analysis is adding convincing support that co-cycling substantially constrains metabolic fluxes. Particularly, it remains unclear for which organisms and conditions the used experimental dataset holds, how it has been generated, and with what uncertainty different measured values come. For example, the comparison requires an estimation of v_max. How can these values determined in-vivo? Are (expected) uncertainties sufficiently low to allow for the statement that fluxes are higher than what enzyme kinetics predict? Furthermore, I am wondering to which extent the correlations between co-substrate pool levels and flux is supporting the idea that co-substrate cyling is important. The positive relation between ATP/AMP/ADP levels for example, is a nice observation. However, it remains a correlation which might occur due to many other factors beyond the limitations of cosubstrate cycling and which might change with provided conditions.

We thank the reviewer for this accurate summary. Although, we would like to clarify that we do not observe nor analyse any relation between ATP/AMP/ADP levels. Rather, in the analysis presented in Fig. 3B-D, we are looking at the relation between fluxes in co-substrate utilising reactions and the pool size of that co-substrate (e.g. total ATP, AMP, and ADP level for reactions utilising any one of these three co-substrates).

In their summary, the reviewer raises several valid points about the data analysis and its possible limitations. We address them here point by point:

How are Vmax values gathered/estimated? We have now added more information regarding how the Vmax values were gathered and from which organisms and conditions. Specifically, we used previously published values of Vmax from (Davidi et al. 2016) where it was estimated by multiplying the in vitro determined kcat by the concentration of the enzyme from proteomic measurement under different conditions - all for model organism Escherichia coli. See also below, reply to recommendation 2.

Are (expected) uncertainties sufficiently low? It is difficult to have an estimate for the uncertainty since much of the error in the previous analysis probably comes from the fact that the kinetic parameters determined in vitro are used to estimate fluxes under in vivo conditions - the main source of error is expected to be this discrepancy, which is hard to estimate. However, since the plot is in log-scale, we highlight only gaps that are more than 1 order of magnitude (dashed diagonal lines) and hopefully the uncertainty is lower than that. Furthermore, high uncertainty would probably contribute equally to over- and under-estimating the maximal flux, while we can clearly see that the flux rarely exceeds the Vmax. We have now included a statement in the revised text capturing this point.

Correlations offer weak evidence. Unfortunately, as we do not have measurements on co-substrate pool sizes and cycling kinetics under all conditions, our analyses of experimental data from cycling-involving reactions are admittedly limited. However, they do show that (1) measured fluxes are lower than those predicted by kinetics of the primary enzyme (i.e. enzyme involved in co-substrate and substrate conversion) alone, and (2) there is - for some cycling-involving reactions - a correlation between flux and co-substrate pool size. Both observations could indicate co-substrate pool sizes and/or co-substrate cycling dynamics being limiting. As the reviewer points out, we cannot state this as a certainty.

Other possible limitations include thermodynamic effects, i.e. limitation by the concentration of both substrate or product, or substrate saturation. We already explored the latter possibility and found that there is still a lower flux when taking into account the primary substrate saturation (see Fig. S6). The former effect is very difficult to analyse without more data, as calculating reaction thermodynamics requires knowledge of concentrations for all substrates and products, as well as enzyme Michaelis-Menten constants in both forward and backward directions. This information is currently not available except for few of the reactions among the ones we analysed. Nevertheless, to give as much insight as possible on the thermodynamic effect, we added a new figure (Appendix – Figure 8) where we plot the physiological Gibbs free energy (is calculated assuming that all reactants are at 1 mM and pH=7) against the normalized flux. The plot shows that although in few cases, such as malate dehydrogenase (MDH), the normalised flux seems to be greatly reduced by the thermodynamic barrier, the general picture is that there is little correlation between physiological Gibbs free energy and normalised flux. We have now included the resulting figure and associated discussion in the revised manuscript.

In relation to all these points on data-based support of the theory, we would also like to point out the comments from reviewer 3 and the fact that our theoretical work provides motivation for further future experimental studies of co-substrate cycling dynamics. Our main analysis about co-substrate dynamics becoming limiting is based on analytical solutions. These solutions provide an inequality of system parameters relating pathway influx, co-substrate pool size, and co-substrate related enzymatic parameters. When this inequality is satisfied, there will be flux limitation due to cosubstrate cycling. Future experimental studies can now be devised to explore this inequality under different conditions by measuring the key parameters more explicitly. This key point and aspects of the above replies are incorporated at the relevant points in the main text. In addition, we have included a new paragraph in the Discussion section (see reply to second recommendation of reviewer 3) and the following paragraph at the end of the Results section:

In summary, these results show that for reactions involving co-substrate cycling (1) measured fluxes are lower than those predicted by kinetics of the primary enzyme (i.e. enzyme involved in substrate conversion) alone, and (2) there is - for some reactions - a correlation between flux and co-substrate pool size. Both observations could indicate co-substrate pool sizes and/or co-substrate cycling dynamics being a main limiting factor for flux. We can not state this as a certainty, however, as there are possibly other factors acting as the extra limitation, including thermodynamic effects. These points call for further experimental analysis of co-substrate cycling within the study of metabolic system dynamics.

Reviewer 3 (Public Review):

In the study, the authors present a mathematical framework and data analysis approach that revisits an "old" idea in cell physiology: The role of co-substrate cycling as potential key determinant of reaction flux limits in enzyme-catalyzed reaction systems. The aim of the study is to identify metabolic network properties that indicate potential global flux regulatory capacities of co-substrate cycling.

The authors approached this aim in two steps. First, a mathematical framework, which is based on ODEs was developed and which reflects small abstract metabolic pathways including kinetic parameters of the involved reactions. While the modeled pathways are abstract, the considered pathway motifs are motivated by structures of known existing pathways such as glycolysis (as example of a linear pathway) and certain amino acid biosynthesis pathways (as example of branched pathways). The developed ODE-based models were used for steady state analysis and symbolic and numerical simulations of flux dynamics. As a main result of the first step, the authors highlight that co-substrate cycling can act as mechanism which limits specific metabolic fluxes across the metabolic network and that co-substrate cycling can facilitate flux regulation at branching points of the network. Second, the authors re-analyzed data on flux rates (experimental measurements and flux-balance-analysis predictions) from previous publications in order to assess whether the predicted role of co-substrate cycling could explain the observed flux distributions. In this data analysis, the author provide evidence that the fluxes of specific reactions in central metabolism could be constrained by co-substrate cycling, because their observed fluxes are often lower than expected by the kinetics of the corresponding enzymes.

A particular strength of the study is that the authors highlight that co-substrates are not limited to ATP and NAD(P)H, but could include a range of other metabolites and which could also be organism-specific. Building on this broad definition of cosubstrates, the authors developed an abstract mathematical framework that can be used to study the general potential 'design principle' of co-substrate cycling in cellular metabolism and to adapt the framework to study different co-substrates in specific organisms in future works.

Experimental data (i.e. measured fluxes using mass-spectrometry data and labeled substrates) that is available to date is limited and therefore also limits the broad evaluation of the developed mathematical framework across various different organisms and environmental conditions. However, with advances in metabolomics and derived metabolic flux measurements, the mathematical framework will serve as a valuable resource to understand the potential role of co-substrate cycling in more biological systems. The framework might also guide new experiments that generate data for a systematic evaluation of when and to what extent co-substrate cycling governs flux distributions, e.g. depending on growth rates or response to environmental stress.

We thank the reviewer for this accurate summary. We agree with the reviewer's final comments on limitations of current testing of our theory, due to limitations in existing data, and that this analysis will now motivate further experimental study of co-substrate dynamics. We have already included revisions of the manuscripts to further highlight and discuss limitations of the data-based analysis.

Author Response

Reviewer #1 (Public Review):

This study investigates the psychological and neurochemical mechanisms of pain relief. To this end, 30 healthy human volunteers participated in an experiment in which tonic heat pain was applied. Three different trial types were applied. In test trials, the volunteers played a wheel of fortune game in which wins and losses resulted in decreases and increases of the stimulation temperature, respectively. In control trials, the same stimuli were applied but the volunteers did not play the game so that stimulation decreases and increases were passively perceived. In neutral trials, no changes of stimulation temperature occurred. The experiment was performed in three conditions in which either a placebo, or a dopamineagonist or an opioid-antagonist was applied before stimulations. The results show that controllability, surprise, and novelty-seeking modulate the perception of pain relief. Moreover, these modulations are influenced by the dopaminergic but not the opioidergic manipulation.

Strengths

• The mechanisms of pain relief is a timely and relevant basic science topic with potential clinical implications.

• The experimental paradigm is innovative and well-designed.

• The analysis includes advanced assessments of reinforcement learning.

Weaknesses

• There is no direct evidence that the opioidergic manipulation has been effective. This weakens the negative findings in the opioid condition and should be directly demonstrated or at least critically discussed.

We agree that we cannot provide direct evidence on the effectiveness of the opioidergic manipulation in our study. However, previous literature strongly suggests that a dose of 50 mg naltrexone (p.o.) is effective in blocking 𝜇-opioid receptors in humans. Using positron emission tomography, Weerts et al. (2013) found a blockage of 𝜇-opioid receptors of more than 90% with 50 mg naltrexone (p.o.) although given repeatedly 4 days in a row. In addition, convincing effects on behavioral functions have been reported with comparable doses that support the efficacy of the opioidergic manipulation. For example, Chelnokova et al. (2014) found attenuating effects of 50 mg naltrexone (p.o.) on wanting as well as liking of social rewards, implicating the involvement of endogenous opioids in the processing of rewarding stimuli. The same dose was also found to attenuate reward directed effort exerted in a value-based decision-making task (Eikemo et al., 2017). Moreover, 50mg of naltrexone (p.o.) have been shown to reduce endogenous pain inhibition induced by conditioned pain modulation (King et al., 2013) and to reduce the perceived pleasantness of pain relief (Sirucek et al., 2021). Thus, based on the available literature we assume the effectiveness of our opioidergic manipulation. A corresponding reasoning including a note of caution on the of the lack of a direct manipulation check of the opioidergic manipulation can be found in the manuscript in the Discussion:

“The doses and methods used here are comparable to those used in other contexts which have identified opioidergic effects. Using positron emission tomography, Weerts et al. (2013) found a blockage of opioid receptors of more than 90% by 50 mg of naltrexone (p.o.) in humans given repeatedly over 4 days. In addition, effects on behavioral functions have been reported with comparable doses that support the efficacy of the opioidergic manipulation. Chelnokova et al. (2014) found attenuating effects of 50 mg naltrexone (p.o.) on wanting as well as liking of social rewards, implicating the involvement of endogenous opioids in the processing of rewarding stimuli. The same dose was also found to attenuate reward directed effort exerted in a value-based decision-making task (Eikemo et al., 2017). Moreover, 50 mg of naltrexone (p.o.) have been shown to reduce endogenous pain inhibition induced by conditioned pain modulation (King et al., 2013). Thus, based on the literature we assume that the opioidergic manipulation was effective in this study, although we do not have a direct manipulation check of this pharmacological manipulation. Despite its effectiveness in blocking endogenous opioid receptors, the effect of naltrexone on reward responses was found to be small (Rabiner et al., 2011). Hence, a lack of power may have limited our chances to find such effects in the present study.”

• The negative findings are exclusively based on the absence of positive findings using frequentist statistics. Bayesian statistics could strengthen the negative findings which are essential for the key message of the paper.

We agree with the reviewers that the power may not have been sufficient to detect potentially small effects of the pharmacological manipulations. The power calculation was based on the design and the medium effect size found in a previous study using a comparable experimental procedure for assessing pain-reward interactions (Becker et al., 2015). To acknowledge this weakness, we clarified in the manuscript the description of the a priori sample size calculation as follows:

“The power estimation was based on the design and the finding of a medium effect size in a previous study using a comparable version of the wheel of fortune game without pharmacological interventions (Becker et al., 2015). The a priori sample size calculation for an 80% chance to detect such an effect at a significance level of 𝛼=0.05 yielded a sample size of 28 participants (estimation performed using GPower (Faul et al., 2007 version 3.1) for a repeated-measures ANOVA with a three-level within-subject factor)."

Further, we did not aim to claim that endogenous opioids do not affect the perception of pain relief. Our phrasing in describing the results was in several instances too bold. The aim of the pharmacological manipulations was to investigate effects of dopamine and endogenous opioids on endogenous modulation of perceived intensity of pain relief. Here, we expected dopamine to enhance such endogenous modulation and naltrexone to reduce this modulation. The higher average pain modulation under naltrexone compared to placebo found in VAS ratings (naltrexone: -10.09, placebo: -7.31, see Table 1) suggests an increase in pain modulation by naltrexone compared to placebo, although this did not reach statistical significance, which is the opposite of what we had expected (see comment #11). Therefore, we concluded that we have no evidence to support our hypothesis of reduced endogenous modulation of pain relief by naltrexone. We do not want to claim that there are no effects of endogenous opioids on pain modulation. Although Bayesian statistics might be used to support such an interpretation, we think this might be misleading in our context here due to the considerations on the lack of power (which also affects null-hypothesis testing in Bayesian statistics) and the lack of a direct manipulation check mentioned above. Since we expected opposite effects of levodopa and naltrexone on pain modulation, we did not intend to compare these effects directly to avoid a distortion of the results. According to our hypotheses, we expected to see increased modulation of pain relief with enhanced dopamine availability and decreased modulation of pain relief with blocking of opioid receptors (see also comment #11). However, we had no a priori assumptions on potential differences in the absolute changes induced by the drug manipulations. Based on these considerations, we did now not include further direct comparisons of the effects of both drugs. Rather, we carefully went through the manuscript to tone down the descriptions and interpretations of our null findings and adjusted the respective section of the discussion to better reflect this interpretation.

• The effects were found in one (pain intensity ratings) but not the other (behaviorally assessed pain perception) outcome measure. This weakens the findings and should at least be critically discussed.

We thank the reviewers for highlighting this important aspect. We have considered the two outcome measures as indicative of two different aspects or dimensions of the pain experience, based also on previous results in the literature. Within our procedure, the ratings indicate the momentary perception of the stimulus intensity after phasic changes in nociceptive input (outcomes), while the behavioral measure indicates perceptual within-trial sensitization or habituation in response to the tonic stimulation within each trial. Supporting the assumption of such two different aspects, it has been shown before that pain intensity ratings and behavioral discrimination measures can dissociate (Hölzl et al., 2005). In line with the assumption that both outcome measures assess different aspects of the pain experience, a differential effect of controllability on these two outcome measures is conceivable. Similarly, Becker et al. (2015), using a very similar experimental paradigm, did only find endogenous pain facilitation in the losing condition of the wheel of fortune game in pain ratings but not in the behavioral outcome measure, while they found endogenous inhibition in both measures. Compared to Becker et al. (2015), we implemented here smaller changes in stimulation intensity as outcomes in the wheel of fortune game (-3°C vs -7°C for win trials, +1°C vs +5°C for lose trials), potentially resulting in the differential effects here. Nevertheless, we agree that this reasoning needs a more explicit discussion in the manuscript and we included the following sentences to the Discussion section:

“Although we did not assess the affective component of the relief experience, we implemented two outcome measures that are assumed to capture independent aspects of the pain experience: VAS ratings indicate perception of phasic changes (outcomes), while the behavioral measure indicates perceptual within-trial sensitization or habituation in response to the tonic stimulation within each trial. We found enhanced endogenous modulation by controllability and unpredictability in the VAS ratings, in line with the view that endogenous modulation enhances behaviorally relevant information. In contrast, the within-trial sensitization did not differ between the active and passive conditions under placebo. In contrast, in a previous study using a similar experimental paradigm Becker et al. (2015) found a reduction of within-trial sensitization after pain relief outcomes by controllability. Compared to this study, we implemented here smaller changes in stimulation intensity as outcomes in the wheel of fortune (-3 °C vs -7 °C for pain relief), potentially explaining the differential results.“

• The instructions given to the participants should be specified. Moreover, it is essential to demonstrate that the instructions do not yield differences in other factors than controllability (e.g., arousal, distraction) between test and control trials. Otherwise, the main interpretation of a controllability effect is substantially weakened.

Thanks for pointing out that specific information on instructions given to the participants was missing. We agree that factors other than controllability would confound the interpretation of differences between test and control trials. We aimed minimizing nonspecific effects of arousal and/or distraction while still giving all needed information with our instructions (see below). In addition, control and test trials were kept as similar as possible. In order to check for unspecific effects of arousal and/or distraction, we also included lose trials in the game as an additional control condition. For clarifying participants’ instructions, we added the following paragraph to the Materials and methods section: “The participants were instructed that there were two types of trials: trials in which they could choose a color to bet on the outcome of the wheel of fortune and trials in which they had no choice. Specifically, they were told that in the first type of trials they could use the left and right mouse button, respectively, to choose between the pink and blue section of the wheel of fortune. Participants were further instructed that if the wheel lands on the color they had chosen they will win, i.e. that the stimulation temperature will decrease, while if the wheel lands on the other color, they will lose, i.e. that the stimulation temperature will increase. For the second type of trials, participants were instructed that they could not choose a color, but were to press a black button, and that after the wheel stopped spinning the temperature would by chance either increase, decrease, or remain constant.”

In general, both arousal and distraction can be assumed to affect pain perception. If the active condition in the wheel of fortune resulted in higher arousal and/or distraction this should result in comparable effects on intensity ratings in both the win and lose outcomes compared to the passive condition. In contrast, controllability is expected to have opposite effects on pain perception in win and lose trials (decreased pain perception after winning and increased pain perception after losing in the active compared to the passive condition). These opposite effects of controllability are tested by the interaction ‘outcome × trial type’ when fitting separate models for each drug condition, which should be zero if unspecific effects of arousal and/or distraction predominated. Instead, we found a significant interaction in these models, confirming opposing effects of controllability in win and lose outcomes and contradicting such unspecific effects. We added this reasoning, marked in red here, to the Results section to better highlight this line of reasoning, as follows:

“To test whether playing the wheel of fortune induced endogenous pain inhibition by gaining pain relief during active (controllable) decision-making, a test condition in which participants actively engaged in the game and ‘won’ relief of a tonic thermal pain stimulus in the game was compared to a control condition with passive receipt of the same outcomes (Figure 1). As a further comparator the game included an opposite (‘lose’) condition in which participants received increases of the thermal stimulation as punishment. This active loss condition was also matched by a passive condition involving receipt of the same course of nociceptive input. Comparing the effects of active versus passive trials between the pain relief and the pain increase condition (interaction ‘outcome × trial type’) allowed us to test for unspecific effects such as arousal and/or distraction. If effects seen in the active compared to the passive condition were due to such unspecific effects, then actively engaging in the game should affect comparably pain in both win and lose trials. In contrast, if the effects were due to increased controllability, pain inhibition should occur in win trials and pain facilitation in lose trials.”

• The blinding assessment does not rule out that the volunteers perceived the difference between placebo on the one hand and levodopa/naltrexone on the other hand. It is essential to directly show that the participants were not aware of this difference.

We based our assessment of blinding on the fact that for none of the drug conditions the frequency of guessing correctly which drug was ingested was above chance (see Results section, page 8, lines 201ff). In addition, the frequency of side effects reported by the participants did not differ between the three drug conditions, supporting this notion indirectly. However, we agree with the reviewer that this does not rule out completely that participants may have perceived a difference between the placebo and the levodopa/naltrexone conditions. We ran additional analyses to test whether participants were more likely to answer correctly that they had ingested an active drug and whether they were more likely to report side effects in the active drug conditions compared to the placebo condition. In 7 out of 28 placebo sessions (25%) the participants assumed incorrectly to have ingested one of the active drugs. In 12 out of 43 drug sessions (21.8%) the participants assumed correctly that they had ingested one of the active drugs. These frequencies did not differ between placebo sessions on the one hand and the levodopa and naltrexone active drug sessions on the other hand (𝜒)(1) = 0.11, p = 0.737). In 9 out of 28 placebo sessions (32.1%) and in 23 out of 55 drug sessions (41.8%) participants reported to be tired at the end of the session. The frequency of reporting tiredness did not significantly differ between placebo sessions on the one hand and drug sessions on the other hand (𝜒)(1) = 1.06, p = 0.304). No other side effects were reported. We added the following information, marked in red here, to the Results section:

“In 32 out of 83 experimental sessions subjects reported tiredness at the end of the session. However, the frequency did not significantly differ between the three drug conditions (𝜒)(2) = 2.17, p = 0.337) or between the placebo condition compared to the levodopa and naltrexone condition (𝜒)(1) = 1.06, p = 0.304). No other side effects were reported. To ensure that participants were kept blinded throughout the testing, they were asked to report at the end of each testing session whether they thought they received levodopa, naltrexone, placebo, or did not know. In 43 out of 83 sessions that were included in the analysis (52%), participants reported that they did not know which drug they received. In 12 out of 28 sessions (43%), participants were correct in assuming that they had ingested the placebo, in 6 out of 27 sessions (22%) levodopa, and in 2 out of 28 sessions (7%) naltrexone. The amount of correct assumptions differed between the drug conditions (𝜒)(2) = 7.70, p = 0.021). However, posthoc tests revealed that neither in the levodopa nor in the naltrexone condition participants guessed the correct pharmacological manipulation significantly above chance level (p’s > 0.997) and the amount of correct assumptions did not differ significantly between placebo compared to levodopa and naltrexone sessions (𝜒)(1) = 0.11, p = 0.737), suggesting that the blinding was successful.”

• The effects of novelty seeking have been assessed in the placebo and the levodopa but not in the naltrexone conditions. This should be explained. Assessing novelty seeking effects also in the naltrexone condition might represent a helpful control condition supporting the specificity of the effects in the naltrexone condition.

We thank the reviewer for this interesting suggestion. Indeed, we did not report the association of pain modulation with novelty seeking in the naltrexone condition, because we did not have an a-priori hypothesis for this relationship. We now included correlations for all three drug conditions, testing if higher novelty seeking was associated with greater perceptual modulation in the active vs. passive condition. In line with comment 3, we applied a correction for multiple comparisons here (Bonferroni-Holm correction). This correction caused the correlation in the placebo condition to be no longer significant with an adjusted p-value of 0.073 (r = -0.412), while the correlation stays significant in the levodopa condition (r = -0.551, p = 0.013). Because of a reasonable effect size of the correlation under placebo (i.e. r = -0.412), we still report this correlation to highlight the increase under levodopa, while emphasizing that this correlation not significant We carefully toned down the interpretation of this correlation to reflected the change in significance with the correction for multiple testing.

We added the following information, marked in red here, in the Results section:

“Previous data suggest that endogenous pain inhibition induced by actively winning pain relief is associated with a novelty seeking personality trait: greater individual novelty seeking is associated with greater relief perception (pain inhibition) induced by winning pain relief (Becker et al., 2015). Similar to these results, we found here that endogenous pain modulation, assessed using self-reported pain intensity, induced by winning was associated with participants’ scores on novelty seeking in the NISS questionnaire (Need Inventory of Sensation Seeking; Roth & Hammelstein, 2012; subscale ‘need for stimulation’ (NS)), although this correlation failed to reach statistical significance after correction for multiple comparisons using Bonferroni-Holm method (r = -0.412, p = 0.073). A significant association between novelty seeking and endogenous pain modulation was found in the levodopa condition (r = 0.551, p = 0.013). More importantly, the higher a participants’ novelty seeking score in the NISS questionnaire, the greater the levodopa-related endogenous pain modulation when winning compared to placebo (NISS NS: r = -0.483, p = 0.034 Figure 7). In contrast, higher novelty seeking scores were not correlated with stronger pain modulation induced by winning in the naltrexone condition (r = 0.153, p = 0.381) and the naltrexone induced change in pain modulation showed no significant association with novelty seeking (r = 0.239, p = 0.499). Pain modulation after losing was not associated with novelty seeking in placebo (r = 0.083, p = 0.866), levodopa (r = -0.164, p = 0.783), or naltrexone (r = 0.405, p = 0.133).

No significant correlations with NISS novelty seeking score were found for behaviorally assessed pain modulation in the placebo, levodopa and naltrexone conditions during pain relief or pain increase (|r|’s < 0.35, p’s > 0.238). Similarly, the difference in pain modulation during pain relief or pain increase between the levodopa and the placebo condition and between the naltrexone and the placebo condition did also not correlate with novelty seeking (|r|’s < 0.22, p’s > 0.576).” <br /> We also edited the interpretation of the correlation in the Discussion:

“Overall, all three predictions were largely borne out by the data: relief perception as measured by VAS ratings was enhanced by controllability, unpredictability and showed a medium sized - although not significant - association with the individual novelty-seeking tendency,”

• The writing of the manuscript is sometimes difficult to follow and should be simplified for a general readership. Sections on the information-processing account of endogenous modulation in the introduction (lines 78-93), unpredictability and endogenous pain modulation in the results (lines 278-331) are quite extensive and add comparatively little to the main findings. These sections might be shortened and simplified substantially. Moreover, providing a clearer structure for the discussion by adding subheadings might be helpful.

We have reworked the manuscript to make it easier to follow. Specifically, we reworked the Introduction section to simplify it and to make it more concise. Further, we also shortened the extensive descriptions of modeling procedures that are not central for understanding the main findings. We think that these additions make it easier to follow the manuscript and our line of arguments, and to understand the applied analysis strategies.

• Effect sizes are generally small. This should be acknowledged and critically discussed. Moreover, effect sizes are given in the figures but not in the text. They should be included to the text or at least explicitly referred to in the text.

We agree that the effect sizes we report appear generally small. Importantly, the effect sizes were calculated by dividing differences in marginal means by the pooled standard deviation of the residuals and the random effects to obtain an estimate of the effect size of the underlying population rather than only for our sample. This procedure was used for the purpose of achieving more generalizable estimates. Due to considerable variance between subjects in our sample, this procedure resulted in comparatively small effect sizes. Nevertheless, we think this calculation of effects sizes results in more informative values because they can be viewed as estimates of population effects. We added specific information on the calculation of the effect sizes and a brief explanation that this procedure results in comparatively small effect sizes estimates to the Materials and methods and to the Results section (see below). In addition, we included standardized effect sizes whenever we report the respective post-hoc comparisons in the Results section.

“Effects sizes were calculated by dividing the difference in marginal means by the pooled standard deviation of the random effects and the residuals providing an estimate for the underlying population (Hedges, 2007).” (Materials and methods section)

“We used post-hoc comparisons to test direction and significance of differences in either outcome condition and report standardized effect sizes for these differences. Note that all reported effect sizes account for random variation within the sample, providing an estimate for the underlying population; due to considerable variance between participants in the present study, this results in comparatively small effect sizes.” (Results section)

• The directions of dopamine and opioid effects on pain relief should be discussed.

We amended our explanation of the hypothesis on the expected drug effects. As outlined there, we indeed expected opposite effects of levodopa and naltrexone on endogenous pain modulation in the active vs. the passive condition of the wheel of fortune.

Reviewer #2 (Public Review):

This study used the tonic heat stimulation combined with the probabilistic relief-seeking paradigm (which is a wheel of fortune gambling task) to manipulate the level of controllability and predictability of pain on 30 healthy participants. The authors focused on the influence of controllability and unpredictability on pain relief using pain reports and computational models and examined the involvement of dopamine and opioids in those effects. For that, the authors conducted the three-day experiments, which involved placebo, levodopa (dopamine precursor), and naltrexone (opioid receptor antagonist) administration on separate days. Lastly, the authors examined the relationship between dopamine-induced pain relief and novelty-seeking traits.

This is a strong and well-performed study on an important topic. The paper is well-written. I really enjoyed reading the introduction and discussion and learned a lot. Below, I have a few minor comments.

First, given that the Results section comes before the Methods section, it would be helpful to include some method and experimental design-related information crucial for the understanding of the results in the Results section. For example, how long was the thermal stimulus? What was the baseline temperature? etc. Maybe this information can be included in the caption of Figure 1.

We thank the reviewer for this helpful suggestion. We agree that due to the order of the manuscript sections, more information on experimental design and the statistical analysis strategies should be included in the results section. Accordingly, we included more detailed information on the analysis strategies in the Results section (please see responses to comments #5 & #9). In addition, we added more detailed information on the experimental design and information such as the duration of the stimuli and the baseline temperature, marked in red below, to the caption of Figure 1 (Results section).

“Figure 1: Time line of one trial with active decision-making (test trials) of the wheel of fortune game. Experimental pain was implemented using contact heat stimulation on capsaicin sensitized skin on the forearm. In each trial, the temperature increased from a baseline of 30 °C to a predetermined stimulation intensity perceived as moderately painful. In each testing session, one of the two colors (pink and blue) of the wheel was associated with a higher chance to win pain relief (counterbalanced across subjects and drug conditions). Pain relief (win) as outcome of the wheel of fortune game (depicted in green) and pain increase (loss; depicted in red) were implemented as phasic changes in stimulation intensity offsetting from the tonic painful stimulation. Based on a probabilistic reward schedule for theses outcomes, participants could learn which color was associated with a better chance to win pain relief. In passive control trials and neutral trials participants did not play the game, but had to press a black button after which the wheel started spinning and landed on a random position with no pointer on the wheel. Trials with active decision-making were matched by passive control trials without decision making but the same nociceptive input (control trials), resulting in the same number of pain increase and pain decrease trials as in the active condition. In neutral trials the temperature did not change during the outcome interval of the wheel. Two outcome measures were implemented in all trial types: i) after the phasic changes during the outcome phase participants rated the perceived momentary intensity of the stimulation on a visual analogue scale (‘VAS intensity’); ii) after this rating, participants had to adjust the temperature to match the sensation they had memorized at the beginning of the trial, i.e. the initial perception of the tonic stimulation intensity (‘self-adjustment of temperature’). This perceptual discrimination task served as a behavioral assessment of pain sensitization and habituation across the course of one trial. One trial lasted approximately 30 s, phasic offsets occurred after approximately 10 s of tonic pain stimulation. Adapted from Becker et al. (2015).”

Second, it would be helpful if the authors could provide their prior hypotheses on the drug effects. It could be a little bit confusing that the goal of using these drugs given that levodopa is a precursor of dopamine, whereas naltrexone is the opioid antagonist, i.e., the effects on the target neurotransmitters seem the opposite. Then, I wondered if the authors expected to see the opposite effects, e.g., levodopa enhances pain relief, while naltrexone inhibits pain relief, or to see similar effects, e.g., both enhance pain relief. Clarifying which direction of expected effects would be helpful for novice readers.

We thank the reviewer for pointing out that information on the expected drug effects should be explained in more detail. Indeed, we expected opposite effects of levodopa and naltrexone with respect to the effect of controllability on pain relief. Levodopa, as a precursor of dopamine, enhances dopamine availability and thus, phasic release of dopamine in response to events, for example, the reception of reward. Accordingly, we hypothesized that endogenous modulation by relief outcomes are increased in the active (reward) compared to the passive condition. In contrast, naltrexone blocks opioid receptors and as such it has been reported that naltrexone blocks placebo analgesia as a type of endogenous pain inhibition. Correspondingly, we hypothesized that naltrexone decreases endogenous pain modulation induced by actively winning pain relief compared to the passive condition. We expanded the explanation of these hypotheses in the Introduction section as follows:

“We expected increased dopamine availability to enhance phasic release of dopamine in response to rewards, and hence, to increase the effect of active compared to passive reception of pain relief. In contrast, we expected the inhibition of endogenous opioid signaling to decrease the effect of active controllability on pain relief. The latter is based on the observation that blocking of opioid receptors attenuates other types of endogenous pain inhibition such as placebo analgesia (Benedetti, 1996; Eippert et al., 2009) or conditioned pain modulation (King et al., 2013). “

Third, on the "Behaviorally assessed pain perception" results in Figs. 2D-F, I wonder why the results for the "pain increase" were still positive. Were the y values on the plots the temperature that participants adjusted (i.e., against the temperature right before the temperature adjustment)? or are the values showing the differences from the baseline (i.e., against the baseline temperature)?

The behavioral measure was calculated as the difference in temperatures between the memorization interval at the beginning of the trial (i.e. the predetermined temperature perceived as moderately painful) minus the self-adjusted temperature at the end of the trial so that positive values indicate sensitization (i.e. an increase in sensitivity) and negative values indicate habituation (i.e. a decrease in sensitivity) across the stimulation within on trial (i.e. approx. 30 seconds of stimulation). In general, for a stimulation of approximately 30 seconds with intensities perceived as painful, perceptual sensitization is expected to occur (Kleinböhl et al., 1999).

The outcome of the wheel of fortune game, i.e. the phasic decrease (winning) or increase (losing) in stimulation intensity, should indeed have opposite effects on this sensitization. A decrease in nociceptive input negatively reinforces pain perception, as seen in stronger sensitization in win trials, while an increase in nociceptive input punishes pain perception, as seen in reduced perceptual sensitization in lose trials. Using the a very similar task, Becker et al. (2015) found values indicating habituation within trials with temperature increases in lose outcomes. However, in this previous study, increases of +5°C were used for lose outcomes (as compared to +1 °C in the present study). Thus, in the present study the comparatively small increase in absolute stimulation temperature may not have been sufficient to induce within trial habituation to the tonic heat pain stimulation.

Nevertheless, independent of the effect of the outcome (increase or decrease of the stimulation intensity) our focus was on the additional effect that controllability (active vs. passive condition) had on the perception of the underlying tonic stimulation within each outcome condition (i.e. on the same nociceptive input). Here we expected to see endogenous inhibition after winning and endogenous facilitation after losing in the active compared to the passive condition.

We added more detailed information on the calculation of the behavioral measure and the expected perceptual modulation within each trial due to the stimulus duration in the Methods section as well as in the Results section.

Methods section:

“After this rating, participants had to adjust the stimulation temperature themselves to match the temperature they had memorized at the beginning of the trial. This self-adjustment operationalizes a behavioral assessment of perceptual sensitization and habituation within one trial (Becker et al., 2011, 2015; Kleinböhl et al., 1999). Participants adjusted the temperature using the left and right button of the mouse to increase and decrease the stimulation temperature. The behavioral measure was calculated as the difference in temperatures in the memorization interval at the beginning of each trial minus this selfadjusted temperature at the end of each trial. Positive values, i.e. self-adjusted temperatures lower than the stimulation intensity at the beginning of the trial, indicate perceptual sensitization, while negative values indicate habituation.” Results section:

“Positive values (i.e. lower self-adjusted temperatures compared to the stimulation intensity at the beginning of the trial) indicate perceptual sensitization across the course of one trial of the game, negative values indicate habituation. For tonic stimulation at intensities that are perceived as painful, perceptual sensitization is expected to occur (Kleinböhl et al., 1999). Differences between the outcome conditions (win, lose) reflect the effect of the phasic changes on the perception of the underlying tonic stimulus. Differences between active and passive trials reflect the effect of controllability on this perceptual sensitization within each outcome condition.”

Lastly, I wonder if it is feasible or not, but examining the effects of dopamine antagonists will be helpful for obtaining a more definitive answer to the role of dopamine in information-related pain relief. This could be a good suggestion for future studies.

We thank the reviewer for this suggestion. We agree that antagonistic manipulation of the dopaminergic system could provide further insights and confirm the role of dopamine in shaping pain related perception and behavior. Moreover, we think that bidirectional manipulations of opioidergic signaling could also provide valuable insights and should be used for future research. We added the following sentences to the Discussion section:

“Because the mechanisms underlying learning from pain and pain relief and their recursive influence on pain perception may contribute to the development and maintenance of chronic pain, it is crucial to better understand the roles of dopamine and endogenous opioids in these mechanisms. Accordingly, bidirectional manipulations of both transmitter systems should be used in future studies to better characterize their respective roles in shaping behavior and perception.“

Author Response

Joint Public review:

1) Line 215: The authors state that pairing TCRseq with RNAseq reflects the magnitude of TCR signaling. This is absolutely not the case. TCR sequencing does not reflect TCR signaling strength.

Thanks for the comments and we apologize for the usage of this misleading description. Actually in this part, we were trying to quantitatively assess the activation states of CD8 T cells based on the average expression of previously described activation-related gene signatures1 (also shown in Supplementary file 3). Therefore, TCRseq data was not involved in this analysis and the magnitude of TCR signaling could neither be reflected. We apologize again for this mistake and have corrected the corresponding texts and figures as follows (line 210-217): "Meanwhile, the activation states of CD8 T cell subpopulations were quantitatively assessed based on the average expression of previously described activation-related gene signatures1 (also shown in Supplementary file 3). Our results showed that the T-Tex cluster was the most activated, followed by the two P-Tex clusters (Fig. 2b left). In addition, CD8 T cells in tumor tissues were more activated than those in adjacent normal tissues (Fig. 2b, right top). And no significant difference in T cell activation states was observed between HPV-positive and HPV-negative samples (Fig. 2b right bottom)."

2) A lot of discussion around "activation" is presented, but there is no evidence to support which genes or gene programs are associated with "activation".

Thanks for the comments. The activation states of CD8 T cell subpopulations were quantitatively assessed based on the average expression of previously described activation-related gene signatures1 (also shown in Supplementary file 3). More specifically, activation-related gene signatures are as follows: "CD69, CCR7, CD27, BTLA, CD40LG, IL2RA, CD3E, CD47, EOMES, GNLY, GZMA, GZMB, PRF1, IFNG, CD8A, CD8B, CD95L, LAMP1, LAG3, CTLA4, HLA-DRA, TNFRSF4, ICOS, TNFRSF9, TNFRSF18".

3) Line 249: It is unclear why the authors are indicating that TCRseq was used in pseudotime analysis. This type of analysis does not take TCRs into account but rather looks at the proportion of spliced mRNA of individual genes from the DGE data.

Thanks for the comments and we apologize for the usage of this misleading description. As acknowledged by the reviewer, pseudotime analysis has nothing to do with TCRseq data. Actually in this part, we separately performed clonality analysis of CD8 T cells based on TCRseq data and pseudotime analysis based on RNAseq data. Shared TCRs were identified among certain cell subclusters, which could partially validate the potential lineage relationships simulated by pseudotime analysis. Therefore, we have corrected the texts as follows to avoid the misunderstanding that TCRseq was used in pseudotime analysis: "Given the clonal accumulation of CD8 T cells was a result of local T cell proliferation and activation in the tumor environment2, we further conducted clonality analysis of CD8 T cells based on TCRseq data. " (line 246-248) and "To further investigate their lineage relationships, we performed pseudotime analysis for CD3+ T cells on the basis of transcriptional similarities (Fig. 3j-l, Figure 3-figure supplementary 2d)." (line 277-279).

Author Response

Reviewer #1 (Public Review):

The authors develop and freely disseminate the THINGS-data collection, a large-scale dataset incorporating MRI, MEG, eye-tracking, and 4.7 million similarity ratings for 1,854 object concepts. Demonstrating the reliability of their data, the authors replicate nearly a dozen previous neuroimaging papers. This "big data" approach significantly advances our ability to link behavioral measures with neuroimaging at scale, with the potential to spark future insights into how the mind represents objects.

I thought that the article was well-written, with a sound methodological approach, high-quality results, and well-supported conclusions. I am overall enthusiastic about this work, and I think THINGS will provide an important benchmark for future big data approaches in cognitive and computational neuroscience.

However, I thought it was also important to articulate more directly the potential insights this dataset can offer to the field. Although the authors mentioned that they "provided five examples for potential research directions", it was not clear to me what these new research directions were, given that the authors entirely describe replications in the results.

We thank Reviewer 1 for their positive evaluation and the enthusiasm for our work! We have revised the manuscript to articulate more clearly and directly some potential research directions for the dataset. There are two aspects to consider: What sets these datasets apart from traditional small-scale research? And what sets them apart from other large-scale research? We elaborate on these two aspects in response to specific comments below.

Reviewer #2 (Public Review):

Hebart et al., present a large-scale multi-model dataset consisting of fMRI, EEG, and behavioral similarity measures towards the study of object representation in the mind and brain. The effort is immense, the methods are rigorous, and the data are of reasonable quality, the demonstrative analyses are extensive and provocative. (One small note regarding one leg of this multi-modal dataset is that the fMRI design consisted of a single image presentation for 0.5s without repetitions for most of the images; this design choice has particular analysis implications, e.g. the dataset will have more power when leveraging a priori grouping of images. However, unlike other datasets of this kind, here the number of images and how they were selected does support this analysis mode, e.g. multiple exemplars per object concept, and rich accompanying meta-data and behavioral data.)

The manuscript is well-written, and the THINGs website that lets you explore the datasets is easy to navigate, delivering on the promise of making this an integrated, expanding worldwide initiative. Further, the datasets have clear complementary strengths to recent other large-scale datasets, in terms of the ways that the images were sampled (not to mention being multi-modal)-thus I suspect that the THINGs dataset will be heavily used by the cognitive/computational/neuroscience research community going forward.

We would like to thank the reviewer for their positive evaluation of our work! We agree that the dataset has more power when leveraging a priori grouping of images, which is specifically the design choice we made here. We also agree that we can better highlight the strength of our dataset with respect to existing datasets regarding multiple exemplars per object concept and the semantic breadth of the included object categories.

Reviewer #3 (Public Review):

This manuscript presents a highly valuable dataset with multimodal functional human brain imaging data (fMRI and MEG) as well as behavioural annotations of the stimuli used (thousands of images from the THINGS collection, systematically covering multiple types of concrete nameable objects).

The manuscript presents details about the dataset, quality control measures, and a careful description of preprocessing choices. The tools and approaches that were used follow the state of the art of the field in human functional brain imaging and I praise the authors for being transparent in their methodological approaches by also sharing their code along with the data. The manuscript also presents a few analyses with the data: 1) multi-dimensional embedding of perceived similarity judgments 2) decoding of neural representations of objects both with fMRI and MEG 3) A replication of findings related to visual size and animacy of objects 4) representation similarity analysis between functional brain data and behavioural ratings 5) MEG-fMRI fusion.

We thank the reviewer for their overall positive assessment of our work!

Author Response

Reviewer #2 (Public Review):

In this manuscript, Polyák et al. report detailed and systematic functional, electrocardiographic, electrophysiologic (both in vivo and in vitro experiments) and histological analysis in a large animal (canine) model of exercise to assess risk of ventricular arrhythmia susceptibility. They find that exercise-trained dogs have a slower heart rate (not accounted by heightened vagal tone alone and consistent with recent work from Denmark), an increased ventricular mass and fibrosis, APD lengthening due to repolarisation abnormality, enhanced HCN4 expression and decreased outward potassium channel density together with increased ventricular ectopic beats and ventricular fibrillation susceptibility (open-chest burst pacing). The authors suggest these changes as underlying the risk of VA in athletes, and appropriately caution against consigning the beneficial effects of exercise. In general, this study is well done, reasonably well-written, with reasonable conclusions, supported by the data presented and is much needed. There are some methodological, however, given the paucity of experimental data in this area, I think it would still be additive to the literature.

Strengths:

1. This is an area with very limited experimental data- this is an area of need.

2. The study, in general seems to be well-conducted with two clear groups

3. The use of a large animal model is appropriate

4. The study findings, in general, support the authors conclusions

5. The authors have shown some restraint in their conclusions and the limitations section is detailed and well written.

Weaknesses:

1. There are some methodological issues:

a. Authors should explain what the conditioning protocol was and why it was necessary.

In order to cause as little discomfort as possible to the animals, we selected animals that were naturally cooperative with the researchers and not afraid of the noise of the treadmill. This selection period lasted about three weeks, during which the animals were not exercised in a formal setting, but familiarized with the experimental setting and walked on the treadmills for a few minutes. During the conditioning period, both control and trained animals were equally handled.

Following your remarks the corresponding part of the text was extended properly explaining the training protocol in more detail.  

b. The rationale for the exercise parameters chosen needs to be presented.

Experimental data on large animal models are very limited. Sled dogs are considered the highest elite of dog exercise. The distances they run are taken as a reference, although this protocol is not exactly the same due to the conditions of training, sledding, and weather. The most widely known races are the Norwegian Finnmarksløp and the Alaskan Iditarod, take place on snow and cover distances ranging from 500–1569 km in a continuous competition lasting for up to 14 days to be completed. (Calogiuri & Weydahl, 2017)

Based on these data, preliminary experiments were conducted to determine the maximum running time and intensity that dogs can sustain without distress, injuries, or severe fatigue. We increased the intensity of exercise in line with the animals' performance. The detailed training protocol and the daily running distances applied are presented in Table 1. Now, a new figure, Figure 1, and a new table, Table 1, illustrate a detailed experimental timeline in the revised manuscript.

Reference:

Calogiuri, G., & Weydahl, A. (2017). Health challenges in long-distance dog sled racing: A systematic review of literature. Int J Circumpolar Health, 76(1), 1396147. https://doi.org/10.1080/22423982.2017.1396147

c. Open chest VF induction was a limitation, and it was unnecessary.

d. A more refined VT/VF induction protocol was required. This is a major limitation to this work.

C, D: Thank you for the reviewer’s comment. For a detailed explanation of the VF induction procedures, please see our responses to question 11 of Reviewer #2.

e. The concept of RV dysfunction has not been considered in the study and its analysis.

Thank you for the suggestion. The complexity of our study and the capacity of our laboratory limited the work that could be carried out, but we are planning to perform additional studies involving the RV.

f. The lack of a quantitative measure for fibrosis is a limitation.

At the Department of Pathology, there was no opportunity to analyze myocardial fibrosis quantitatively. As described by Mustroph et al., quantitative analysis of fibrosis can be based on appropriate software measuring the amount of fibrotic area per total area on digitized slides. Such software was not available during the evaluation. This is a limitation of the study; however, the semi-quantitative assessment in histology reports is widely accepted in human pathology (Mustroph et al., 2021).

Reference:

Mustroph, J., Hupf, J., Baier, M. J., Evert, K., Brochhausen, C., Broeker, K., Meindl, C., Seither, B., Jungbauer, C., Evert, M., Maier, L. S., & Wagner, S. (2021). Cardiac Fibrosis Is a Risk Factor for Severe COVID-19. Front Immunol, 12, 740260. https://doi.org/10.3389/fimmu.2021.740260

1. Statistical analysis requires further detail (checking of normality of the data/appropriate statistical test).

Thank you for this comment. This question has been answered in response to question 12 of Reviewer #2 and the statistical part of the methodology in the manuscript has been updated.

1. The use of Volders et al. study as a corollary in the discussion does not seem justified given that this study used AV block induced changes as an acquired TdP model.

We agree with the reviewer that the two models involve completely different mechanisms. Therefore, in order to avoid misunderstandings, we have deleted the part of the discussion that made the comparison with the study by Volders et al.(Volders et al., 1998; Volders et al., 1999) Nevertheless, the exercise-induced compensatory adaptive mechanisms of the athlete's heart have been considered as a phenomenon completely distinct from pathological conditions, yet the electrical remodeling observed in our model indicates important similarities with the experimental model of long-term complete AV block. For example, both resulted in profound bradycardia, compensated cardiac hypertrophy, prolonged QTc interval, APD prolongation, and increased spatial and temporal dispersion of repolarization. These changes were attributed to the downregulation of potassium currents and were associated with increased ventricular arrhythmia susceptibility. Therefore, we hypothesized that the mechanisms of increased propensity for ventricular fibrillation in this model may have a similar electrophysiological background to the compensated hypertrophy studies of Volders et al. However, the autonomic changes, the potential impairment of the conduction system of the athlete’s heart, and the electrophysiological background require further, more detailed investigations.

References:

Volders, P. G., Sipido, K. R., Vos, M. A., Kulcsar, A., Verduyn, S. C., & Wellens, H. J. (1998). Cellular basis of biventricular hypertrophy and arrhythmogenesis in dogs with chronic complete atrioventricular block and acquired torsade de pointes. Circulation, 98(11), 1136-1147. https://doi.org/10.1161/01.cir.98.11.1136

Volders, P. G., Sipido, K. R., Vos, M. A., Spatjens, R. L., Leunissen, J. D., Carmeliet, E., & Wellens, H. J. (1999). Downregulation of delayed rectifier K(+) currents in dogs with chronic complete atrioventricular block and acquired torsades de pointes. Circulation, 100(24), 2455-2461. https://doi.org/10.1161/01.cir.100.24.2455

Author Response

Reviewer #1 (Public Review):

This article is aimed at constructing a recurrent network model of the population dynamics observed in the monkey primary motor cortex before and during reaching. The authors approach the problem from a representational viewpoint, by (i) focusing on a simple center-out reaching task where each reach is predominantly characterised by its direction, and (ii) using the machinery of continuous attractor models to construct network dynamics capable of holding stable representations of that angle. Importantly, M1 activity in this task exhibits a number of peculiarities that have pushed the authors to develop important methodological innovations which, to me, give the paper most of its appeal. In particular, M1 neurons have dramatically different tuning to reach direction in the movement preparation and execution epochs, and that fact motivated the introduction of a continuous attractor model incorporating (i) two distinct maps of direction selectivity and (ii) distinct degrees of participation of each neuron in each map. I anticipate that such models will become highly relevant as neuroscientists increasingly appreciate the highly heterogeneous, and stable-yet-non-stationary nature of neural representations in the sensory and cognitive domains.

As far as modelling M1 is concerned, however, the paper could be considerably strengthened by a more thorough comparison between the proposed attractor model and the (few) other existing models of M1 (even if these comparisons are not favourable they will be informative nonetheless). For example, the model of Kao et al (2021) seems to capture all that the present model captures (orthogonality between preparatory and movement-related subspaces, rotational dynamics, tuned thalamic inputs mostly during preparation) but also does well at matching the temporal structure of single-neuron and population responses (shown e.g. through canonical correlation analysis). In particular, it is not clear to me how the symmetric structure of connectivity within each map would enable the production of temporally rich responses as observed in M1. If it doesn't, the model remains interesting, as feedforward connectivity between more than two maps (reflecting the encoding of many more kinematic variables) or other mechanisms (such as proprioceptive feedback) could well explain away the observed temporal complexity of neural responses. Investigating such alternative explanations would of course be beyond the scope of this paper, but it is arguably important for the readers to know where the model stands in the current literature.

Below is a summary of my view on the main strengths and weaknesses of the paper:

1) From a theoretical perspective, this is a great paper that makes an interesting use of the multi-map attractor model of Romani & Tsodyks (2010), motivated by the change in angular tuning configuration from the preparatory epoch to the movement execution epoch. Continuous attractor models of angular tuning are often criticised for being implausibly homogeneous/symmetrical; here, the authors address this limitation by incorporating an extra dimension to each map, namely the degree of participation of each neuron (the distribution of which is directly extracted from data). This extension of the classical ring model seems long overdue! Another nice thing is the direct use of data for constraining the model's coupling parameters; specifically, the authors adjust the model's parameters in such a way as to match the temporal evolution of a number of "order parameters" that are explicitly manifested (i.e. observable) in the population recordings.

I believe the main weakness of this continuous attractor approach is that it - perhaps unduly binarises the configuration of angular tuning. Specifically, it assumes that while angular tuning switches at movement onset, it is otherwise constant within each epoch (preparation and execution). I commend the authors for carefully motivating this in Figure 2 (2e in particular), by showing that the circular variance of the distribution of preferred directions is higher across prep & move than within either prep or move. While this justifies a binary "two-map model" to first order, the analysis nevertheless shows that preferred directions do change, especially within the preparatory epoch. Perhaps the authors could do some bootstrapping to assess whether the observed dispersion of PDs within sub-periods of the delay epoch is within the noise floor imposed by the finite number of trials used to estimate tuning curves. If it is, then this considerably strengthens the model; otherwise, the authors should say that the binarisation reflects an approximation made for analytical tractability, and discuss any important implications.

We thank the reviewer for the suggested analysis. We have included this new analysis in Fig. S1.

First of all, in Fig 2e of the previous version of the manuscript, we were considering three time windows during preparation and two time windows during movement execution. We are now using a shorter time window of 160ms, so that we can fit three time windows within either epoch. The results do not change qualitatively, and the results of the bootstrap analysis below do not change based on the definition of this time window.

The bootstrap analysis is described in detail in the second paragraph of the Methods sections (“Preparatory and movement-related epochs of motion”). The bootstrap distribution is generated by resampling trials with repetitions (and keeping the number of trials per condition the same as in the data), while shuffling the temporal windows in time, within epochs. For example: for condition 1, we have 43 trials in the data. In one trial of the bootstrap distribution for condition 1, each one of the 3 time windows of the delay period is chosen at random (with repetitions) between the possible 43*3 windows from the data. The analysis shows that the median variance of preferred directions from the data is significantly larger than the one from the bootstrap samples.

This suggests that neurons do change their preferred direction within epochs, but these changes are smaller in magnitude than changes that occur between the epochs. We explicitly comment on this in the methods, and in the main text we point out that considering only two epochs is a simplifying assumption, and as such it can be thought as a first step towards building a more complete model that shows dynamics of tuning within both preparatory and execution epochs. Note, however, that this simple framework is enough for the model to recapitulate to a large extent neuronal activity, both at the level of single-units and at the population level.

2) While it is great to constrain the model parameters using the data, there is a glaring "issue" here which I believe is both a weakness and a strength of the approach. The model has a lot of freedom in the external inputs, which leads to relatively severe parameter degeneracies. The authors are entirely forthright about this: they even dedicate a whole section to explaining that depending on the way the cost function is set up, the fit can land the model in very different regimes, yielding very different conclusions. The problem is that I eventually could not decide what to make of the paper's main results about the inferred external inputs, and indeed what to make of the main claim of the abstract. It would be great if the authors could discuss these issues more thoroughly than they currently do, and in particular, argue more strongly about the reasons that might lead one to favour the solutions of Fig 6d/g over that of Fig 6a. On the other hand, I see the proposed model as an interesting playground that will probably enable a more thorough investigation of input degeneracies in RNN models. Several research groups are currently grappling with this; in particular, the authors of LFADS (Pandarinath et al, 2018) and other follow-up approaches (e.g. Schimel et al, 2022) make a big deal of being able to use data to simultaneously learn the dynamics of a neural circuit and infer any external inputs that drive those dynamics, but everyone knows that this is a generally ill-posed problem (see also discussion in Malonis et al 2021, which the authors cite). As far as I know, it is not yet clear what form of regularisation/prior might best improve identifiability. While Bachschmid-Romano et al. do not go very far in dissecting this problem, the model they propose is low-dimensional and more amenable to analytical calculations, such that it provided a valuable playground for future work on this topic.

We agree with the reviewer that the problem of disambiguating between feedforward and recurrent connections from observation of the state of the recurrent units alone is a degenerate problem in general.

By explicitly looking for solutions that minimize the role of external inputs in driving the dynamics, we argued that the solutions of Fig 4d/g are favorable over the one of Fig 4a because they are based on local computations implemented through shorter range connections compared to incoming connections from upstream areas; as such, they likely require less metabolic energy.

In the new version of the paper, we discuss this issue more explicitly:

Degeneracy of solutions. We considered the case where parameters are inferred by minimizing a cost function that equals the reconstruction error only (this corresponds to the case of very large values of the parameter α in the cost function). Figure 4—figure supplement 2 shows that after minimizing the reconstruction error, the cost function is flat in a large region of the order parameters. We also added Figure 5—figure supplement 5, to show that the dynamics of the feedforward network looks almost indistinguishable from the one of the recurrent network (Fig.5) - although the average canonical correlation coefficient is a bit lower for the purely feedforward case.

Breaking the degeneracy of solutions. We added Figure 4—figure supplement 1 to show that for a wide range of the parameter α, all solutions cluster in a small region of parameter space. Solutions are found both above and below the bifurcation line. Note that all solutions are such that parameters jA and jB are close to the bifurcation line that separate the region where tuned network activity requires tuned external input, and the region where tuned network activity can be sustained autonomously. Furthermore, the weight of recurrent-connections within map B (j_B) is much stronger than the corresponding weight for map A (j_A). Hence, we observe that external inputs play a stronger role in shaping the dynamics during motor preparation than during execution, while recurrent inputs dominate the total inputs during movement execution, for a broad range of values of alpha. This prediction needs to be tested experimentally, although it is in line with the results of ref. 39, as we explain in the Discussion, section “Interplay between external and recurrent currents”, last paragraph.

3) As an addition to the motor control literature, this paper's main strengths lie in the modelcapturing orthogonality between preparatory and movement-related activity subspaces (Elsayed et al 2016), which few models do. However, one might argue that the model is in fact half hand-crafted for this purpose, and half-tuned to neural data, in such a way that it is almost bound to exhibit the phenomenon. Thus, some form of broader model cross-validation would be nice: what else does the model capture about the data that did not explicitly inspire/determine its construction? As a starting point, I would suggest that the authors apply the type of CCA-based analysis originally performed by Sussillo et al (2015), and compare qualitatively to both Sussillo et al. (2015) and Kao et al (2021). Also, as every recorded monkey M1 neuron can be characterized by its coordinates in the 4-dimensional space of angular tuning, it should be straightforward to identify the closest model neuron; it would be very compelling to show side-by-side comparisons of single-neuron response timecourses in model and monkey (i.e., extend the comparison of Fig S6 to the temporal domain).

We thank the reviewer for these suggestions. We have added the following comparisons:

● A CCA-based analysis (Fig 5.a) shows that the performance of our model is qualitatively comparable to the Sussillo et al. (2015) and Kao et al (2021) at generating realistic motor cortical activity (average canonical correlation ρ = 0.77 during movement preparation and 0.82 during movement execution).

● For each of the 141 neurons in the data, we selected the corresponding one in the model that is closest in the eta- and theta- parameters space:

a) A side-by-side comparison of the time course of responses shows a good qualitative agreement (Fig 5.c).

b) We successfully trained a linear decoder to read the responses of these 141 neurons from simulations and output trial-averaged EMG activity recorded from a monkey performing the same task Fig 5.b.

c) Figure 5—figure supplement 4 shows that simulated data presents sequential activity, as does the recorded data.

In our simulations, the temporal variability in single-neuron responses is due to the temporal evolution of the inferred external inputs, and to noise, implemented by an Ornstein-Uhlenbeck (OU) process that is added to the total inputs. Another source of variability could be introduced in the synaptic connectivity: one could add a gaussian random variable to each synaptic efficacy, for example. We checked that this simple extension of our model is able to reproduce the dynamics of the order parameters seen in the data. A full characterization of this extended model is beyond the scope of our paper.

4) The paper's clarity could be improved.

We thank the reviewer for his feedback. We have significantly rewritten most sections of the paper to improve clarity.

Reviewer #2 (Public Review):

The authors study M1 cortical recordings in two non-human primates performing straight delayed center-out reaches to one of 8 peripheral targets. They build a model for the data with the goal of investigating the interplay of inferred external inputs and recurrent synaptic connectivity and their contributions to the encoding of preferred movement direction during movement preparation and execution epochs. The model assumes neurons encode movement direction via a cosine tuning that can be different during preparation and execution epochs. As a result, each type of neuron in the model is described with four main properties: their preferred direction in the cosine tuning during preparation (denoted by θ_A) and execution (denoted by θ_B) epochs, and the strength of their encoding of the movement direction during the preparation (denoted by η_A) and execution (denoted by η_B) epochs. The authors assume that a recurrent network that can have different inputs during the preparation and execution epochs has generated the activity in the neurons. In the model, these inputs can both be internal to the network or external. The authors fit the model to real data by optimizing a loss that combines, via a hyperparameter α, the reconstruction of the cosine tunings with a cost to discourage/encourage the use of external inputs to explain the data. They study the solutions that would be obtained for various values of α. The authors conclude that during the preparatory epoch, external inputs seem to be more important for reproducing the neuron's cosine tunings to movement directions, whereas during movement execution external inputs seem to be untuned to movement direction, with the movement direction rather being encoded in the direction-specific recurrent connections in the network.

Major:

1) Fundamentally, without actually simultaneously recording the activity of upstream regions, it should not be possible to rule out that the seemingly recurrent connections in the M1 activity are actually due to external inputs to M1. I think it should be acknowledged in the discussion that inferred external inputs here are dependent on assumptions of the model and provide hypotheses to be validated in future experiments that actually record from upstream regions. To convey with an example why I think it is critical to simultaneously record from upstream regions to confirm these conclusions, consider two alternative scenarios: I) The recorded neurons in M1 have some recurrent connections that generate a pattern of activity that is based on the modeling seems to be recurrent. II) The exact same activity has been recorded from the same M1 neurons, but these neurons have absolutely no recurrent connections themselves, and are rather activated via purely feed-forward connections from some upstream region; that upstream region has recurrent connections and is generating the recurrent-like activity that is later echoed in M1. These two scenarios can produce the exact same M1 data, so they should not be distinguishable purely based on the M1 data. To distinguish them, one would need to simultaneously record from upstream regions to see if the same recurrent-like patterns that are seen in M1 were already generated in an upstream region or not. I think acknowledging this major limitation and discussing the need to eventually confirm the conclusions of this modeling study with actual simultaneous recordings from upstream regions is critical.

We agree with the reviewer that it is not possible to rule out the hypothesis that motor cortical activity is purely generated by feedforward connectivity.

In the new version of the paper, we discuss more explicitly the fact that neural activity can be fully explained by feedforward inputs, and we added Figure 5—figure supplement 5 to show that the dynamics of the feedforward network looks almost indistinguishable from the one of the recurrent network (Fig.5), provided their parameters are appropriately tuned. Notice, however, that a canonical correlation analysis comparing the activity from recording with the one from simulations shows that the average canonical correlation coefficient is slightly lower for the case of a purely feedforward network (Fig.5.a vs Fig.S12.a).

A summary of our approach is:

• We observe that both a purely feedforward and a recurrent network can reproduce the temporal course of the recordings equally well (see also our answer to question 5 below);

• We point out that a solution that would save metabolic energy consumption is one where the activity is generated by recurrent currents (with shorter range local connections) rather than by feedforward inputs from upstream regions (long-range connections).

• We study the solution that best reproduces the recorded activity and minimizes inputs from upstream regions.

In the Discussion, we included the Reviewer’s observation that our hypothesis needs to be tested by simultaneous recordings of M1 and upstream regions, as well as measures of synaptic strength between motor cortical neurons. See the second paragraph of page 14: “ Our prediction (…) will be necessary to rule out alternative explanations”. Yet, we think that the results of reference [51] are consistent with our results.

One last point we would like to stress is that external inputs drive the network's dynamics at all times, even in the solution that we argue would save metabolic energy consumption: untuned inputs are present throughout the whole course of the motor action, also during movement execution, and they determine the precise temporal pattern of neurons firing rates.

2) The ring network model used in this work implicitly relies on the assumption that cosinetuning models are good representations of the recorded M1 neuronal activity. However, this assumption is not quantitatively validated in the data. Given that all conclusions depend on this, it would be important to provide some goodness of fit measure for the cosine tuning models to quantify how well the neurons' directional preferences are explained by cosine tunings. For example, reporting a histogram of the cosine tuning fit error over all neurons in Fig 2 would be helpful (currently example fits are shown only for a few neurons in Fig. 2 (a), (b), and Figure S6(b)). This would help quantitatively justify the modeling choice.

We thank the reviewer for this observation. Fig.S2.e-f shows the R^2 coefficient of the cosine fit; in particular, we show that the R^2 of the cosine fit strongly correlates with the variables \eta, which represent the degree of participation of single units to the recurrent currents. Units with higher \eta (the ones that contribute more to the recurrent currents) are the ones whose tuning curves better resemble a cosine. However, the plot also shows that the R^2 coefficient of the cosine fit is pretty low for many cells. To show that a model with cosine tuning can yield this result, we repeated the same analysis on the units in our simulated network. In our simulations, all neurons receive a stochastic input mimicking large fluctuations around mean inputs that are expected to occur in vivo. We selected the 141 units whose activity more strongly resembled the activity of the 141 recorded neurons (see figure caption for details). We then looked at the tuning curves of these 141 units from simulations, and calculated the R^2 coefficient of the cosine fit. Figure 5—figure supplement 2.c shows that the result agrees well with the data: the R^2 coefficient is pretty low for many neurons, and correlates with the variable \eta. To summarize, a model that assumes cosine tuning, but also incorporates noise in the dynamics, reproduces well the R^2 coefficient of the cosine fit of tuning curves from data. We added the paragraph “Cosine tuning “ in the Discussion to comment on this point.

3) The authors explain that the two-cylinder model that they use has "distinct but correlated"maps A and B during the preparation and movement. This is hard to see in the formulation. It would be helpful if the authors could expand in the Results on what they mean by "correlation" between the maps and which part of the model enforces the correlation.

We thank the reviewer for this comment. By correlation, we meant the correlation between neural activity during the preparatory and movement-related temporal intervals. In the model, the correlation between the vectors θA and θB induces correlation in the preparatory and movement-related activity patterns. To make the paper easier to read, we are not mentioning this concept in the Results; in the Discussion, we explicitly refer to it in the following two paragraphs:

“A strong correlation between the selectivity properties of the preparatory and movement-related epochs will produce strongly correlated patterns of activity in these two intervals and a strong overlap between the respective PCA subspaces.” (Discussion, section Orthogonal spaces dedicated to movement preparation and execution)

“The correlation between the vectors θAand θB (Discussion, section Interplay between external and recurrent currents)”

4) The authors note that a key innovation in the model formulation here is the addition ofparticipation strengths parameters (η_A, η_B) to prior two-cylinder models to represent the degree of neuron's participation in the encoding of the circular variable in either map. The authors state that this is critical for explaining the cosine tunings well: "We have discussed how the presence of this dimension is key to having tuning curves whose shape resembles the one computed from data, and decreases the level of orthogonality between the subspaces dedicated to the preparatory and movement-related activity". However, I am not sure where this is discussed. To me, it seems like to show that an additional parameter is necessary to explain the data well, one would need to compare fit to data between the model with that parameter and a model without that parameter. I don't think such a comparison was provided in the paper. It is important to show such a comparison to quantitatively show the benefit of the novel element of the model.

We thank the reviewer for this comment.

● The key observation is that without the parameters eta_A, eta_B, the temporal evolution of all neurons in the network is the same (only the noise term added to the dynamics is different). To show this, we have performed a comparison of the temporal evolution of the firing rates of single neurons of the model with data. Fig 5.c shows a comparison between the time-course of single neurons firing rates from data and simulations (good agreement), while Figure 6—figure supplement 2.a shows the same comparison for a model in which all neurons have the same value of the eta_A, eta_B parameters (worse agreement: the range of firing rates is the same for all neurons). In summary, the parameters eta_A, eta_B introduce the variability in the coupling strengths that is necessary to generate heterogeneity in neuronal responses.

● At the end of section “PCA subspaces dedicated to movement preparation and execution”, we refer to (Figure 6—figure supplement 2).c, showing that a model with eta_A=1=eta_B for all neurons yields less orthogonal subspaces.

5) The model parameters are fitted by minimizing a total cost that is a weighted average of twocosts as E_tot = α E_rec + E_ext, with the hyperparameter α determining how the two costs are combined. The selection of α is key in determining how much the model relies on external inputs to explain the cosine tunings in the data. As such, the conclusions of the paper rely on a clear justification of the selection of α and a clear discussion of its effect. Otherwise, all conclusions can be arbitrary confounds of this selection and thus unreliable. Most importantly, I think there should be a quantitative fit to data measure that is reported for different scenarios to allow comparison between them (also see comment 2). For example, when arguing that α should be "chosen so that the two terms have equal magnitude after minimization", this would be convincing if somehow that selection results in a better fit to the neural data compared with other values of α. If all such selections of α have a similar fit to neural data, then how can the authors argue that some are more appropriate than others? This is critical since small changes in alpha can lead to completely different conclusions (Fig. 6, see my next two comments).

All the points raised in questions 5 to 8 are interrelated, and we address them below, after Major issue 8.

6) The authors seem to select alpha based on the following: "The hyperparameter α was chosen so that the two terms have equal magnitude after minimization (see Fig. S4 for details)". Why is this the appropriate choice? The authors explain that this will lead to the behavior of the model being close to the "bifurcation surface". But why is that the appropriate choice? Does it result in a better fit to neural data compared with other choices of α? It is critical to clarify and justify as again all conclusions hinge on this choice.

7) Fig 6 shows example solutions for 2 close values of α, and how even slight changes in the selection of α can change the conclusions. In Fig. 6 (d-e-f), α is chosen as the default approach such that the two terms E_rec and E_ext have equal magnitude. Here, as the authors note, during movement execution tuned external inputs are zero. In contrast, in Fig. 6 (g-h-i), α is chosen so that the E_rec term has a "slightly larger weight" than the E_ext term so that there is less penalty for using large external inputs. This leads to a different conclusion whereby "a small input tuned to θ_B is present during movement execution". Is one value of α a better fit to neural data? Otherwise, how do the authors justify key conclusions such as the following, which seems to be based on the first choice of α shown in Fig. 6 (d-e-f): "...observed patterns of covariance are shaped by external inputs that are tuned to neurons' preferred directions during movement preparation, and they are dominated by strong direction-specific recurrent connectivity during movement execution".

8) It would be informative to see the extreme case of very large and very small α. For example, if α is very large such that external inputs are practically not penalized, would the model rely purely on external inputs (rather than recurrent inputs) to explain the tuning curves? This would be an example of the hypothetical scenario mentioned in my first comment. Would this result in a worse fit to neural data?

We agree with the reviewer that it is crucial to discuss how the choice of the parameter alpha affects the results, and we have strived to improve this discussion in the revised manuscript.

I. When we looked for the coupling parameters that best explain the data, without introducing a metabolic cost, we found multiple solutions that were equally good (see Figure 4—figure supplement 2 and our answer to question (1) above). These included the solution with all couplings set to zero ( j_s^B = j_s^A = j_a = 0), as well as many solutions with different values of synaptic couplings parameters. The solution with the strongest couplings is close to the bifurcation line, in the area where j_s^B > j_s^A.

II. We then introduced a metabolic cost to break the degeneracy between these different solutions. The cost function we minimized contains two terms; their relative strength is modulated by alpha. The case of very small alpha (i.e., only minimizing external input) yields a very poor reconstruction of neural dynamics and is not interesting. The case of very large alpha reduces to the case (I) above. We added Figure 4—figure supplement 1 to show the results for intermediate values of alpha - alpha is large enough to yield a good reconstruction of neural dynamics, yet small enough to ensure that we find a unique solution. For these intermediate values of alpha, the two terms of the cost function have comparable magnitudes. Although slight changes in the selection of alpha do change whether the solutions are above or below the bifurcation surface, Figure 4—figure supplement 1 shows that all solutions are close to the bifurcation surface. In particular, the value of j_s^B is close to its critical value, while we never find solutions where j_s^A is close to its critical value - we never find solutions in the lower-right region of the plot in Figure 4—figure supplement 1. The critical value for j_s^B is the one above which no tuned external inputs are necessary to sustain the observed activity during movement execution. For values of j_s^B close to the bifurcation line but below it (for example, Fig.4g) inferred tuned inputs are still much weaker than the untuned ones, during movement execution. Also, the inferred direction-specific couplings are strong and amplify the weak external inputs tuned to map B, therefore still playing a major role in shaping the observed dynamics during movement execution.

We have rewritten accordingly the abstract, introduction and conclusions of the paper. Instead of focusing on only one solution for a particular value of alpha, we now discuss all solutions and their implications.

9) The authors argue in the discussion that "the addition of an external input strengthminimization constraint breaks the degeneracy of the space of solutions, leading to a solution where synaptic couplings depend on the tuning properties of the pre- and post-synaptic neurons, in such a way that in the absence of a tuned input, neural activity is localized in map B". In other words, the use of the E_ext term, apparently reduces "degeneracy" of the solution. This was not clear to me and I'm not sure where it is explained. This is also related to α because if alpha goes toward very large values, it would be like the E_ext term is removed, so it seems like the authors are saying that the solution becomes degenerate if alpha grows very large. This should be clarified.

We thank the reviewer for pointing this out. By degeneracy of solution, we mean that the model can explain the data equally well for different choices of the recurrent couplings parameters (j_s^A, j_s^B, j_a). In other words, if we look for the coupling parameters that best explain the data, there are many equivalent solutions. When we introduce the E_ext term in the cost function, we then find one unique solution for each choice of alpha. So by “breaking the degeneracy”, we mean going from a scenario where there are many solutions that are equally valid, to one single solution. We added this explanation in the paper, along with the explanation on how our conclusion depends on the ‘choice of alpha’.

10) How do the authors justify setting Φ_A = Φ_B in equation (5)? In other words, how is the last assumption in the following sentence justified: "To model the data, we assumed that the neurons are responding both to recurrent inputs and to fluctuating external inputs that can be either homogeneous or tuned to θ_A; θ_B, with a peak at constant location Φ_A = Φ_B ≡ Φ". Does this mean that the preferred direction for a given neuron is the same during preparation and movement epochs? If so, how is this consistent with the not-so-high correlation between the preferred directions of the two epochs shown in Fig. 2 c, which is reported to have a circular correlation coefficient of 0.4?

We would like to stress the important distinction between the parameters \theta and the parameters Φ. While the parameters \theta_A and \theta_B represent the preferred direction of single neurons during preparatory and execution epochs, respectively, the parameters Φ_A, Φ_B represent the direction of motion that is encoded at the population level during these two epochs. The mean-field analysis shows that Φ_A = Φ_B, even though single neurons change their preferred direction from one epoch to the next. We added a more extensive explanation of the order parameters in the Results section.

Reviewer #3 (Public Review):

In this work, Bachschmid-Romano et al. propose a novel model of the motor cortex, in which the evolution of neural activity throughout movement preparation and execution is determined by the kinematic tuning of individual neurons. Using analytic methods and numerical simulations, the authors find that their networks share some of the features found in empirical neural data (e.g., orthogonal preparatory and execution-related activity). While the possibility of a simple connectivity rule that explains large features of empirical data is intriguing and would be highly relevant to the motor control field, I found it difficult to assess this work because of the modeling choices made by the authors and how the results were presented in the context of prior studies.

Overall, it was not clear to me why Bachschmid-Romano et al. couched their models within a cosine-tuning framework and whether their results could apply more generally to more realistic models of the motor cortex. Under cosine-tuning models (or kinematic encoding models, more generally), the role of the motor cortex is to represent movement parameters so that they can presumably be read out by downstream structures. Within such a framework, the question of how the motor cortex maintains a stable representation of movement direction throughout movement preparation and execution when the tuning properties of individual neurons change dramatically between epochs is highly relevant. However, prior work has demonstrated that kinematic encoding models provide a poor fit for empirical data. Specifically, simple encoding models (and the more elaborate extensions [e.g., Inoue, et al., 2018]) cannot explain the complexity of single-neuron responses (Churchland and Shenoy, 2007), and do not readily produce the population-level signals observed in the motor cortex (Michaels, Dann, and Scherberger, 2016) and cannot be extended to more complex movements (Russo, et al., 2018).

In both the Introduction and Discussion, the authors heavily cite an alternative to kinematic encoding models, the dynamical systems framework. Here, the correlations between kinematics and neural activity in the motor cortex are largely epiphenomenal. The motor cortex does not 'represent' anything; its role is to generate patterns of muscle activity. While the authors explicitly acknowledge the shortcomings of encoding models ('Extension to modeling richer movements', Discussion) and claim that their proposed model can be extended to 'more realistic scenarios', they neither demonstrate that their models can produce patterns of muscle activity nor that their model generates realistic patterns of neural activity. The authors should either fully characterize the activity in their networks and make the argument that their models better provide a better fit to empirical data than alternative models or demonstrate that more realistic computations can be explained by the proposed framework.

Major Comments

1) In the present manuscript, it is unclear whether the authors are arguing that representing movement direction is a critical computation that the motor cortex performs, and the proposed models are accurate models of the motor cortex, or if directional coding is being used as a 'proof of concept' that demonstrates how specific, population-level computations can be explained by the tuning of individual neurons.

If the authors are arguing the former, then they need to demonstrate that their models generate activity similar to what is observed in the motor cortex (e.g., realistic PSTHs and population-level signals). Presently, the manuscript only shows tuning curves for six example neurons (Fig. S6) and a single jPC plane (Fig. S8). Regarding the latter, the authors should note that Michaels et al. (2016) demonstrated that representational models can produce rotations that are superficially similar to empirical data, yet are not dependent on maintaining an underlying condition structure (unlike the rotations observed in the motor cortex).

If the authors are arguing the latter - and they seem to be, based on the final section of the Discussion - then they need to demonstrate that their proposed framework can be extended to what they call 'more realistic scenarios'. For example, could this framework be extended to a network that produces patterns of muscle activity?

We thank the reviewer for raising these issues.

Is our model a kinematic encoding model or a dynamical system?

Our model is a dynamical system, as can be seen by inspecting equations (1,2). The main difference between our model and recently proposed dynamical system models of motor cortex is that the synaptic connectivity matrix in our model is built from the tuning properties of neurons, instead of being trained using supervised learning techniques (we come back to this important difference below). Since the network’s connectivity and external input depend on the neurons’ tuning to the direction of motion (eq 5-6), kinematic parameters emerge from the dynamic interaction between recurrent and feedforward currents, as specified by equations (1-6). Thus, kinematic parameters can be decoded from population activity.

While in kinematic encoding models neurons’ firing rates are a function of parameters of the movement, we constrained the parameters of our model by requiring the model to reproduce the dynamics of a few order parameters, which are low-dimensional measures of the activity of recorded neurons. Our model is fitted to neural data, not to the parameters of the movement.

Although we observed that a linear decoder of the network’s activity can reproduce patterns of muscle activity without decoding any kinematic parameter (see below), discussing whether tuning in M1 plays a computational role in controlling muscle activity is outside of the scope of our work. Rather, the scope of our paper is to discuss how a specific connectivity structure can generate the observed patterns of neural activity, and which connectivity structure requires minimum external inputs to sustain the dynamics. In our approach, the correlations between kinematics and neural activity in the motor cortex are not merely epiphenomenal, but emerge from a specific structure of the connectivity that has likely been shaped by hebbian-like learning mechanisms.

Can the model generate realistic PSTHs and patterns of muscle activity? Yes, it can. As suggested, we have added the following comparisons:

● A CCA-based analysis (Fig 5.a) shows that the performance of our model is qualitatively comparable to the Sussillo et al. (2015) and Kao et al (2021) at generating realistic motor cortical activity (average canonical correlation ρ = 0.77 for motor preparation, 0.82 for motor execution).

● For each of the 141 neurons in the data, we selected the corresponding most similar unit in the model (the closest neurons in the eta- and theta- parameters space, i.e. the one with smallest euclidean distance in the space defined by (\theta_A, \theta_B, \eta_A, \eta_B)). A side-by-side comparison of the time course of responses (Fig 5.c) shows a good qualitative agreement.

● We successfully trained a linear decoder to read the responses of these 141 units from simulations and output trial-averaged EMG activity recorded from a monkey performing the same task (Fig 5.b).

● The model displays sequential activity and rotational dynamics (Fig. S10) without the need to introduce neuron-specific latencies (Michaels, Dann, and Scherberger, 2016).

Can our model explain the complexity of single-neuron tuning?

We have shown that our model captures the heterogeneity of neural responses. Yet, it has been shown that neurons’ tuning properties depend on many features of movement. For example, the current version of the model does not describe the dependence of tuning on speed (Churchland and Shenoy, 2007). However, our model could be extended to incorporate it. Preliminary results suggest that in a network model in which neurons differ by the degree of symmetry of their synaptic connectivity the speed of neural trajectories can be modulated by external inputs targeting preferentially neurons that are asymmetrically connected. In our model, all connections are a sum of a symmetric and an asymmetric term. We could extend our model to incorporate variability in the degree of symmetry in the connections, and speculate that in such a model tuning would depend on the speed of movement, for appropriate forms of external inputs. We leave this study to future work.

Can our model explain neural activity underlying more complex trajectories? When limb trajectories are more complex than simple reaches (Russo, et al., 2018), a single neuron’s activity displays intricate response patterns. Our work could be extended to model more complex movement in several ways. A simplifying assumption we made is that the task can be clearly separated into a preparatory phase and one movement-related phase. A possible extension is one where the motor action is composed of a sequence of epochs, corresponding to a sequence of maps in our model. It will be interesting to study the role of asymmetric connections for storing a sequence of maps. Such a network model could be used to study the storing of motor motifs in the motor cortex (Logiaco et al, 2021); external inputs could then combine these building blocks to compose complex actions.

In summary, we proposed a simple model that can explain recordings during a straight-reaching task. It provides a scaffold upon which we can build more sophisticated models to explain the activity underlying more complex tasks. We point out that a similar limitation is present in modeling approaches where a network is trained to perform specific neural or muscle activity. The question of whether/how trained recurrent networks can generalize is not yet solved, although currently under investigation (e.g., Dubreuil et al 2022; Driscoll et al 2022).

What is the advantage of the present model, compared to an RNN trained to output specific neural/muscle activity?

Its simplicity. Our model is a low-rank recurrent neural network: the structure of the connectivity matrix is simple enough to allow for analytical tractability of the dynamics. The model can be used to test specific hypotheses on the relationship between network connectivity, external inputs and neural dynamics, and to test hypotheses on the learning mechanisms that may lead to the emergence of a given connectivity structure. The model is also helpful to illustrate the problem of degeneracy of network models. An interesting future direction would be to compare the connectivity matrices of trained RNNs and our model.

We addressed these points in the Discussion, in sections: “Representational vs dynamical system approaches” and “Extension to modeling activity underlying more complex tasks.”

2) Related to the above point, the authors claim in the Abstract that their models 'recapitulatethe temporal evolution of single-unit activity', yet the only evidence they present is the tuning curves of six example units. Similarly, the authors should more fully characterize the population-level signals in their networks. The inferred inputs (Fig. 6) indeed seem reasonable, yet I'm not sure how surprising this result is. Weren't the authors guaranteed to infer a large, condition-invariant input during movement and condition-specific input during preparation simply because of the shape of the order parameters estimated from the data (Fig. 6c, thin traces)?

We thank the reviewer for this comment. Regarding the first part of the question: we added new plots with more comparisons between the activity of our model and neural recordings (see the answer above referring to Fig 5).

Regarding the second part: It is true that the shape of the latent variables that we measure from data constrains the solution that we find. However, a “condition-invariant input during movement and condition-specific input during preparation” is not the only scenario compatible with the data. Let’s take a step back and focus on the parameters that we are inferring from data. We are inferring both the strength of external inputs and the couplings parameters. This is done in a two-step inference procedure: we start from a random guess of the couplings parameters, then we infer the strength of the external inputs, and finally we compute the cost function, which depends on all parameters. This is done iteratively, by moving in the space of the coupling parameters; for each point in the space of the coupling parameters, there is one possible configuration of external inputs. The space of the coupling parameters is shown in Fig 4.a, for example (see also Fig. S4). The solutions that we find do not trivially follow from the shape of the latent variables. For example, one possible solution could be: large parameter j_s^A, small parameter j_s^B, which correspond to a point in the lower-right region of the parameter space in Fig 4.a (Fig. S4). The resulting external input would be a strong condition-specific external input during movement execution, but a condition-invariant input during movement preparation: the model is such that, for example, exciting for a short time-interval a few neurons whose preferred direction corresponds to the direction of motion would be enough to “set the direction of motion” for the network; the pattern of tuned activity could be sustained during the whole delay period thanks to the strong recurrent connections j_s^A. We could not rule out this solution by simply looking at the shape of the latent variables. However, it is a solution we have never observed. We only found solutions in the region where j_s^B is large and close to its critical value. This implies the presence of condition-specific inputs during the whole delay period, and condition-invariant external inputs that dominate over condition-specific ones during movement execution.

3) In the Abstract and Discussion (first paragraph), the authors highlight that the preparatory andexecution-related spaces in the empirical data and their models are not completely orthogonal, suggesting that this near-orthogonality serves an important mechanistic purpose. However, networks have no problem transferring activity between completely orthogonal subspaces. For example, the generator model in Fig. 8 of Elsayed, et al. (2016) is constrained to use completely orthogonal preparatory and execution-related subspaces. As the authors point out in the Discussion, such a strategy only works because the motor cortex received a large input just before movement (Kaufman et al., 2016).

We thank the reviewer for this observation. We would like to stress the fact that we are not claiming that having an overlap between subspaces is necessary to transfer activity. Instead, our model shows that a small overlap between the maps can be exploited by the network to transfer activity between subspaces without requiring direction-specific external inputs right before movement execution. A solution where activity is transferred through feedforward inputs is also possible. Indeed, one of the observations of our work (which we highlight more in the new version of the paper) is that by looking at motor cortical activity only, we are not able to distinguish between the activity generated by a feedforward network, and one generated by a recurrent one. However, we argue that a solution where external inputs are minimized can be favorable from a metabolic point of view, as it requires fewer signals to be transmitted through long-range connections. This informs our cost function, and yields a solution where activity is transferred through recurrent connections, by exploiting the small correlation between subspaces.

Author Response

Reviewer #1 (Public Review):

DeRisi and colleagues used a new phage-display peptide platform, with 238,068 tiled 62-amino acid peptides covering all known P falciparum coding regions (and numerous other entities), to survey seroreactivity in 198 Ugandan children and adults from two cohorts. They find that the breadth of responses to repeat-containing peptides was twofold higher in children living in the high versus moderate exposure setting, while no such differences were observed for peptides without repeats. Additionally, short motifs associated with seroreactivity were extensively shared among hundreds of antigens, with much of this driven by motifs shared with PfEMP1 antigens.

Malaria immunity is complex, and this new platform is a potentially valuable addition to the toolkit for understanding humoral responses. The two cohorts differed in fundamental ways: 1) high versus moderate exposure to infective bites; 2) samples drawn at the time of malaria for most donors in the high zone versus ~100 days after the last malaria episode in the moderate zone. The effect of acute malaria to boost short-term cross-reactive antibodies can confound the ability to draw inferences when comparing the two cohorts, and this should be further explored to understand its role in the patterns of seroreactivity observed.

We thank the reviewer for this very insightful comment. In endemic areas, this potential confounder is a natural occurrence – in areas of higher transmission, people will on average be more likely to have an active or recent infection. The question is whether the differences seen in repeat-containing peptides are due to cumulative exposure or recency/active exposure. To address this point, we have added new analyses, as suggested, taking into account infection status in both exposure settings. In the moderate exposure setting, we find that the breadth of response in children to repeat containing peptides significantly narrows between the most recently exposed subjects, and those that have been infection free for >240 days, indicative of a short-lived response. This difference was not observed for peptides without repeats. (New figure: Figure 5, Supplement 4). We also observe an increase in breadth for repeat-containing peptides in high vs. moderate exposure settings, regardless of infection status (New figure: Figure 5, Supplement 3), a difference that was absent in non-repeat containing peptides. Overall, these data suggest that responses to repeats are not only more exposure-dependent, but also short-lived relative to non-repeats in children. We have included this new analysis (lines 409-435.)

Reviewer #2 (Public Review):

This work profiles naturally acquired antibodies against Plasmodium falciparum proteins in two Ugandan cohorts, at incredibly high resolution, using a comprehensive library of overlapping peptides. These findings highlight the ubiquity and importance of intra- and inter-protein repeat elements in the humoral immune response to malaria. The authors discuss evidence that repeat elements reside in more seroreactive proteins, and that the breadth of immunity to repeat-containing antigens is associated with transmission intensity in children.

A key strength and value added to publicly available data are the breadth of proteome coverage and unprecedented resolution from using tiling peptides. The authors point out that a known limitation of PhIP-seq is that conformational and discontinuous-linear epitopes cannot be detected with short linear peptides. In addition, disulfide linkages and post-translational modifications would be absent in the T7 representations.

Several significant conclusions drawn from the results in this study are based on the humoral response to repeat elements that are present in multiple locations, including different genes. If antibodies to these regions are cross-reactive as described, it is not clear how the assay can differentiate antibodies that were developed against one or many of these loci. This potential confounding could change the conclusions about inter-protein motifs.

• We thank the reviewer for their comments on the study. We have added a note about post-translational modifications to the text (Line 675-676) as recommended.

• With regards to interprotein motifs (Figure 6), we only suggest a potential for antibody cross-reactivity across these motifs based on sequence similarity alone. We do not claim direct evidence that they are indeed cross-reactive, especially given the complex polyclonal nature of the response we are measuring. We present this sequence analysis only as a landscape of potential cross-reactivity among linear epitopes in the proteome, derived from the pool of seroreactive peptides enriched in this cohort.

• Regardless, we have included a new analysis following the suggestion of Reviewer #1 to determine whether reactivity to these shared motifs indeed correlates between peptides from different proteins sharing a motif within the same individual. While this analysis shows apparent cross reactivity within individuals, we point out that the data is derived from complex polyclonal repertoires inherent to each individual, and thus these observations must be taken in that context and do not definitively establish cross reactivity. Along with the new analysis (Line 495-503), we have sought to be clear on these limitations (Line 632-635).

Reviewer #3 (Public Review):

This work provides a new tool, a comprehensive PhIP-seq library, containing 238,068 individual 62-amino acids peptides tiled every 25-amino acid peptide covering all known 8,980 proteins of the deadliest malaria parasite, Plasmodium falciparum, to systematically profile antibody targets in high resolution. This phage display library has been screened by plasma samples obtained from 198 Ugandan children and adults in high and moderate malaria transmission settings and 86 US controls. This work identified that repeat elements were commonly targeted by antibodies. Furthermore, extensive sharing of motifs associated with seroreactivity indicated the potential for extensive cross-reactivity among antigens in P. falciparum. This paper provides a new proteome-wide high-throughput methodology to identify antibody targets that have been investigated by protein arrays and alpha screens to date. Importantly, only this methodology (PhIP-seq library) is able to investigate repeat-containing antigens and cross-reactive epitopes in high resolution (25-amino acid resolution).

Strengths:

1) Novel technology

Firstly, the uniqueness of this study is the use of novel technology, the PhIP-seq library. This PhIP-seq library in this study contains >99.5% of the parasite proteome and is the highest coverage among existing proteome-wide tools for P. falciparum. Moreover, this library can identify antibody responses in high resolution (25 amino acids).

Secondly, the PhIP-seq converts a proteomic assay (ie. protein array and alpha screen) into a genomic assay, leveraging the massive scale and low-cost nature of next-generation short-read sequencing.

Thirdly, the phage display system is the ability to sequentially enrich and amplify the signal to noise. Finally, a high-quality strategic bioinformatic analysis of PhIP-seq data was applied.

2) Novel findings

The major findings of this study were obtained only by using this novel technology because of its full-proteome coverage and high resolution. Repeat elements were the common target of naturally acquired antibodies. Furthermore, extensive sharing of motifs associated with seroreactivity was observed among hundreds of parasite proteins, indicating the potential for extensive cross-reactivity among antigens in P. falciparum.

3) Usefulness for the future research

Importantly, plasma samples from longitudinal cohort studies will give the scientific community important insights into protective humoral immunity which will be important for the identification of vaccine and exposure-marker candidates in the near future.

Weaknesses:

Although the paper does have strengths in principle, the weaknesses of the paper are the insufficient description of the selected parasite proteins and seroreactivity ranking of the selected proteins such as TOP100 proteins.

We thank the reviewer for their comments, corrections, and suggestions. We have made a number of changes and added new analyses, all of which have improved the work. These changes include the following:

• Analysis of breadth of seroreactivity to repeat and non-repeat regions taking into account infection status in both exposure settings.

• Analysis to test whether reactivity to peptides with interprotein motifs correlates within the same individual

• A table listing top 100 proteins in terms of their seropositivity % in response to the reviewer’s comment (Supplementary table 2b).

Author Response

Reviewer #1 (Public Review):

The authors used data from extracellular recordings in mouse piriform cortex (PCx) by Bolding & Franks (2018), they examined the strength, timing, and coherence of gamma oscillations with respiration in awake mice. During "spontaneous" activity (i.e. without odor or light stimulation), they observed a large peak in gamma that was driven by respiration and aligned with the spiking of FBIs. TeLC, which blocks synaptic output from principal cells onto other principal cells and FBIs, abolishes gamma. Beta oscillations are evoked while gamma oscillations are induced. Odors strongly affect beta in PCx but have minimal (duration but not amplitude) effects on gamma. Unlike gamma, strong, odor-evoked beta oscillations are observed in TeLC. Using PCA, the authors found a small subset of neurons that conveyed most of the information about the odor (winner cells). Loser cells were more phase-locked to gamma, which matched the time course of inhibition. Odor decoding accuracy closely follows the time course of gamma power.

We thank the reviewer for the accurate summary of our work.

I think this is an interesting study that uses a publicly available dataset to good effect and advances the field elegantly, especially by selectively analyzing activity in identified principal neurons versus inhibitory interneurons, and by making use of defined circuit perturbations to causally test some of their hypotheses.

We thank the reviewer for the positive appraisal.

Major:

• The authors show odor-specificity at the time of the gamma peak and imply that the gamma coupling is important for odor coding. Is this because gamma oscillations are important or because gamma is strongest when activity in PCx is strongest (i.e. both excitatory and inhibitory activity, which would cancel each other in the population PSTH, which peaks earlier)? To make this claim, the authors could show that odor decoding accuracy - with a small (~10 ms sliding window) - oscillates at approx. gamma frequencies. As is, Fig. 5 just shows that cells respond at slightly different times in the sniff cycle. What time window was used for computing the Odor Specificity Index? Put another way, is it meaningful that decoding is most accurate when gamma oscillations are strongest, or is this just a reflection of total population activity, i.e., when activity is greatest there is more gamma power, and odor decoding accuracy is best?

We thank the reviewer for the critical comment. Please note that the employed decoding strategy (supervised learning with cross-validation) prevents us from quantifying a time series of decoding accuracy. Nevertheless, to overcome this difficulty, we divided the spike data (0-500 ms following the inhalation start) according to the gamma cycle into four non-overlapping gamma phase bins. Then we tested whether odor decoding accuracy varied as a function of the gamma cycle phase. Using this approach, we found that decoding depended on the gamma phase, as shown below:

(The bottom plot shows the modulation of decoding accuracy within the gamma cycle [Real MI] compared to a surrogate distribution [Surr MI, obtained by circularly shifting the gamma phases by a random amount]).

We interpret this new result as indicative that gamma influences decoding accuracy directly and that our previous result was not only a reflection of total population activity. Moreover, please note that we only use the principal cell activity for computing the odor specificity index (Fig 5E) and decoding accuracy (Fig 7B). Both peak at ~150 ms following inhalation start, at a time window where the net principal cell activity is roughly similar to baseline levels (Fig 5A bottom panel).

These new panels were added to revised Figure 7 and mentioned in the revised manuscript (page 8); we now also discuss the above considerations about maximal decoding not coinciding with the peak firing rate (page 10).

Regarding the Odor Specificity Index computation, we apologize for not describing it appropriately in the corresponding Methods subsection. We employed the same sliding time window as in the population vector correlation and the decoding analyses (i.e., 100 ms window, 62.5 % overlap). This information has been added to the revised manuscript (page 15).

• The authors say, "assembly recruitment would depend on excitatory-excitatory interactions among winner cells occurring simultaneously during gamma activity." Can the authors test this prediction by examining the TeLC recordings, in which excitatory-excitatory connections are abolished?

We thank the reviewer for the relevant comment. We followed the reviewer's suggestion and analyzed odor assemblies in TeLC recordings. Interestingly, we found a greater increase in the firing rate of winner cells in TeLC recordings (see figure below), which therefore does not support our previous interpretation that assembly recruitment would depend on excitatory-excitatory local interactions.

Thus, this new result suggests a much more critical role than we previously considered for the OB projections in determining winner neurons.

Moreover, we found significant differences in the properties of loser cells. In particular, the TeLC-infected piriform cortex showed a decreased number of losing cells, which were significantly less inhibited than their contralateral counterparts:

Furthermore, the reduced inhibition of losing cells was associated with an increased correlation of assembly weights across odors for the affected hemisphere:

Therefore, we believe these results highlight the role of gamma oscillations in segregating cell assemblies and generating a sparse orthogonal odor representation in the piriform cortex. These findings are now included as new panels of Figure 6 and discussed on page 8. Noteworthy, to conform with them, we modified our speculative sentence (page 9) "assembly recruitment would depend on excitatory-excitatory interactions among winner cells occurring simultaneously during gamma activity" to “(…) the assembly recruitment would depend on OB projections determining which winner cells “escape” gamma inhibition, highlighting the relevance of the OB-PCx interplay for olfaction (Chae et al., 2022; Otazu et al., 2015).”

• The authors show that gamma oscillations are abolished in the TeLC condition and use this to claim that gamma arises in the PCx. However, PCx neurons also project back to the OB, where they form excitatory connections onto granule cells. Fukunaga et al (2012) showed that granule cells are essential for generating gamma oscillations in the bulb. Can the authors be sure that gamma is generated in the PCx, per se, rather than generated in the bulb by centrifugal inputs from the PCx, and then inherited from the bulb by the PCx?

We thank the reviewer for the pertinent comment regarding gamma generation in the PCx. To address this point, we have performed current source density (CSD) analysis, which showed sink and sources of low-gamma oscillations within the PCx and also a phase reversal:

This result – shown as panel F in Figure 1 – suggests a local generation of gamma within the PCx. Along with the fact that PCx gamma tightly correlates with piriform FBI firing and that PCx gamma disappears in the TeLC ipsi hemisphere, which has intact OB projections, we deem it more parsimonious to assume that gamma does originate in the piriform circuit during feedback inhibition acting on principal cells and is not directly inherited from OB (though it depends on its drive). We have edited our text to incorporate the figure above panel (page 4). We now also relate our results with those of Fukunaga and colleagues for the OB gamma generation and discuss the alternative interpretation of inherited gamma (page 9).

Reviewer #2 (Public Review):

This is a very interesting paper, in which the authors describe how respiration-driven gamma oscillations in the piriform cortex are generated. Using a published data set, they find evidence for a feedback loop between local principal cells and feedback interneurons (FBIs) as the main driver of respiration-driven gamma. Interestingly, odour-evoked gamma bursts coincide with the emergence of neuronal assemblies that activate when a given odour is presented. The results argue in favour of a winner-take-all mechanism of assembly generation that has previously been suggested on theoretical grounds.

We thank the reviewer for his/her work and accurate summary of our results.

The article is well-written and the claims are justified by the data. Overall, the manuscript provides novel key insights into the generation of gamma oscillations and a potential link to the encoding of sensory input by cell assemblies. I have only minor suggestions for additional analyses that could further strengthen the manuscript:

We thank the reviewer for the positive appraisal.

1) The authors' analysis of firing rates of FFIs and FBIs combined with TeLC experiments make a compelling case for respiration-driven gamma being generated in a pyramidal cell-FBI feedback mechanism. This conclusion could be further strengthened by analyzing the gamma phase-coupling of the three neuronal populations investigated. One would expect strong coupling for FBIs but not FFIs (assuming that enough spikes of these populations could be sampled during the respiration-triggered gamma bursts). An additional analysis to strengthen this conclusion could be to extract FBI- and FFI spike-triggered gamma-filtered signals. One might expect an increase in gamma amplitude following FBI but not FFI spiking (see e.g., Pubmed ID 26890123).

We thank the reviewer for the comment. To address this point, we first computed spike-coupling strength (by means of the Mean Vector Length – MVL) for each neuronal subtype. As shown below, we did not find major differences in MVL values across subtypes (if anything, the FBIs actually displayed the lowest MVL, though it should be cautioned that this metric is sensible to sample size, which differed among subtypes):

Of note, this result also translated to spike-triggered gamma-filtered signals, with FBIs having the lowest average. We don’t however believe these findings speak against a major role of FBIs in giving rise to field gamma, since it is expected that inhibited neurons will highly phase-lock to gamma (while more active neurons during gamma would show lower phase-locking). Nevertheless, we also computed the spike-triggered gamma amplitude envelope for all three neuronal subtypes. This analysis showed that gamma envelopes closely followed FBI spikes (and not FFIs or EXC cells), and thus this new result reinforces the idea that FBIs trigger gamma oscillations. This plot is now part of an inset of Figure 1G (described on page 5).

2) The authors utilize the neurons' weight in the first PC to assign them to odour-related assemblies. This method convincingly extracts an assembly for each odour (when odours are used individually), and these seem to be virtually non-overlapping. It would be informative to test whether a similar clear separation of the individual assemblies could be achieved by running the analysis on all odours simultaneously, perhaps by employing a procedure of assembly extraction that allows to deal with overlapping assembly membership better than a pure PCA approach (as used for instance in the work cited on page 11, including the authors' previous work)? I do not doubt the validity of the authors' approach here at all, but the suggested additional analysis might allow the authors to increase their confidence that individual neurons contribute mostly to an assembly related to a single odour.

We thank the reviewer for the pertinent comment. In order to address it, we ran the ICA-based approach to detect cell assemblies (Lopes-dos-Santos et al., 2013) using the spike time series of all odors concatenated. The concatenation included time windows around the gamma peak (100-400 ms after inhalation start). We chose this window to prevent the ICA from picking temporal features of the response as different ICs instead of the spiking variations caused by the different odors. As a reference, we also calculated ICA for each odor independently during the gamma peak.

We found that the results obtained from ICA computed using concatenated data from all odors show important resemblances to those from the single ICA per odor approach. For instance, we get similar sparsity and cell assembly membership (Figure 6-figure supplement 1A), orthogonality (Figure 6-figure supplement 1B), and odor specificity (Figure 6-figure supplement 1C) in the ICs loadings through both approaches. Noteworthy, the average absolute IC correlation between the six odors (computed separately) and the six first ICs (computed from the combined odor responses) were similar across animals and showed no significant differences (Figure 6-figure supplement 1C).

We also directly tested odor selectivity and separation in the concatenated data approach by computing each odor’s mean assembly activity (i.e., “IC projection”). Regarding the former, we found that most assemblies coded for 1 or 2 odors (Figure 6-figure supplement 1D). Regarding the diversity of representations for the sampled neurons, we assessed odor separation by examining to which odor each IC is activated the most. Under this framework, we get that, on average, the first 6 ICs encode three to five different odors (Figure 6-figure supplement 1E).

We have included this result as a new Figure 6-figure supplement 1 and mention it on page 8. Of note, we have also performed all of our previous assembly analyses (i.e., Figure 6) using ICA instead of PCA to be consistent throughout the manuscript and allow the reader to compare with the new supplementary figure. This led to a new and enhanced version of Figure 6.

3) Do the authors observe a slow drift in assembly membership as predicted from previous work showing slowly changing odour responses of principal neurons (Schoonover et al., 2021)? This could perhaps be quantified by looking at the expression strengths of assemblies at individual odour presentations or by running the PCA separately on the first and last third of the odour presentations to test whether the same neurons are still 'winners'.

We thank the reviewer for calling our attention to this point. We note, however, that the representation drift observed by Schoonover et al. occurred along several days of recordings, i.e., at a much slower time scale than the single-day recordings we analyzed here (of note, Schoonover et al. observed no drift within the same day [their Fig 2a]). But irrespective of this, we believe that the data at hand does not allow for a confident analysis of possible drifts. This is because each odor was only presented ~12 times; so, further subdividing the data into subsets of only 4 trials would not render a reliable analysis, unfortunately.

4) Does the winner-take-all scenario involve the recruitment of specific sets of FBIs during the activation of the individual odour-selective assemblies? The authors could address this by testing whether the rate of FBIs changes differently with the activation of the extracted assemblies.

Within each recording session, the number of recorded FBIs is very low, on average 3.6 FBIs per recording session. Thus, unfortunately such interesting analysis cannot be confidently performed.

5) Given the dependence on local gamma oscillations, one might expect that odour-selective assemblies do not emerge in the TeLC-expressing hemisphere. This could be directly tested in the existing data set.

We are thankful for the comment. We followed the reviewer's suggestion and analyzed odor assemblies in TeLC recordings, comparing the ipsilateral hemisphere (infected) with the contralateral one. Interestingly, we find an increased correlation of assembly weights across odors, suggesting that the formation/segregation of odor-selective assemblies is hindered when the principal cell synapses are abolished. This assembly selectivity reduction co-occurred as the number of losing neurons decreased, and the inhibition of the latter was also reduced. Consequently, decoding accuracy significantly decreased during the 150-250 ms window in the infected TeLC hemisphere compared to the contralateral cortex.

Therefore, we believe these new results support the role of gamma oscillations in segregating cell assemblies and generating a sparse orthogonal odor representation. These findings are now included as new panels of Figure 6 and Figure 7 and discussed on page 8.