Reviewer #2:

In the present manuscript, Bazin and colleagues describe an automatized computational approach to segment 17 subcortical nuclei from individual quantitative 7T quantitative MRI derivations. Therefore, they have trained a Bayesian "Multi-contrast Anatomical Subcortical Structure Parcellation (MASSP)" algorithm. They validate the approach in a leave-one-out fashion trained on 9/10 high-resolution scans. They assess age-related bias and report that dilated dice overlap allowing 1 voxel of uncertainty is demonstrating very high accuracy of segmentations when compared to expert delineation.

This is a straight forward work. It would certainly benefit from an additional step of out-of-center / out-of-cohort validation, but I have no serious concern that performance would be unsatisfactory. The most important limitation is acknowledged, which is the bias from anatomical variation through age or disease. The algorithm is shown to be affected by age and most certainly will be affected by contrast and size changes in neurodegenerative disorders.

The authors certainly know their field and are a driving force in open 7T research of the basal ganglia.

Reviewer #1:

The main criticisms of the work fall under categories largely centered on how the method is evaluated, rather than fundamental concerns with the method itself.

Major concerns:

1) Relative effectiveness. While a critical advancement of this method is the ability to segment many more regions than previous subcortical atlases, there are still many regions that overlap with existing segmentation tools. Knowing how the reliability of this new approach compares to previous automatic segmentation methods is crucial in being able to know how to trust the overall reliability of the method. The authors should make a direct benchmark against previous methods where they have overlap.

2) Aging analysis. The analysis of the aging effects on the segmentations seemed oddly out of place. It wasn't clear if this is being used to vet the effectiveness of the algorithm (i.e., its ability to pick up on patterns of age-related changes) or the limitations of the algorithm (i.e., the segmentation effectiveness decreases in populations with lower across-voxel contrast). What exactly is the goal with this analysis? Also, why is it limited to only a subset of the regions output from the algorithm?

3) Clarity of the algorithm. Because of the difficulty of the parcellation problem, the algorithm being used is quite complex. The authors do a good job showing the output of each stage of the process (Figures 7 & 8), but it would substantially help general readers to have a schematic of the logic of the algorithm itself.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript. Timothy Verstynen (Carnegie Mellon University) served as the Reviewing Editor.

Summary:

In this study, Bazin and colleagues propose a novel segmentation algorithm for parcelling subcortical regions of the human brain that was developed from multiple MRI measures derived from the M2RAGEME sequence acquired on a 7T MRI system. The key advancement of this approach is a reliable segmentation of more subcortical areas (17 regions) in native space than what is possible with currently available methods. The authors validate their algorithm by comparing against age-related measures.

This manuscript was reviewed by three experts in the field, who found that this method has strong potential to be a new "workhorse" tool in human neuroimaging that could substantially advance our ability to measure brain structures that are largely overlooked due to problems with segmentation. The main criticisms of the work are largely centered on how the method is evaluated & implemented, rather than fundamental concerns with the validity of the method itself.

Reviewer #3:

This paper presents a neural network based approach to predict the retinotopic organization of the human visual cortex from structural MRI data. The authors are promoting the use of non-Euclidean/geometric deep learning methods for this problem. They apply their technique to the HCP data and show some interesting results, which they claim demonstrates that functional organization in the visual system can be predicted at the individual level. For me, the paper has several substantial and important flaws.

First, one of the most important contributions of the paper is the promotion of geometric deep learning. To me, the value of this framework has not been demonstrated with the experiments. In order to assess the additional boost afforded by geometric techniques, one would need to establish a baseline with a Euclidean model. Without this comparison, it is impossible to evaluate the value of this innovation.

Second, in general, I did not find the quality of the individual-level predictions and the presented quantitative results convincing or impressive. In Figure 3, for example, I'd like to see the underlying sulcal geometry (of each subject) to assess the value of the presented "individualized" predictions. Also, the quality of the predictions, as the authors acknowledge, is significantly reduced in large parts of the cortex, including higher order areas. Importantly, though, it is not clear how much of the individual variability is truly captured in these predictions. For example, the error maps in Figure 6 for the "shuffled" and "constant" cases look very similar to the actual error maps. And quantitatively, the overall error values are very close for these cases. This suggests that the predicted retinotopic maps are not much better than a simple group average retinotopic map. One way to counter this concern would be to conduct a fingerprinting/identifiability experiment and demonstrate that the predicted maps are much closer to the observed/measured/estimated (ground truth) maps for the same individual than other individuals. Without such an analysis, it is impossible to assess how much of individual variation is captured.

The proposed smooth L1 loss was not properly justified and seems inappropriate. The threshold of 1 seems arbitrary. In fact, the cyclical nature of polar angle should require a cyclical loss function. However, this is a minor concern.

The need for dropout was not also demonstrated. Was there a concern of overfitting? Showing learning curves (for training and validation data) would help with that.

Choosing the best model based on validation loss can be improved with a "deep ensemble" strategy.

In the shuffling procedure, spatial correlation structure seems to have been destroyed. A better approach would be to randomly deform/rotate the structural image.

Setting the structural data to zero at input and assessing test time performance makes no sense and provides no real value.

I suggest that authors make their code available during peer review too. Otherwise, it is impossible to assess the reproducibility of their work.

Finally, I believe 10 is too small for the test dataset. A widely accepted convention is to use at least 10% of the total dataset for testing. I would recommend using 20 or 30 subjects for testing.

Reviewer #2:

The authors use deep learning to map brain anatomy (cortical curvature and myelination) to retinotopic maps (eccentricity and polar angle) in individual subjects.

My overall assessment of this work is that, although the idea is neat, the execution seems a bit rushed and lacks somewhat in depth of analysis.

More specifically:

1) This is my main concern: The evaluation of the method's ability to find fine-grained individual differences is somewhat anecdotal and not strongly backed by rigorous analyses.

-The idiosyncratic differences shown in Fig4a are intriguing but they could also simply be explained by gross differences in the gyral patterns of these subjects.

-The differences between the predictions of different subjects is much lower than the within-subject prediction errors.

-The authors should make these evaluations more quantitative. For example, by delineating several visual areas in the empirical datasets and predicted maps (in a blinded manner) and checking to see if the sizes of the different visual areas are well predicted at an individual level. This could even be built up in the model as a classifier for different visual areas.

-Using shuffled features as some sort of null is not appropriate in my opinion, as that breaks the statistics of the input. In fact, I am amazed that it has any predictive power at all, which it clearly does seeing that the prediction errors are similar to the empirical data (Fig 6). Why is that? Is it the case e.g. that the model learns the relation between where the edges of the visual areas mask is and the retinotopy map? What happens if you give the model a mask as input that is completely different (e.g. arbitrarily expanded or contracted). My guess is that the predictions will be vastly different and distorted.

2) It is really unclear what the approach achieves beyond finding the border between primary regions V1,V2, and V3.

-The authors should consider delineating more areas in the empirical data and showing that their predictions cover the full 0-360 and 0-12deg range in both dimensions. This analysis would greatly inform the individual variations mentioned above.

-One interesting suggestion by the authors is that dorsal areas in the IPS actually have bad empirical retinotopy data (indeed these areas might need specialised tasks, e.g. involving attentional components, i.e. attending to parts of the visual field [see Sereno et al.]). In fact the empirical data seem to predict that these regions cover a different hemifield in the shown test subjects, which is not what is expected. It would be interesting to see if the model proposed here does indeed predict, e.g. polar angle reversals in IPS1,2,3.. (I can see a hint of it in Fig3). To me, even without empirical data to compare to, this would be a strong suggestion that the authors may be capturing some genuine structure-function relations.

3) Some discussion around the modelling/quantification is lacking:

-Errors in the polar angles are really high (~30deg even in V1).

-Related to a sub-point in comment (1): why does shuffling work? Can the authors show the actual predictions of the shuffled data (as opposed to the errors) - do they look like retinotopy maps?

-Do we need deep learning? Previous work has shown simple relations between V1,V2,V3 and the geometry of the brain. Does this model actually capture more fine-grained features?

-I would have set it up as a regression against x,y coords in the visual field rather than polar coords (which have obvious wrap-around problems). This will avoid the use of tricks like rotating the visual field before training, as the authors did.

-The obvious deep-learning question: learning such a highly parameterised model based on 180*2 hemispheres sound hard. What evidence is there that this is not overfitting?

-The authors mention in the methods that the 3D coordinates were also used as features, but in their Fig2 It looks like the features are only curvature+myelin: which is it? Are 3D coords used as explicit features?

4) Show the data:

-It would be good to see the features going into these predictions and the relationship with the targets. Maybe even scatter plots of curvature/myelin vs polar angle?

-Subjects shown (test set) have very noisy maps outside the early visual cortex. Where are they in the subject-distribution of variance explained? (Benson J Vis 2018).

Reviewer #1:

The manuscript by Ribeiro, Bollmann and Puckett uses machine-learning to predict, across individuals, the retinotopic mapping from the cortical myeline and curvature map. The authors use a sophisticated method (convolutional network on the graph, called here geometric deep learning) and show appealing predicted maps of individual retinotopy in V1. While the work is interesting, the quality of the result is disappointing and the positioning to the literature imprecise.

The authors claim that their model is "able to predict retinotopic organization far beyond early visual cortex, throughout the visual hierarchy". However the figures do not seem to support this claim: the qualitative figures do not show a clear structure in the higher-level regions.

Figure 1 is appealing, however it should be compared to a simple average of all retinotopic maps. Likewise, the quantitative results in supplementary table 2 do not come with a comparison to the mean predictor (as with an R2 score), and it is not possible to judge whether these numbers are a good performance or not.

Rather, figure 6 shows that the models trained on shuffled and constant data perform qualitatively and quantitatively well. The proposed model does perform slightly better, but the statistical and practical significance of this improvement is unclear. The manuscript makes no clear attempt at judging the statistical significance, and the small number of participants in the test set (10), makes it unlikely that significance would be attained. It would be beneficial to perform a complementary analysis on a larger cohort, for instance using the 3T HCP data, at the cost of lower-quality data.

There have been many prior works that have shown the ability to predict functional organization from other mapping information. In this respect, the positioning of the present manuscript with regards to the literature is very unclear. The manuscript does acknowledge some prior work, including work using template warping, but claims that they have not "been able to capture the detailed idiosyncrasies seen in the actual measured maps of those individuals". However, no precise argument is brought forward: no quantitative measure can be compared with the prior publication, no comparison is performed. Also, individual task functional topography has been inferred from other information such as anatomical connectivity [Saygin 2012], resting-state activity [Tavor 2016], or movie watching [Eickenberg 2017]. A discussion of the relative accuracy, or pros and cons would have been interesting here.

With this in mind, the title feel much too general: "Predicting brain function from anatomy using geometric deep learning"

As a minor comment: controlling for the twin structure could be done in a more powerful way by isolating siblings in each of the train, validation, and test set so that there is one pair separated across sets.

[Saygin 2012] Saygin, Zeynep M., et al. "Anatomical connectivity patterns predict face selectivity in the fusiform gyrus." Nature neuroscience (2012)

[Tavor 2016] Tavor, I., et al. "Task-free MRI predicts individual differences in brain activity during task performance." Science 2016

[Eickenberg 2017] Eickenberg, Michael, et al. "Seeing it all: Convolutional network layers map the function of the human visual system." NeuroImage (2017)

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 2 of the manuscript. Gaël Varoquaux (INRIA) served as the Reviewing Editor.

Summary:

The reviewers all expressed interest in the research agenda as well as the methods. However, it was felt that the results did not demonstrate a clear and sufficient improvement with regards to prior art. On the methodological side, the benefit of the deep-learning formulation was not clearly revealed. On the neuroscience side, the evidence that the method captures fine inter-individual differences was felt insufficient.

Author Response

Summary:

This is an interesting and creative paper implicating a differential mechanism of intracellular trafficking and subsequent signaling that is triggered by different dynorphins binding to the kappa opioid receptor. In principle, if the authors could explain the molecular basis for this phenomenon, the story would be of tremendous impact in the fields of opioid receptor signaling and trafficking. The reviewers noted a number of concerns that would require significant further work and clarification to support the authors' conclusions.

We are very happy that you and the reviewers found that the study could be of tremendous impact and describe the paper as “interesting and creative”, “novel and intriguing”, “fascinating and novel”, and feel that the study was “nicely conducted”. We appreciate the comments of the reviewers, and we are confident that we can address the comments as below.

Reviewer #1:

General assessment: In this manuscript the authors have assessed the different endocytic routes of KOR when activated by DynA or DynB. These are nicely conducted experiments that show interesting results, however the authors completely obviate the connection with their own work that highlights the different degradation mechanisms of these two peptides. As it stands it does not add to the field, and lacks a mechanistic explanation that could be explored given the authors’ expertise in these systems.

We thank the reviewer for the positive comments. We are happy that the reviewer felt that the experiments are nicely conducted, and that the results are interesting. However, we respectfully but strongly disagree with the comments that our study does not add to the field.

First, considering the extended and severe opioid epidemic, understanding the many ways in which the opioid peptide/receptor system is modulated is of high priority. Endogenous opioid peptides are highly relevant neuromodulators about which we know even less than opioid drugs. Why there are over 20 different endogenous opioid peptides but only three receptors, has been a question that has been unanswered for decades. We show that two highly related endogenous opioids, which initially activate KOR to similar levels but subsequently diverge in trafficking and endosomal signaling. We feel that this is a clear advance in the field of opioids and GPCRs.

Second, the idea that location-biased signaling can lead to different consequences for the same agonist is still a relatively new idea, and clearly a very important area of continuing research. Even for well-studied systems like the adrenergic receptor system, we know very little about the mechanisms or the relevance of differential signaling. Demonstrating that endogenous opioids take advantage of location bias to generate distinct signaling consequences is a clear indication that such differential trafficking and signaling is physiologically relevant. Considering that opioid receptor trafficking has been implicated in opioid signaling and tolerance (although again, the mechanisms are debated), showing that different endogenous opioids can regulate localization and trafficking of the same receptor is a key advance.

Numbered summary of substantive concerns:

1) The major conclusion of the study is that after endocytosis, DynA preferentially sorts KOR into the degradative pathway, while DynB sorts KOR into the recycling pathway and this has consequences in the duration of the active state of the receptor and its ability to signal. It is surprising that the authors do not investigate the connection between these results and previously published work that shows differences in the degradation of DynB vs DynA within endosomes. Indeed, the authors have previously shown that: i) ECE2 hydrolyzes DynB and not DynA (Mzhavia et al JBC 2003), ii) overexpression of ECE2 increases the rate of mu-opioid receptor recycling upon DynB stimulation (Gupta et al BJP 2015) and iii) inhibition of ECE2 decreases mu-opioid receptor recycling (Gupta et al BJP 2015). Considering this previous work, it is totally expected that the two ligands show distinct post-endocytic trafficking of KOR.

The reviewer cites data that the surface recovery rates of a different GPCR (MOR) is regulated by ECE2, and that ECE2 differentially processes Dyn A and B, to argue that it is expected that the two ligands will direct KOR to different subcellular localizations. While our results certainly could be one logical outcome of previous data, we disagree that it is a foregone conclusion.

Specific to the reviewer’s assessment of our previous work, we were never able to test DynA previously because traditional assays did not have the sensitivity to resolve DynA-mediated recycling or trafficking. This limitation precluded the key comparison, between DynA and DynB, necessary for addressing differences between these two physiologically relevant opioid peptides. Here we use advanced high-resolution imaging experiments to carefully address how DynA and DynB diverge in directing KOR trafficking and signaling.

More generally, we have known for over a decade that the rates of GPCR recycling can be regulated by signaling pathways without changing sorting, endosomal localization, or fates (e.g., PMID: 16604070, PMID: 27226565, PMID: 25801029, PMID: 24003153). Further, many recent studies have highlighted that the details of how GPCRs are regulated and how that affects their function diverges considerably between different receptors, even though the gross signaling characteristics are nearly identical. Therefore, it is becoming increasingly clear that we cannot apply our understanding of one GPCR too broadly to argue that we expect all GPCRs are regulated in the same manner.

We also appreciate the reviewer’s interest in the question of whether and how ECE2 regulates location-specific signaling, and we agree that it will be very exciting to study. This is particularly important since ECE2 is not ubiquitously expressed in every cell type in the brain and thus cells with no/low ECE2 expression should exhibit different profiles for recycling or location-based signaling by DynA and DynB compared to cells expressing moderate/high levels of ECE2.

Nevertheless, we disagree with the reviewer’s assumption that there is an obvious correlation. ECE2 sensitivity for opioid peptides was estimated using purified peptides and enzymes, and there is no evidence that the selectivity persists in vivo. In fact, most of the previous studies measured simply the sensitivity to overexpressed ECE2. Even within these constraints, the correlation is not obvious or direct. For example, we have found that BAM22 and BAM18, two peptides that activate opioid receptors, show much lower recycling of KOR than DynB (Gupta, Gomes and Devi, INRC 2019, manuscript in preparation) even though all three are ECE2 substrates (PMID: 12560336). Therefore, it is unlikely that ECE substrate sensitivity is the only difference between these peptides.

We will be happy to provide some insight on the question of ECE sensitivity and discuss possibilities, but we feel that a thorough characterization of how ECE regulates location-specific signaling, while interesting, is outside the scope of our study that demonstrates a physiological difference between two different endogenous opioids in neurons.

Most importantly, we respectfully feel that following up and demonstrating a logical conclusion is a strength, and should not be viewed as a negative. Clearly differentiating and establishing predicted outcomes is a critical part of advancing biology. Acknowledging and supporting this is especially important in these times where there is a clear effort and an opportunity to make academic publishing open and fair.

2) Similarly, the differences in ECE2 sensitivity can also explain the Nb39 results, with KOR activated by the ligand that is not hydrolysable (DynA) being able to remain in the active state (and signal) for longer than when activated with the hydrolyzable ligand (DynB).

As described in the response to #1, we agree that it is possible that the trafficking and signaling differences we see could correlate with ECE2 substrate sensitivity. Again, we feel that the focus of the manuscript is on signaling differences between endogenous opioids, and not on how ECE inhibition regulates location-specific signaling.

3) A simple experiment to address this obvious connection is to use an ECE2 inhibitor. One would expect that in the presence of this inhibitor DynB-activated KOR is retained intracellularly and remains active for longer.

We agree that ECE inhibitors are important tools to manipulate recycling. As mentioned above, we can provide some insight towards the correlation of ECE sensitivity and trafficking and discuss possibilities, but an in-depth characterization of how ECE proteases regulate GPCR location-specific signaling is not the focus of our study.

4) The authors state "this is the first example of different physiological agonists driving spatial localization and trafficking of a GPCR" in light of the above comment, previous work from Bunnett et al have shown how peptides with different endocytic enzyme sensitivity can indeed, localize GPCRs (e.g somatostatin receptor) in different compartments and elicit distinct signals (Padilla et al J Cell Biol 2007; Roosterman et al PNAS 2007; Zhao et al JBC 2013 to name a few).

We were quite taken aback by this comment. We take previously published work very seriously, and we try to be as fair as possible when we describe them. We will be happy to modify the sentence to match the current literature.

We carefully searched through the papers the reviewer pointed out for an example where two physiological agonists drive different spatial localization and signaling of the same receptor. But we could not find one. Padilla et al., 2007, show that the recycling of CLR, activated by the ECE1-sensitive CGRP, is sensitive to ECE inhibition, but that the recycling of angiotensin receptor or bradykinin receptor, whose ligands are not sensitive to ECE, is not. Similarly, Roosterman et al., 2007, focus on how NK1 receptor recycling is sensitive to ECE1 inhibition. To the best of our knowledge, neither paper shows that spatial localization or location-biased signaling of a given GPCR is regulated differentially by two different endogenous agonists.

The closest experiment we could find are in Fig 2, titled “Agonists induce endocytosis of SSTR2A in myenteric neurons” in Zhao et al JBC 2013. This figure shows that, when cells exposed to SST14 or the pro-peptide SST28 for 1 hour at 4˚C are followed at 37˚C and fixed, SSTR labeling at the plasma membrane and cytoplasm is similar at 30 min, but diverges after that. As far as we could figure out, receptor recycling, the precise endosomal distribution, or signaling were not tested in this manuscript.

Therefore, we respectfully submit that the manuscripts the reviewer points to, which describe how the recycling of a receptor that binds an ECE-sensitive peptide is sensitive to ECE inhibition, should not be conflated with our careful analysis of whether different endogenous opioids can drive different spatial localization and signaling fates of the same opioid receptor.

We would, however, be be happy to modify the sentence to state the impact of our work more precisely and to discuss the details on SSTR trafficking in the revised manuscript. If the reviewer would point us to specific examples that show that subcellular localization and spatially restricted signaling of a given GPCR is regulated differentially by two different endogenous agonists, we will be more than happy to include a discussion of that work.

5) Support for endosomal signalling falls a bit short. For example, if indeed KOR signals from endosomes, the authors should use an inhibitor of receptor internalization and assess Nb39 recruitment and KOR signalling.

We agree this experiment will support the conclusion, and we will be happy to provide this data.

Reviewer #2:

This manuscript demonstrates that two highly similar endogenous opioid agonists can give distinct opioid receptor trafficking and signaling fates. There are two key observations that are novel and intriguing: 1) two opioid peptides that are derived from the same precursor can distinctly modulate Kappa Opioid receptor (KOR) trafficking into two distinct pathways; Dynorphin A causes KOR trafficking to the late endosomes/lysosomes pathway whereas Dynorphin B promotes rapid recycling; 2) Dynorphin A activates Gi proteins on the late endosomes/lysosomes which leads to Gi-mediated cAMP inhibition from these compartments.

The idea that GPCRs can activate G proteins at the late endosome/lysosomal compartments is fascinating and novel, however, the data presented here does not fully support their model that Dynorphin A activated Gi proteins on the late endosomes/lysosomes.

We are very happy that the reviewer found our study fascinating and novel. We thank the reviewer for the comments, and we can address them as follows.

Main questions:

1) There is a mismatch with the timing of receptor colocalization experiment (Fig 3B and C, 20 min Dynorphin A/B treatment) and the cAMP assay (Fig 3H, 5 min treatment). There needs to be direct evidence that KOR is localized on the late endosomes/lysosomes at 5 minutes post agonist stimulation, i.e. at the time that cAMP levels are measured. It is important to demonstrate that the sustained signaling inhibition by DynA comes from the late endosomes/lysosomes as opposed to early endosomes. A colocalization experiment with 5 min DynA stimulation followed by a 25min washout would be necessary to support their model.

We agree that this is a good point, and we will be happy to perform the experiment suggested. In addition, we can also provide live cell imaging data, where we simultaneously localize the nanobody that recognizes active KOR with a lysosomal marker and KOR, to show that they colocalize after DynA treatment.

2) What percentage of KORs are proteolytically degraded in the late endosomes/lysosomes at 20 min DynA stimulation?

At 20 min, although some of the receptors reach the lysosome, it is unlikely that there is significant degradation. This is supported by our blots that show similar levels of KOR expression at 30 minutes, and loss of receptor levels at 2 hours. This is also roughly consistent with previous studies on GPCR degradation. We will include these details in the revised manuscript.

3) Given that KOR trafficking to the late endosomes and lysosomes is mediate by ubiquitination (as shown here PMID: 18212250), does mutation of these ubiquitination sites (3 lysine residues on KOR C-terminus) block its trafficking and the sustained signaling from the late endosomes/lysosomes?

The reviewer raises an interesting topic that has been a subject of considerable debate in the GPCR trafficking field. The mutation of the three lysine residues on the KOR C-terminus cause more residual KOR levels after 4 hours of Dyn A, suggesting that degradation/downregulation of KOR is reduced in these mutants, even though internalization is comparable. For some opioid receptors, although ubiquitination might be required for involution and entry into the intralumenal vesicles, lysosomal localization is arguably independent of ubiquitination. Ubiquitination and/or lysine residues that interact with Ub-transferases could also affect downstream signaling, especially in the endosomes, by some GPCRs. Therefore, we feel that interpretation of results from the lysine mutant receptors will not be straightforward. Nevertheless, we appreciate that this is an interesting point, and we will address this in the revised manuscript.

4) Is there any evidence for Gi protein localization on the late endosome/lysosomes?

This is another interesting point raised by the reviewer, as the majority of endosomal signaling data rely on Gs-coupled or Gq-coupled receptors. However, Gi-coupled GPCRs, such as the cannabinoid receptor or the related mu opioid receptor can exist in the active conformation in endosomes (e.g, PMID: 18267983, PMID: 29754753), and internalization is required for sustained cAMP inhibition for the Class B S1P receptor (PMID: 24638168). These provide indirect evidence that Gi proteins might be present and active on endosomes.

Unfortunately, directly testing whether Gi proteins are active on endosomes has been technically challenging, unlike with Gs proteins. The main limitation has been the lack of conformation-sensors for Gi proteins. We will be happy to discuss these points in the revised manuscript.

5) Additional functional readouts would also be helpful to support their model of Gi-mediated inhibition of cAMP response from late endosomes/lysosomes and not the plasma membrane or early endosomes. Perhaps mTOR activation (as authors have suggested in their discussion) could be used as a read out to show differences between DynA and B-mediated signaling?

We will be happy to test endosome-based mTOR signaling downstream of KOR to see if there is a difference between DynA and B. Since our data already suggest that the main impact might be on cAMP signaling, we will also discuss the implications to cAMP signaling.

Reviewer #3:

This is an interesting idea and creative paper implicating a differential mechanism of intracellular trafficking and subsequently signaling that is triggered by different dynorphins binding to the kappa opioid receptor. However, there are some questions for the authors:

We thank the reviewer for the comments that the paper is interesting and creative, and for the critique. We are confident that we can fully address them as follows.

1) My reading is that some dynorphins are extremely rapidly degraded in serum and with these experiments performed in 15% Horse/FCS there is concern that some of the differential results could be explained by differential degradation. One hypothesis could be a differential frequency of receptor activation over time of a fast recycling receptor population. Can the authors convince me that this difference in trafficking and subsequent signaling is an intrinsic property of the peptide and not an exhaustion of peptide (would be DynB) over the 30min assay?

We agree this is an important point, and we apologize for not specifically addressing this point. For the trafficking experiments, we directly compared results from experiments done with and without protease inhibitors. We saw no difference between the two conditions, possibly because we were using short time points, high enough concentrations, and dialyzed serum. We agree that it will be important to include these data in the revised manuscript. The signaling experiments, which required longer incubations, were performed in the presence of protease inhibitors, consistent with previous studies.

2) In Fig 2D, 2G and 2J at what time after addition peptides was this data obtained?

For measuring individual recycling events (2D and G), cells were treated with agonist for 5 minutes at 37°C. Receptor clustering was visualized using TIRF microscopy, and then a recycling movie was recorded at 10 Hz for 1 minute in TIRF. For 2J, we measured 2 time points, 30 min and 120 min after agonist addition. We apologize for not stating these details in the figure, and will be happy to do so.

3) In Fig 2F the divergence of internalized receptor only occurs from time 20-30 mins which was difficult for me to understand since DynA should result in lost surface receptor number. What confuses me is that in Fig2H the initial recycling induced by DynA17 is fast and slows down so I am wondering if a second hit is needed which feeds into my concern about peptide degradation in the media. Since released peptide would be pulsatile maybe in vivo DynA17 could act like DynB?

We realize that a better explanation is needed for the recycling experiment performed in 2F. The cells were imaged for a period of 2 minutes to collect baseline SpH fluorescence, which corresponds to the steady-state amount of KOR on the cell surface. After this period, cells were imaged for 15 min after DynA or DynB was added. In this period, because internalization is the predominant factor affecting surface levels, we see a loss in fluorescence as the receptors are internalized and SpH is quenched in the relatively acidic compartments. Because KOR internalization rates are not dramatically different between DynA and B, we do not expect the fluorescence traces to be different. The agonist was then washed out at this time (t=17), and cells were imaged in media containing antagonist. Because there is very little agonist-induced internalization after this point, the fluorescence change depends predominantly on reappearance of receptors via recycling. Therefore, if the main difference between DynA and DynB is in KOR recycling, we expect to see a divergence only in the late points of the trace.

We thank the reviewer for carefully viewing the traces in 2F and 2H. We understand the interpretation that there might be fast and slow components to DynA induced recycling. While it certainly is possible, we are not comfortable making a strong conclusion on that, based on the sensitivity of the assays used and the variability between cells.

As mentioned in point#1, it is unlikely, however that this divergence in recycling is due to significant degradation of DynA. Nevertheless, it is an important point to discuss in light of the new data we provide, and we will be happy to explain this in detail.

4) The assays seem to be done with a single concentration of peptide - 1µM. Do the authors have data to show that at lower (or higher) concentrations than 1µM result in the same trafficking patterns, albeit to a lesser or greater extent. Also, for the cAMP inhibition what concentration gives max inhibition? For a binding affinity of 0.01nM in the cells and with high expression, the 1micromolar concentration seems high.

We used the 1µM dose based on careful dose-response measurements for cAMP signaling. Part of the dose-response data has been published (PMID: 32393639). We will be happy to provide the extended data, and also provide a dose-response for trafficking. It is possible that the dose is what helps us mitigate potential degradation of the peptides.

5) In Fig 2H 100% of receptors appear to be recycled after DynB however 25% of kappa colocalize in Rab7 in 3C so do these Rb 7 co-localized receptors recycle?

It is certainly possible that some receptors from Rab7 endosomes can recycle. Current views are more aligned with overlapping populations of endosomes as labelled by biochemical markers, especially by trafficking components like Rabs. Therefore, our characterization likely describes a spread of receptor distributions across overlapping compartments. Moreover, the recycling of receptors in Fig 2H was quantitated using ELISA over 2 hours after agonist washout. The endosome colocalization in 3C was measured after 20 min of agonist treatment. As the reviewer would agree, it is difficult to directly compare data from these two experiments and draw definite conclusions.

That said, we certainly did not mean to imply that all of DynB-activated KOR is recycled and that DynA-activated KOR is degraded. Current data on trafficking support a more dynamic and flexible model for receptor sorting, where a fraction of the receptors is recycled while a fraction is degraded from each endosome. Our results are consistent with this model. We feel that, because the receptor populations undergo many rounds of rapid iterative sorting as the endosome matures, a larger fraction is recycled back to the surface in the case of DynB at a steady state, while a larger fraction stays behind in the case of DynA. Importantly, this difference in steady state localization is enough to cause a difference in endosomal receptor activation and cAMP signaling, suggesting that small differences in steady state localization can cause relevant changes in signaling.

We apologize for not making this important point clearer, and we will be happy to clarify this in the revised manuscript.

6) Could some of the signaling differences be explained by continued activation of receptors as a consequence of peptide processing in the endocytosed vesicle as opposed to different vesicles? I guess the continued signaling could also direct subsequent trafficking and this could be tested with a membrane permeable antagonist.

We thank the reviewer for raising this point. As we described in our response to reviewer#1, peptide processing by ECE proteases could contribute to the differences, but the data suggest that this is not a direct correlation or the main explanation for the differences we observe. We will be happy to provide data to address this aspect.

7) The impact statement "Co-released dynorphins, which signal similarly from the cell surface, can differentially localize GPCRs to specific subcellular compartments, and cause divergent receptor fates and distinct spatiotemporal patterns of signaling" could be misconstrued. If one of the pathways is dominant and blocks the other, then co-release may only have one signaling outcome. Have any dynorphin mix experiments been conducted? What might be anticipated?

We agree that the question of whether one peptide is dominant is an interesting one in the context of the paper, and we thank the reviewer for pointing this out. Assay sensitivity has remained a long-standing problem when trying these mixed experiments in the endogenous opioid system. We will be happy to try a dynorphin mix experiment with our state-of-the-art imaging assays. We will also revise the sentence to reduce ambiguity.

8) It looks like details for the ELISA measurements in the methods section was missing. Were the ELISA measurements done with untagged KOR or SpH-KOR? One might worry about the effects of the N-terminal SpH tag on KOR trafficking, and it would be nice if the fluorescence SpH-KOR data were supported by ELISA for untagged KOR. (At least some of the data is immunostaining of FLAG-KOR, which probably introduces only minimal perturbation)

We apologize for not including the details of the ELISA experiments. The ELISA experiments were performed essentially as described previously (PMID: 24990314; PMID: 24847082). Briefly, CHO-KOR cells or SpH-KOR cells (2x105) were seeded in complete growth media into each well of a 24 well poly-lysine coated plate. The following day cells were washed once in PBS, placed on ice and incubated with 1:1000 dilution (PBS containing 1% BSA) of either anti-Flag M1 mouse monoclonal antibody (for CHO-KOR cells), or anti-GFP rabbit polyclonal antibody (for SpH-KOR) for 1h at 4˚C. Cells were then gently washed twice with PBS and treated without or with 1mM peptides in either F-12 medium (for CHO-KOR cells) or F-12K(for SpH-KOR) containing protease inhibitor cocktail (Sigma) for 30 min at 37oC to induce receptor internalization. Cells were then washed and incubated in media without peptides for different time periods (5-120 min). Cells were chilled to 4˚C and briefly fixed with paraformaldehyde for 3 min. Cells were then incubated with 1:1000 dilution of either anti-mouse or anti-rabbit HRP-coupled secondary antibody. The substrate o-phenylenediamine (5 mg/10 ml in 0.15 M citrate buffer, pH 5, containing 20 ul of H2O2 ) was added to each well (100 ul) and reaction stopped after 10 min by addition of 50 ul 1N HCl. Absorbance at 490 nm was measured with a Bio-Rad ELISA reader. We will definitely correct this oversight and include these details in the revised manuscript.

The reviewer’s concern about the tag is a valid one, and one that we are very careful about. We have used three different tags to label the receptor, all on the N-terminus to reduce potential interference. The ELISA measurements were done using FLAG-tagged and HA-tagged KOR. The trafficking experiments were done with FLAG-tagged and SpH-tagged KOR. The results are consistent between all these experiments, suggesting that the difference we observe are not due to tagging. We will clarify these details in the revised manuscript.

9) Dynorphin A17 is a very sticky peptide and difficult to wash out. Since we don't have a dose response it may require only very doses to have full activation for cAMP inhibition. It would be nice to be able to discount this as a potential for prolonged activation after washout.

The reviewer brings up a good point. DynA is less sticky in media or solutions containing 150mM NaCl, but we realize that this is a concern that should be addressed. In our case, we picked the doses we used based on dose-response curves that we have performed for cAMP signaling for these peptides. We realize that it is important to explain the choice of our concentrations better, and we will be happy to do so in the revised manuscript.

Reviewer #3:

This is an interesting idea and creative paper implicating a differential mechanism of intracellular trafficking and subsequently signaling that is triggered by different dynorphins binding to the kappa opioid receptor. However, there are some questions for the authors:

1) My reading is that some dynorphins are extremely rapidly degraded in serum and with these experiments performed in 15% Horse/FCS there is concern that some of the differential results could be explained by differential degradation. One hypothesis could be a differential frequency of receptor activation over time of a fast recycling receptor population. Can the authors convince me that this difference in trafficking and subsequent signaling is an intrinsic property of the peptide and not an exhaustion of peptide (would be DynB) over the 30min assay?

2) In Fig 2D, 2G and 2J at what time after addition peptides was this data obtained?

3) In Fig 2F the divergence of internalized receptor only occurs from time 20-30 mins which was difficult for me to understand since DynA should result in lost surface receptor number. What confuses me is that in Fig2H the initial recycling induced by DynA17 is fast and slows down so I am wondering if a second hit is needed which feeds into my concern about peptide degradation in the media. Since released peptide would be pulsatile maybe in vivo DynA17 could act like DynB?

4) The assays seem to be done with a single concentration of peptide - 1µM. Do the authors have data to show that at lower (or higher) concentrations than 1µM result in the same trafficking patterns, albeit to a lesser or greater extent. Also, for the cAMP inhibition what concentration gives max inhibition? For a binding affinity of 0.01nM in the cells and with high expression, the 1micromolar concentration seems high.

5) In Fig 2H 100% of receptors appear to be recycled after DynB however 25% of kappa colocalize in Rab7 in 3C so do these Rb 7 co-localized receptors recycle?

6) Could some of the signaling differences be explained by continued activation of receptors as a consequence of peptide processing in the endocytosed vesicle as opposed to different vesicles? I guess the continued signaling could also direct subsequent trafficking and this could be tested with a membrane permeable antagonist.

7) The impact statement "Co-released dynorphins, which signal similarly from the cell surface, can differentially localize GPCRs to specific subcellular compartments, and cause divergent receptor fates and distinct spatiotemporal patterns of signaling" could be misconstrued. If one of the pathways is dominant and blocks the other, then co-release may only have one signaling outcome. Have any dynorphin mix experiments been conducted? What might be anticipated?

8) It looks like details for the ELISA measurements in the methods section was missing. Were the ELISA measurements done with untagged KOR or SpH-KOR? One might worry about the effects of the N-terminal SpH tag on KOR trafficking, and it would be nice if the fluorescence SpH-KOR data were supported by ELISA for untagged KOR. (At least some of the data is immunostaining of FLAG-KOR, which probably introduces only minimal perturbation)

9) Dynorphin A17 is a very sticky peptide and difficult to wash out. Since we don't have a dose response it may require only very doses to have full activation for cAMP inhibition. It would be nice to be able to discount this as a potential for prolonged activation after washout.

Reviewer #2:

This manuscript demonstrates that two highly similar endogenous opioid agonists can give distinct opioid receptor trafficking and signaling fates. There are two key observations that are novel and intriguing: 1) two opioid peptides that are derived from the same precursor can distinctly modulate Kappa Opioid receptor (KOR) trafficking into two distinct pathways; Dynorphin A causes KOR trafficking to the late endosomes/lysosomes pathway whereas Dynorphin B promotes rapid recycling; 2) Dynorphin A activates Gi proteins on the late endosomes/lysosomes which leads to Gi-mediated cAMP inhibition from these compartments.

The idea that GPCRs can activate G proteins at the late endosome/lysosomal compartments is fascinating and novel, however, the data presented here does not fully support their model that Dynorphin A activated Gi proteins on the late endosomes/lysosomes.

Main questions:

1) There is a mismatch with the timing of receptor colocalization experiment (Fig 3B and C, 20 min Dynorphin A/B treatment) and the cAMP assay (Fig 3H, 5 min treatment). There needs to be direct evidence that KOR is localized on the late endosomes/lysosomes at 5 minutes post agonist stimulation, i.e. at the time that cAMP levels are measured. It is important to demonstrate that the sustained signaling inhibition by DynA comes from the late endosomes/lysosomes as opposed to early endosomes. A colocalization experiment with 5 min DynA stimulation followed by a 25min washout would be necessary to support their model.

2) What percentage of KORs are proteolytically degraded in the late endosomes/lysosomes at 20 min DynA stimulation?

3) Given that KOR trafficking to the late endosomes and lysosomes is mediate by ubiquitination (as shown here PMID: 18212250), does mutation of these ubiquitination sites (3 lysine residues on KOR C-terminus) block its trafficking and the sustained signaling from the late endosomes/lysosomes?

4) Is there any evidence for Gi protein localization on the late endosome/lysosomes?

5) Additional functional readouts would also be helpful to support their model of Gi-mediated inhibition of cAMP response from late endosomes/lysosomes and not the plasma membrane or early endosomes. Perhaps mTOR activation (as authors have suggested in their discussion) could be used as a read out to show differences between DynA and B-mediated signaling?

Reviewer #1:

General assessment:

In this manuscript the authors have assessed the different endocytic routes of KOR when activated by DynA or DynB. These are nicely conducted experiments that show interesting results, however the authors completely obviate the connection with their own work that highlights the different degradation mechanisms of these two peptides. As it stands it does not add to the field, and lacks a mechanistic explanation that could be explored given the authors’ expertise in these systems.

Numbered summary of substantive concerns:

1) The major conclusion of the study is that after endocytosis, DynA preferentially sorts KOR into the degradative pathway, while DynB sorts KOR into the recycling pathway and this has consequences in the duration of the active state of the receptor and its ability to signal. It is surprising that the authors do not investigate the connection between these results and previously published work that shows differences in the degradation of DynB vs DynA within endosomes. Indeed, the authors have previously shown that: i) ECE2 hydrolyzes DynB and not DynA (Mzhavia et al JBC 2003), ii) overexpression of ECE2 increases the rate of mu-opioid receptor recycling upon DynB stimulation (Gupta et al BJP 2015) and iii) inhibition of ECE2 decreases mu-opioid receptor recycling (Gupta et al BJP 2015). Considering this previous work, it is totally expected that the two ligands show distinct post-endocytic trafficking of KOR.

2) Similarly, the differences in ECE2 sensitivity can also explain the Nb39 results, with KOR activated by the ligand that is not hydrolysable (DynA) being able to remain in the active state (and signal) for longer than when activated with the hydrolyzable ligand (DynB).

3) A simple experiment to address this obvious connection is to use an ECE2 inhibitor. One would expect that in the presence of this inhibitor DynB-activated KOR is retained intracellularly and remains active for longer.

4) The authors state "this is the first example of different physiological agonists driving spatial localization and trafficking of a GPCR" in light of the above comment, previous work from Bunnett et al have shown how peptides with different endocytic enzyme sensitivity can indeed, localize GPCRs (e.g somatostatin receptor) in different compartments and elicit distinct signals (Padilla et al J Cell Biol 2007; Roosterman et al PNAS 2007; Zhao et al JBC 2013 to name a few).

5) Support for endosomal signalling falls a bit short. For example, if indeed KOR signals from endosomes, the authors should use an inhibitor of receptor internalization and assess Nb39 recruitment and KOR signalling.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Summary:

This is an interesting and creative paper implicating a differential mechanism of intracellular trafficking and subsequent signaling that is triggered by different dynorphins binding to the kappa opioid receptor. In principle, if the authors could explain the molecular basis for this phenomenon, the story would be of tremendous impact in the fields of opioid receptor signaling and trafficking. The reviewers noted a number of concerns that would require significant further work and clarification to support the authors' conclusions.

Note: This rebuttal was posted by the corresponding author to Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

Reviewer1

Reviewer #1 (Evidence, reproducibility and clarity (Required)):

The manuscript is clearly written and the figures appropriate and informative. Some descriptions of data analyses are a little dense but reflect what would appear long hard efforts on the part of the authors to identify and control for possible sources of misinterpretation due to sensitivities of parameters in their fitness model. The authors efforts to retest interactions under non-competition conditions allay fears of most concerns that I would have. One problem though that I could not see explicitly addressed was that of potential effects of interactions between methotrexate and the other conditions and how this is controlled for. Specifically, I could be argued that the fact that a particular PPI is observed under a specific condition could have more to do with a synthetic effect of treatment of cells with a drug plus methotrexate. Is this controlled for and how? I raise this because in a chemical genetic screen for fitness it was shown that methotrexate is particularly promiscuous for drug-drug interactions (Hillenmeyer ME ,et al. Science 2008). I tried to think of how this works but couldn't come up with anything immediately. I'd appreciate if the authors would take a crack at resolving this issue. Otherwise I have no further concerns about the manuscript.

We thank the reviewer for the kind comments. We agree with the reviewer’s point that methotrexate could be interacting with drugs or other perturbagens, similar to how the chosen nitrogen source, carbon source, or other growth conditions may interact with a drug. However, the methotrexate concentration is held constant across all conditions, as is the rest of the media components such as the nitrogen and carbon source (with the exception of the raffinose perturbation). Any interactions with methotrexate, or other media components, is undetectable without systematically varying all components for all stressors. Therefore, we use the typical experimental design of measuring molecular variation from a reference, holding invariant media components (such as methotrexate, glucose, or vitamins) fixed between conditions. This is a general practice, and we describe that every condition contains methotrexate on page 3, line 10.

The library was grown under mild methotrexate selection in 9 environments for 12-18 generations in serial batch culture, diluting 1:8 every ~3 generations, with a bottleneck population size greater than 2 x 109 cells (Table S1).

We also list the full details of each environment in Table S1.

Reviewer #1 (Significance (Required)):

Lui et al expand on previous work from the Levy group to explore a massive in vivo protein interactome in the yeast S. cerevisiae. They achieve this by performing screens cross 9 growth conditions, which, with replication, results in a total of 44 million measurements. Interpreting their results based on a fitness model for pooled growth under methotrexate selection, they make the key observation that there is a vastly expanded pool of protein-protein interactions (PPI) that are found under only one or two condition compared to a more limited set of PPI that are found under a broad set of conditions (mutable versus immutable interactors). The authors show that this dichotomy suggests some important features of proteins and their PPIs that raise important questions about functionality and evolution of PPIs. Among these are that mutable PPIs are enriched for cross-compartmental, high disorder and higher rates of evolution and subcellular localization of proteins to chromatin, suggesting roles in gene regulation that are associated with cellular responses to new conditions. At the same time these interactions are not enriched for changes in abundance. These results are in contrast to those of immutable PPIs, which seem to form a core background noise, more determined by changes in abundance than what the authors interpret must be post-translational processes that may drive, for instance, changes in subcellular localization resulting in appearance of PPIs under specific conditions. The authors are also able to address a couple of key issues about protein interactomes, including the controversial Party-date Hub hypothesis of Vidal, in which they could now affirm support for this hypothesis based on their results and notably negative correlation of PPIs to protein abundance for mutable PPIs. Finally, they also addressed the problem of predicting the upper limit of PPIs in yeast, showing the remarkable results that it may be no more than about 2 times the number of proteins expressed by yeast. Such an upper limit is profoundly important to modelling cellular network complexity and, if it holds up, could define a general upper limit on organismal complexity.

This manuscript is a very important contribution to understanding dynamics of molecular networks in living cells and should be published with high priority.

Reviewer 2

Reviewer #2 (Evidence, reproducibility and clarity (Required)):

Report on Liu et al. "A large accessory protein interactome is rewired across environments"

Liu et al. use a mDHFR-based, pooled barcode sequencing / competitive growth / mild methotrexate selection method to investigate changes of PPI abundance of 1.6 million protein pairs across different 9 growth conditions. Because most PPI screens aim to identify novel PPIs in standard growth conditions, the currently known yeast PPI network may be incomplete. The key concept is to define immutable" PPIs that are found in all conditions and "mutable" PPIs that are present in only some conditions.

The assay identified 13764 PPIs across the 9 conditions, using optimized fitness cut offs. Steady PPI i.e. across all environments, were identified in membrane compartments and cell division. Processes associated with the chromosome, transcription, protein translation, RNA processing and ribosome regulation were found to change between conditions. Mutable PPIs are form modules as topological analyses reveals.

Interestingly, a correlation on intrinsic disorder and PPI mutability was found and postulated as more flexible in the conformational context, while at the same time they are formed by less abundant proteins.

I appreciate the trick to use homodimerization as an abundance proxy to predict interaction between heterodimers (of proteins that homodimerize). This "mass-action kinetics model" explains the strength of 230 out of 1212 tested heterodimers.

A validation experiment of the glucose transporter network was performed and 90 "randomly chosen" PPIs that were present in the SD environment were tested in NaCl (osmotic stress) and Raffinose (low glucose) conditions through recording optical density growth trajectories. Hxt5 PPIs stayed similar in the tested conditions, supported by the current knowledge that Hxt5 is highly expressed in stationary phase and under salt stress. In Raffinose, Hxt7, previously reported to increase the mRNA expression, lost most PPIs indicating that other factors might influence Hxt7 PPIs.

**Points for consideration:**

*) A clear definition of mutable and immutable is missing, or could not be found e.g. at page 4 second paragraph.

We thank the reviewer for pointing this out. We have now added better definition of mutable and immutable on line 19 page 4:

We partitioned PPIs by the number of environments in which they were identified and defined PPIs at opposite ends of this spectrum as “mutable” PPIs (identified in only 1-3 environments) and “immutable” (identified in 8-9 environments).

*) Approximately half of the PPIs have been identified in one environment. Many of those mutable PPIs were detected in the 16{degree sign}C condition. Is there an explanation for the predominance of this specific environment? What are these PPIs about?

The reviewer is correct that ~40% of the PPIs identified in only one environment were found in the 16 ℃ environment. One reason for this could be technical: the positive predictive value (PPV) is the lowest amongst the conditions (16 ℃: 31.6%, mean: 57%, Table SM6). It must be noted, however, that PPVs are calculated using reference data that has generally been collected in standard growth conditions. So, it might be expected that the most divergent environment from standard growth conditions (resulting in the most differences in PPIs) would result in a lower PPV in our study even if the true frequency of false positives was equivalent across environments. We have attempted to be transparent about the quality of the data in each environment by reporting PPVs and other metrics in Table SM6. However, we suspect that the large number of PPIs unique to 16 ℃ is due in part to the fact that it causes the largest changes in the protein interactome, and believe that it should be included, even at the risk of lowering the overall quality of the data. The main reason for this is that this data is likely to contain valuable information about how the cell copes with this stress. For example, we find, but do not highlight in the manuscript, that 16 ℃-specific PPIs contain two major hubs (DID4: 285 PPIs involved in endocytosis and vacuolar trafficking, and DED1: 102 PPIs involved in translation), both of which are reported to be associated with cold adaptation in yeast (Hilliker et al., 2011; Isasa et al., 2015).

To assess whether the potentially higher false-positive rate in 16 ℃ could be impacting our conclusions related to PPI network organization and features of immutable and mutable PPIs, we repeated these analyses leaving out the 16 ℃ data and found that our main conclusions did not change. This new analysis is now presented in Figure S8 and described on page 5, line 10.

Finally, we used a pair of more conservative PPI calling procedures that either identified PPIs with a low rate of false positives across all environments (FPR

We have also added references to other panels in Figure S8 throughout the manuscript, where appropriate.

*) 50 % overall retest validation rate is fair and reflects a value comparable to other large-scale approaches. However what is the actual variation, e.g. between mutable PPIs and immutable or between condition. e.g. at 16{degree sign}C.

We validated 502 PPIs present in the SD environment and an additional 36 PPIs in the NaCl environment. As the reviewer suggests, we do indeed observe differences in the validation rate across mutability bins. This data is reported in Figures 3B and S6B, and we use this information to provide a confidence score for each PPI on page 5, line 4.

To better estimate how the number of PPIs changes with PPI mutability, we used these optical density assays to model the validation rate as a function of the mean PPiSeq fitness and the number of environments in which a PPI is detected. This accurate model (Spearman's r =0.98 between predicted and observed, see Methods) provided confidence scores (predicted validation rates) for each PPI (Table S5) and allowed us to adjust the true positive PPI estimate in each mutability bin. Using this more conservative estimate, we still found a preponderance of mutable PPIs (Figure S6E).

The validation rate in NaCl is similar to SD (39%, 14/36), suggesting that validation rates do not vary excessively across environments. Because validation experiments are time consuming (we performed 6 growth experiments per PPI), performing a similar scale of validations in all environments as in SD would be resource intensive. Insead, we report a number of metrics (true positive rate, false positive rate, positive predictive value) in Table SM6 using large positive and random reference sets. We believe these metrics are sufficient for readers to compare the quality of data across environments.

*) What is the R correlation cutoff for PPIs explained in the mass equilibrium model vs. not explained?

We do not use an R correlation cutoff to assess if a PPI is explained by the mass-action equilibrium model. We instead rely on ordinary least-squares regression as detailed in the methods on page 68, line 13.

...we used ordinary least-squares linear regression in R to fit a model of the geometric mean of the homodimer signals multiplied by a free constant and plus a free intercept. Significantly explained heterodimer PPIs were judged by a significant coefficient (FDR 0.05, single-test). This criteria was used to identify PPIs for which protein expression does or does not appear to play as significant of a role as other post-translational mechanisms.

The first criterion identifies a quantitative fit to the model of variation being related. The second criterion is used to filter out PPIs for which the relationship appears to be explained by more than just the homodimer signals. This approach is more stringent, but we believe this is the most appropriate statistical test to assess fit to this linear model.

*) 90 "randomly chosen" PPIs for validation. It needs to be demonstrated that these interaction are a random subset otherwise is could also mean cherry picked interactions.

We selected 90 of the 284 glucose transport-related PPIs for validation using the “sample” function in R (replace = FALSE). We have now included text that describes this on page 63, line 3 in the supplementary methods:

Diploids (PPIs) on each plate were randomly picked using the “sample” function in R (replace = FALSE) from PPIs that meet specific requirements.

*) Figure 4 provides interesting correlations with the goal to reveal properties of mutable and less mutable PPIs. PPIs detected in the PPIseq screen can partially be correlated to co-expression (4A) as well as co-localization. Does it make sense to correlate the co-expression across number of conditions? Are the expression correlation condition specific. In this graph it could be that expression correlation stems from condition 1 and 2 and the interaction takes place in 4 and 5 still leading to the same conclusion ... Is the picture of the co-expression correlation similar when you simply look at individual environments like in S4A?

We use co-expression mutual rank scores from the COXPRESdb v7.3 database (Obayashi et al., 2019). These mutual rank scores are derived from a broad set of 3593 environmental perturbations that are not limited to the environments we tested here. By using this data, we are asking if co-expression in general is correlated with mutability and report that it is in Figure 4A. We thank the reviewer for pointing out that this was not clear and have now added text to clarify that the co-expression analysis is derived from external data on page 6, line 7.

We first asked whether co-expression is indeed a predictor of PPI mutability and found that it is: co-expression mutual rank (which is inversely proportional to co-expression across thousands of microarray experiments) declined with PPI mutability (Figures 4A and S11) (Obayashi and Kinoshita, 2009; Obayashi et al., 2019).

The new figure S11 examines how the co-expression mutual rank changes with PPI mutability for PPIs identified in each environment, as the reviewer suggested. For each environment, we find the same general pattern as in Figure 4A (which considers PPIs from all environments).

*) Figure 4C: Interesting, how dependent are the various categories?

It is well known that many of these categories are correlated (e.g. mRNA expression level and protein abundance, and deletion fitness effect and genetic interaction degree). However, we believe it is most valuable to report the correlation of each category with PPI mutability independently in Figures 4C and S12, since similar correlations with related categories provide more confidence in our conclusions.

*) Figure 4 F: When binned in the number of environments in which the PPI was found, the distribution peaks at 6 environments and decreases with higher and lower number of environments. The description /explanation in the text clearly says something else.

We reported on page 7, line 15:

We next used logistic regression to determine what features may underlie a good or poor fit to the model (Figure S14C) and found that PPI mutability was the best predictor, with more mutable PPIs being less frequently explained (Figure 4F). Unexpectedly, mean protein abundance was the second best predictor, with high abundance predicting a poor fit to the model, particularly for less mutable PPIs (Figure S14D and S14E).

As the reviewer notes, Figure 4F shows that the percent of heterodimers explained by the model does appear to decrease for PPIs observed in the most environments. We suspect that the reviewer is correct that something more complicated is going on. One possibility is that extraordinarily stable PPIs (stable in all conditions) would have less quantitative variation in protein or PPI abundance across environments. If this is true, it would be statistically difficult to fit the mass action kinetics model for these PPIs (lower signal relative to noise), thereby resulting in the observed dip.

A second possibility is that multiple correlated factors are associated with contributing positively or negatively to a good fit, and the simplicity of Figure 4F or a Pearson correlation does not capture this interplay. This second possibility is why we used multivariate logistic regression (Figure S14C) to dissect the major contributing factors. In the text quote above, we report that high abundance is anti-correlated with a good fit to the model (S14D, S14E). Figure 4C shows that immutable PPIs tend to be formed from highly abundant proteins. One possible explanation is that highly abundant proteins saturate the binding sites of their binding partners, breaking from the assumptions of mass action kinetics model. We have now changed the word “limit” to “saturate” on page 7, line 22 to make this concept more explicit.

Taken together, these data suggest that mutable PPIs are subject to more post-translational regulation across environments and that high basal protein abundance may saturate the binding sites of their partners, limiting the ability of gene expression changes to regulate PPIs.

A third possibility is that the dip is simply due to noise. Given the complexity of the possible explanations and our uncertainty about which is more likely, we chose to leave this description out of the main text and focus on the major finding: that PPIs detected in more environments are generally associated with a better fit to the mass action kinetics model.

*) Figure 6: I apologize, but for my taste this is not a final figure 6 for this study. Investigation of different environments increases the PPI network in yeast, yes, yet it is very well known that a saturation is reached after testing of several conditions, different methods and even screening repetition (sampling). It does not represent an important outcome. Move to suppl or remove.

We included Figure 6 to summarize and illustrate the path forward from this study. This is an explicit reference to impactful computational analyses done using earlier generations of data to assess the completeness of single-condition interaction networks (Hart et al., 2006; Sambourg and Thierry-Mieg, 2010). Here, we are extending PPI measurement of millions-scale networks across multiple environments, and are using this figure to extend these concepts to multi-condition screens. We agree that the property of saturation in sampling is well known, but it is surprising that we can quantitatively estimate convergence of this expanded condition-specific PPI set using only 9 conditions. Thus, we agree with Reviewer 1 that these are “remarkable results” and that the “upper limit is profoundly important to modelling cellular network complexity and, if it holds up, could define a general upper limit on organismal complexity.” We think this is an important advance of the paper, and this figure is useful to stimulate discussion and guide future work.

Reviewer #2 (Significance (Required)):

Liu et al. increase the current PPI network in yeast and offer a substantial dataset of novel PPIs seen in specific environments only. This resource can be used to further investigate the biological meaning of the PPI changes. The data set is compared to previous DHFR providing some sort of quality benchmarking. Mutable interactions are characterized well. Clearly a next step could be to start some "orthogonal" validation, i.e. beyond yeast growth under methotrexate treatment.

The reviewer makes a great point that we also discuss on page 9, line 33:

While we used reconstruction of C-terminal-attached mDHFR fragments as a reporter for PPI abundance, similar massively parallel assays could be constructed with different PCA reporters or tagging configurations to validate our observations and overcome false negatives that are specific to our reporter. Indeed, the recent development of “swap tag” libraries, where new markers can be inserted C- or N-terminal to most genes (Weill et al., 2018; Yofe et al., 2016), in combination with our iSeq double barcoder collection (Liu et al., 2019), makes extension of our approach eminently feasible.

Reviewer 3

Reviewer #3 (Evidence, reproducibility and clarity (Required)):

**Summary**

The manuscript "A large accessory protein interactome is rewired across environments" by Liu et al. scales up a previously-described method (PPiSeq) to test a matrix of ~1.6 million protein pairs of direct protein-protein interactions in each of 9 different growth environments.

While the study found a small fraction of immutable PPIs that are relatively stable across environments, the vast majority were 'mutable' across environments. Surprisingly, PPIs detected only in one environment made up more than 60% of the map. In addition to a false positive fraction that can yield apparently-mutable interactions, retest experiments demonstrate (not surprisingly) that environment-specificity can sometimes be attributed to false-negatives. The study authors predict that the whole subnetwork within the space tested will contain 11K true interactions.

Much of environment-specific rewiring seemed to take place in an 'accessory module', which surrounds the core module made of mostly immutable PPIs. A number of interesting network clustering and functional enrichment analyses are performed to characterize the network overall and 'mutable' interactions in particular. The study report other global properties such as expression level, protein abundance and genetic interaction degree that differ between mutable and immutable PPIs. One of the interesting findings was evidence that many environmentally mutable PPI changes are regulated post-translationally. Finally, authors provide a case study about network rewiring related to glucose transport.

**Major issues**

-The results section should more prominently describe the dimensions of the matrix screen, both in terms of the set of protein pairs attempted and the set actually screened (I think this was 1741 x 1113 after filtering?). More importantly, the study should acknowledge in the introduction that this was NOT a random sample of protein pairs, but rather focused on pairs for which interaction had been previously observed in the baseline condition. This major bias has a potentially substantial impact on many of the downstream analyses. For example, any gene which was not expressed under the conditions of the original Tarrasov et al. study on which the screening space was based will not have been tested here. Thus, the study has systematically excluded interactions involving proteins with environment-dependent expression, except where they happened to be expressed in the single Tarrasov et al. environment. Heightened connectivity within the 'core module' may result from this bias, and if Tarrasov et al had screened in hydrogen peroxide (H2O2) instead of SD media, perhaps the network would have exhibited a code module in H2O2 decorated by less-densely connected accessory modules observed in other environments. The paper should clearly indicate which downstream analyses have special caveats in light of this design bias.

We have now added text the matrix dimensions of our study on page 3, line 3:

To generate a large PPiSeq library, all strains from the protein interactome (mDHFR-PCA) collection that were found to contain a protein likely to participate in at least one PPI (1742 X 1130 protein pairs), (Tarassov et al., 2008) were barcoded in duplicate using the double barcoder iSeq collection (Liu et al., 2019), and mated together in a single pool (Figure 1A). Double barcode sequencing revealed that the PPiSeq library contained 1.79 million protein pairs and 6.05 million double barcodes (92.3% and 78.1% of theoretical, respectively, 1741 X 1113 protein pairs), with each protein pair represented by an average of 3.4 unique double barcodes (Figure S1).

We agree with the reviewer that our selection of proteins from a previously identified set can introduce bias in our conclusions. Our research question was focused on how PPIs change across environments, and thus we chose to maximize our power to detect PPI changes by selecting a set of protein pairs that are enriched for PPIs. We have now added a discussion of the potential caveats of this choice to the discussion on page 9, line 4:

Results presented here and elsewhere (Huttlin et al., 2020) suggest that PPIs discovered under a single condition or cell type are a small subset of the full protein interactome emergent from a genome. We sampled nine diverse environments and found approximately 3-fold more interactions than in a single environment. However, the discovery of new PPIs began to saturate, indicating that most condition-specific PPIs can be captured in a limited number of conditions. Testing in many more conditions and with PPI assays orthogonal to PPiSeq will undoubtedly identify new PPIs, however a more important outcome could be the identification of coordinated network changes across conditions. Using a test set of ~1.6 million (of ~18 million) protein pairs across nine environments, we find that specific parts of the protein interactome are relatively stable (core modules) while others frequently change across environments (accessory modules). However, two important caveats of our study must be recognized before extrapolating these results to the entire protein interactome across all environment space. First, we tested for interactions between a biased set of proteins that have previously been found to participate in at least one PPI as measured by mDHFR-PCA under standard growth conditions (Tarassov et al., 2008). Thus, proteins that are not expressed under standard growth conditions are excluded from our study, as are PPIs that are not detectable by mDHFR-PCA or PPiSeq. It is possible that a comprehensive screen using multiple orthogonal PPI assays would alter our observations related to the relative dynamics of different regions of the protein interactome and the features of mutable and immutable PPIs. Second, we tested a limited number of environmental perturbations under similar growth conditions (batch liquid growth). It is possible that more extreme environmental shifts (e.g. growth as a colony, anaerobic growth, pseudohyphal growth) would introduce new accessory modules or alter the mutability of the PPIs we detect. Nevertheless, results presented here provide a new mechanistic view of how the cell changes in response to environmental challenges, building on the previous work that describes coordinated responses in the transcriptome (Brauer et al., 2007; Gasch et al., 2000) and proteome (Breker et al., 2013; Chong et al., 2015).

-Related to the previous issue, a quick look at the proteins tested (if I understood them correctly) showed that they were enriched for genes encoding the elongator holoenzyme complex, DNA-directed RNA polymerase I complex, membrane docking and actin binding proteins, among other functional enrichments. Genes related to DNA damage (endonuclease activity and transposition), were depleted. It was unclear whether the functional enrichment analyses described in the paper reported enrichments relative to what would be expected given the bias inherent to the tested space?

We did two functional enrichment analyses in this study: network density within Gene Ontology terms (related to Figure 2) and gene ontology enrichment of network communities (related to Figure 3). For both analyses, we performed comparisons to proteins included in PPiSeq library. This is described in the Supplementary Materials on page 63, line 35:

To estimate GO term enrichment in our PPI network, we constructed 1000 random networks by replacing each bait or prey protein that was involved in a PPI with a randomly chosen protein from all proteins in our screen. This randomization preserves the degree distribution of the network.

And on page 66, line 38:

The set of proteins used for enrichment comparison are proteins that are involved in at least one PPI as determined by PPiSeq.

-Re: data quality. To the study's great credit, they incorporated positive and random reference sets (PRS and RRS) into the screen. However, the results from this were concerning: Table SM6 shows that assay stringency was set such that between 1 and 3 out of 67 RRS pairs were detected. This specificity would be fine for an assay intended for retest or validate previous hits, where the prior probability of a true interaction is high, but in large-scale screening the prior probability of true interactions that are detectable by PCA is much lower, and a higher specificity is needed to avoid being overwhelmed by false positives. Consider this back of the envelope calculation: Let's say that the prior probability of true interaction is 1% as the authors' suggest (pg 49, section 6.5), and if PCA can optimistically detect 30% of these pairs, then the number of true interactions we might expect to see in an RRS of size 67 is 1% * 30% * 67 = 0.2 . This back of the envelope calculation suggests that a stringency allowing 1 hit in RRS will yield 80% [ (1 - 0.2) / 1 ] false positives, and a stringency allowing 3 hits in RRS will yield 93% [ (3 - 0.2) / 3] false positives. How do the authors reconcile these back of the envelope calculations from their PRS and RRS results with their estimates of precision?

We thank the reviewer for bringing up with this issue. We included positive and random reference sets (PRS:70 protein pairs, RRS:67 protein pairs) to benchmark our PPI calling (Yu et al., 2008). The PRS reference lists PPIs that have been validated by multiple independent studies and is therefore likely to represent true PPIs that are present in some subset of the environments we tested. For the PRS set, we found a rate of detection that is comparable to other studies (PPiSeq in SD: 28%, Y2H and yellow fluorescent protein-PCA: ~20%) (Yu et al., 2008). The RRS reference, developed ten years ago, is randomly chosen protein pairs for which there was no evidence of a PPI in the literature at the time (mostly in standard growth conditions). Given the relatively high rate of false negatives in PPI assays, this set may in fact contain some true PPIs that have yet to be discovered. We could detect PPIs for four RRS protein pairs in our study, when looking across all 9 environments. Three of these (Grs1_Pet10, Rck2_Csh1, and YDR492W_Rpd3) could be detected in multiple environments (9, 7, and 3, respectively), suggesting that their detection was not a statistical or experimental artifact of our bar-seq assay (see table below derived from Table S4). The remaining PPI detected in the RRS, was only detected in SD (standard growth conditions) but with a relatively high fitness (0.35), again suggesting its detection was not a statistical or experimental artifact. While we do acknowledge it is possible that these are indeed false positives due to erroneous interactions of chimeric DHFR-tagged versions of these proteins, the small size of the RRS combined with the fact that some of the protein pairs could be true PPIs, did not give us confidence that this rate (4 of 70) is representative of our true false positive rate. To determine a false positive rate that is less subject to biases stemming from sampling of small numbers, we instead generated 50 new, larger random reference sets, by sampling for each set ~ 60,000 protein pairs without a reported PPI in BioGRID. Using these new reference sets, we found that the putative false positive rate of our assay is generally lower than 0.3% across conditions for each of the 50 reference sets. We therefore used this more statistically robust measure of the false positive rate to estimate positive predictive values (PPV = 62%, TPR = 41% in SD). We detail these statistical methods in Section 6 of the supplementary methods and report all statistical metrics in Table SM6.

PPI

Environment_number

SD

H2O2

Hydroxyurea

Doxorubicin

Forskolin

Raffinose

NaCl

16℃

FK506

Rck2_Csh1

7

0.35

0.35

0

0.20

0.54

0.74

0

0.17

0.59

Grs1_Pet10

9

0.44

0.39

0.34

0.25

0.65

1.19

0.2

0.16

0.95

YDR492W_Rpd3

3

0

0.18

0

0

0

0

0

0.17

0.61

Mrps35_Bub3

1

0.35

0

0

0

0

0

0

0

0

Positive_control

9

1

0.8

0.73

0.62

1.4

2.44

0.4

0.28

1.8

Table. Mean fitness in each environment

-Methods for estimating precision and recall were not sufficiently well described to assess. Precision vs recall plots would be helpful to better understand this tradeoff as score thresholds were evaluated.

We describe in detail our approach to calling PPIs in section 6.6 of the supplementary methods, including Table SM6, and Figures SM3, SM4, SM6, and now Figure SM5. We identified positive PPIs using a dynamic threshold that considers the mean fitness and p-value in each environment. For each dynamic threshold, we estimated the precision and recall based on the reference sets (described supplementary methods in section 6.5). We then chose the threshold with the maximal Matthews correlation coefficient (MCC) to obtain the best balance between precision and recall. We have now added an additional plot (Figure SM5) that shows the precision and recall for the chosen dynamic threshold in each environment.

-Within the tested space, the Tarassov et al map and the current map could each be compared against a common 'bronze standard' (e.g. literature curated interactions), at least for the SD map, to have an idea about how the quality of the current map compares to that of the previous PCA map. Each could also be compared with the most recent large-scale Y2H study (Yu et al).

We thank the reviewer for this suggestion. We have now added a figure panel (Figure S4) that compares PPiSeq in SD (2 replicates) to mDHFR PCA (Tarassov et al., 2008), Y2H (Yu et al., 2008), and our newly constructed ‘bronze standard’ high-confidence positive reference set (PRS, supplementary method section 6.4).

• Experimental validation of the network was done by conventional PCA. However, it should be noted that this is a form of technical replication of the DHFR-based PCA assay, and not a truly independent validation. Other large-scale yeast interaction studies (e.g., Yu et al, Science 2008) have assessed a random subset of observed PPIs using an orthogonal approach, calibrated using PRS and RRS sets examined via the same orthogonal method, from which overall performance of the dataset could be determined.

We appreciate the reviewer’s perspective, since orthogonal validation experiments have been a critical tool to establish assay performance following early Y2H work. We know from careful work done previously that modern orthogonal assays have a low cross validation rate ((Yu et al., 2008) and that they tend to be enriched for PPIs in different cellular compartments (Jensen and Bork, 2008), indicating that high false negative rates are the likely explanation. High false negative rates have been confirmed here and elsewhere using positive reference sets (e.g. Y2H 80%, PCA 80%, PPiSeq 74% using the PRS in (Yu et al., 2008)). Therefore, the expectation is that PPiSeq, as with other assays, will have a low rate of validation using an orthogonal assay -- although we would not know if this rate is 10%, 30% or somewhere in between without performing the work. However, the exact number -- whether it be 10% or 30% -- has no practical impact on the main conclusions of this study (focused on network dynamics rather than network enumeration). Neither does that number speak to the confidence in our PPI calls, since a lower number may simply be due to less overlap in the sets of PPIs that are callable by PPiSeq and another assay. Our method uses bar-seq to extend an established mDHFR-PCA assay (Tarassov et al., 2008). The validations we performed were aimed at confirming that our sequencing, barcode counting, fitness estimation, and PPI calling protocols were not introducing excessive noise relative to mDHFR-PCA that resulted in a high number of PPI miscalls. Confirming this, we do indeed find a high rate of validation by lower throughput PCA (50-90%, Figure 3B). Finally, we do include independent tests of the quality of our data by comparing it to positive and random reference sets from literature curated data. We find that our assay performs extremely well (PPV > 61%, TPR > 41%) relative to other high-throughput assays.

-The Venn diagram in Figure 1G was not very informative in terms of assessing the quality of data. It looks like there is a relatively little overlap between PPIs identified in standard conditions (SD media) in the current study and those of the previous study using a very similar method. Is there any way to know how much of this disagreement can be attributed to each screen being sub-saturation (e.g. by comparing replica screens) and what fraction to systematic assay or environment differences?

We have now added a figure panel (Figure S4) that compares PPiSeq in SD (2 replicates) to mDHFR-PCA (Tarassov et al., 2008), Y2H (Yu et al., 2008), and our newly constructed ‘bronze standard’ high-confidence positive reference sets (PRS, supplementary methods section 6.4). We find that SD replicates have an overlap coefficient of 79% with each other, ~45% with mDHFR-PCA, ~45% the ‘bronze standard’ PRS, and ~13% with Y2H. Overlap coefficients between the SD replicates and mDHFR-PCA are much higher than those found between orthologous methods ((Yu et al., 2008), indicating that these two assays are identifying a similar set of PPIs. We do note that PPiSeq and mDHFR-PCA do screen for PPIs under different growth conditions (batch liquid growth vs. colonies on agar), so some fraction of the disagreement is due to environmental differences. PPIs that overlap between the two PPiSeq SD replicates are more likely to be found in mDHFR-PCA, PRS, and Y2H, indicating that PPIs identified in a single SD replicate are more likely to be false positives. However, we do find (a lower rate of) overlaps between PPIs identified in only one SD replicate and other methods, suggesting that a single PPiSeq replicate is not finding all discoverable PPIs.

-In Figure S5C, the environment-specificity rate of PPIs might be inflated due to the fact that authors only test for the absence of SD hits in other conditions, and the SD condition is the only condition that has been sampled twice during the screening. What would be the environment-specific verification rate if sample hits from each environment were tested in all environments? This seems important, as robustly detecting environment-specific PPIs is one of the key points of the study.

We use PPIs found in the SD environment to determine the environment-specificity because this provides the most conservative (highest) estimate of the number of PPIs found in other environments that were not detectable by our bar-seq assay. To identify PPIs in the SD environment, we pooled fitness estimates across the two replicates (~ 4 fitness estimates per replicate, ~ 8 total). The higher number of replicates results in a reduced rate of false positives (an erroneous fitness estimate has less impact on a PPI call), meaning that we are more confident that PPIs identified in SD are true positives. Because false positives in one environment (but not other environments) are likely to erroneously contribute to the environment-specificity rate, choosing the environment with the lowest rate of false positives (SD) should result in the lowest environment-specificity rate (highest estimate of PPIs found in other environments that were not detectable by our bar-seq assay).

**Minor issues**

-Re: "An interaction between the proteins reconstitutes mDHFR, providing resistance to the drug methotrexate and a growth advantage that is proportional to the PPI abundance" (pg 2). It may be more accurate to say "monotonically related" than "proportional" here. Fig 2 from the cited Freschi et al ref does suggests linearity with colony size over a wide range of inferred complex abundances, but non-linear at low complex abundance. Also note that Freschi measured colony area which is not linear with exponential growth rate nor with cell count.

We agree with the reviewer and have changed “proportional” to “monotonically related” on page 2, line 41.

-Re: "Using putatively positive and negative reference sets, we empirically determined a statistical threshold for each environment with the best balance of precision and recall (positive predictive value (PPV) > 61% in SD media, Methods, section 6)." (pg 3). Should state the recall at this PPV.

We agree with the reviewer and have added the recall (41%) in the main text (line 26, page3).

Using putatively positive and negative reference sets, we empirically determined a statistical threshold for each environment with the best balance of precision and recall (positive predictive value (PPV) > 61% and true positive rate > 41% in SD media, Methods, section 6).

-Authors could discuss the extent to which related methods (e.g. PMID: 28650476, PMID: 27107012, PMID: 29165646, PMID: 30217970) would be potentially suitable for screening in different environments.

We have now added a reference to a barcode-based Y2H study that examined interactions between yeast proteins to the introduction on page 2, line 2:

Yet, little is known about how PPI networks reorganize on a global scale or what drives these changes. One challenge is that commonly-used high-throughput PPI screening technologies are geared toward PPI identification (Gavin et al., 2002; Ito et al., 2001; Tarassov et al., 2008; Uetz et al., 2000; Yu et al., 2008, Yachie et al., 2016), not a quantitative analysis of relative PPI abundance that is necessary to determine if changes in the PPI network are occurring. The murine dihydrofolate reductase (mDHFR)‐based protein-fragment complementation assay (PCA) provides a viable path to characterize PPI abundance changes because it is a sensitive test for PPIs in the native cellular context and at native protein expression levels (Freschi et al., 2013; Remy and Michnick, 1999; Tarassov et al., 2008).

We have excluded the references to other barcode-based Y2H studies that reviewer mentions because they test heterologous proteins within yeast, and the effect of perturbations to yeast on these proteins would be difficult to interpret in the context of our questions. The yeast protein Y2H study, although a wonderful approach and paper, would also not be an appropriate method to examine how PPI networks change across environments because protein fusions are not expressed under their endogenous promoters and must be transported to, in many cases, a non-native compartment (cell nucleus) to be detected. Rather than explicitly discuss the caveats of this particular approach, we have instead chosen to discuss why we use PCA.

• the term "mutable" is certainly appropriate according to the dictionary definition of changeable. The authors may wish to consider though, that in a molecular biology context the term evokes changeability by mutation (a very interesting but distinct topic). Maybe another term (environment-dependent interactions or ePPIs?) would be clearer. Of course this is the authors' call.

We thank the reviewer for this suggestion, and have admittedly struggled with the terminology. For clarity of presentation, we strived to have a single word that describes the property of a PPI that is at the core of this manuscript -- how frequently a PPI is found across environments. However, the most descriptive words come with preloaded meanings in PPI research (e.g. transient, stable, dynamic), as does “mutable” with another research field. We are, quite frankly, open to suggestions from the reviewers or editors for a more appropriate word that does not raise similar objections.

-Some discussion is warranted about the phenomenon that a PPI that is unchanged in abundance could appear to change because of statistical significance thresholds that differ between screens. This would be a difficult question for any such study, and I don't think the authors need to solve it, but just to discuss.

We agree with the reviewer that significance thresholds could be impacting our interpretations and discuss this idea at length on page 4, line 23 of the Results. This section has been modified to include an additional analysis (excluding 16 ℃ data) in response to another reviewer’s comment:

Immutable PPIs were likely to have been previously reported by colony-based mDHFR-PCA or other methods, while the PPIs found in the fewest environments were not. One possible explanation for this observation is that previous PPI assays, which largely tested in standard laboratory growth conditions, and variations thereof, are biased toward identification of the least mutable PPIs. That is, since immutable PPIs are found in nearly all environments, they are more readily observed in just one. However, another possible explanation is that, in our assay, mutable PPIs are more likely to be false positives in environment(s) in which they are identified or false negatives in environments in which they are not identified. To investigate this second possibility, we first asked whether PPIs present in very few environments have lower fitnesses, as this might indicate that they are closer to our limit of detection. We found no such pattern: mean fitnesses were roughly consistent across PPIs found in 1 to 6 conditions, although they were elevated in PPIs found in 7-9 conditions (Figure S6A). To directly test the false-positive rate stemming from pooled growth and barcode sequencing, we validated randomly selected PPIs within each mutability bin by comparing their optical density growth trajectories against controls (Figures 3B). We found that mutable PPIs did indeed have lower validation rates in the environment in which they were identified, yet putative false positives were limited to ~50%, and, within a bin, do not differ between PPIs that have been previously identified and those that have been newly discovered by our assay (Figure S65B). We also note mutable PPIs might be more sensitive to environmental differences between our large pooled PPiSeq assays and clonal 96-well validation assays, indicating that differences in validation rates might be overstated. To test the false-negative rate, we assayed PPIs identified in only SD by PPiSeq across all other environments by optical density growth and found that PPIs can be assigned to additional environments (Figure S6C). However, the number of additional environments in which a PPI was detected was generally low (2.5 on average), and the interaction signal in other environments was generally weaker than in SD (Figure S6D). To better estimate how the number of PPIs changes with PPI mutability, we used these optical density assays to model the validation rate as a function of the mean PPiSeq fitness and the number of environments in which a PPI is detected. This accurate model (Spearman's r =0.98 between predicted and observed, see Methods) provided confidence scores (predicted validation rates) for each PPI (Table S5) and allowed us to adjust the true positive PPI estimate in each mutability bin. Using this more conservative estimate, we still found a preponderance of mutable PPIs (Figure S6E). Finally, we used a pair of more conservative PPI calling procedures that either identified PPIs with a low rate of false positives across all environments (FPR

We later examine major conclusions of our study using more conservative calling procedures, and find that they are consistent. On page 6, line 14:

Both the co-expression and co-localization patterns were also apparent in our higher confidence PPI sets (Figures S7B, and S7C, S8B, S8C ), indicating that they are not caused by different false positive rates between the mutability bins.

And on page 6, line 19:

We binned proteins by their PPI degree, and, within each bin, determined the correlation between the mutability score and another gene feature (Figure 4C and S12A, Table S8) (Costanzo et al., 2016; Finn et al., 2014; Gavin et al., 2006; Holstege et al., 1998; Krogan et al., 2006; Levy and Siegal, 2008; Myers et al., 2006; Newman et al., 2006; Östlund et al., 2010; Rice et al., 2000; Stark et al., 2011; Wapinski et al., 2007; Ward et al., 2004; Yang, 2007; Yu et al., 2008). These correlations were also calculated using our higher confidence PPI sets, confirming results from the full data set (Figures S7D and, S7E, S8D, S8E). We found that mutable hubs (> 15 PPIs) have more genetic interactions, in agreement with predictions from co-expression data (Bertin et al., 2007; Han et al., 2004), and that their deletion tends to cause larger fitness defects.

-More discussion would be helpful about the idea that immutability may to some extent favor interactions that PCA is better able to detect (possibly including membrane proteins?)

We agree with the reviewer and now added a discussion of this potential caveats to the discussion on page 9, line 4:

Results presented here and elsewhere (Huttlin et al., 2020) suggest that PPIs discovered under a single condition or cell type are a small subset of the full protein interactome emergent from a genome. We sampled nine diverse environments and found approximately 3-fold more interactions than in a single environment. However, the discovery of new PPIs began to saturate, indicating that most condition-specific PPIs can be captured in a limited number of conditions. Testing in many more conditions and with PPI assays orthogonal to PPiSeq will undoubtedly identify new PPIs, however a more important outcome could be the identification of coordinated network changes across conditions. Using a test set of ~1.6 million (of ~18 million) protein pairs across nine environments, we find that specific parts of the protein interactome are relatively stable (core modules) while others frequently change across environments (accessory modules). However, two important caveats of our study must be recognized before extrapolating these results to the entire protein interactome across all environment space. First, we tested for interactions between a biased set of proteins that have previously been found to participate in at least one PPI as measured by mDHFR-PCA under standard growth conditions (Tarassov et al., 2008). Thus, proteins that are not expressed under standard growth conditions are excluded from our study, as are PPIs that are not detectable by mDHFR-PCA or PPiSeq. It is possible that a comprehensive screen using multiple orthogonal PPI assays would alter our observations related to the relative dynamics of different regions of the protein interactome and the features of mutable and immutable PPIs. Second, we tested a limited number of environmental perturbations under similar growth conditions (batch liquid growth). It is possible that more extreme environmental shifts (e.g. growth as a colony, anaerobic growth, pseudohyphal growth) would introduce new accessory modules or alter the mutability of the PPIs we detect. Nevertheless, results presented here provide a new mechanistic view of how the cell changes in response to environmental challenges, building on the previous work that describes coordinated responses in the transcriptome (Brauer et al., 2007; Gasch et al., 2000) and proteome (Breker et al., 2013; Chong et al., 2015).

-Re: "As might be expected, we also found that mutable hubs, but not non-hubs, are more likely to participate in multiple protein complexes than less mutable proteins." (pg 6) This is a cool result. To what extent was this result driven by members of one or two complexes? If so, it would worth noting them.

We thank the reviewer for this question. We have now included Figue S13, which shows the number and size of protein complexes that underlie the finding that mutable hubs are more likely to participate in multiple protein complexes. We find that proteins in our screen that participate in multiple complexes are distributed over a wide range of complexes, indicating that this observation is not driven by one or two complexes. On page 6, line 34:

As might be expected, we also found that mutable hubs, but not non-hubs, are more likely to participate in multiple protein complexes than less mutable proteins (Figures S13A-C) (Costanzo et al., 2016).

-Re: "Borrowing a species richness estimator from ecology (Jari Oksanen et al., 2019), we estimate that there are ~10,840 true interactions within our search space across all environments, ~3-fold more than are detected in SD (note difference to Figure 3, which counts observed PPIs)." (pg 8) Should note that this only allows estimation of the number of interactions that are detectable by PCA methods. Previous work (Braun et al, 2019) showed that every known protein interaction assay (including PCA approaches) can only detect a fraction of bona fide interactions.

We agree with the reviewer and have modified the discussion to make this point explicit on page 9, line 4:

Results presented here and elsewhere (Huttlin et al., 2020) suggest that PPIs discovered under a single condition or cell type are a small subset of the full protein interactome emergent from a genome. We sampled nine diverse environments and found approximately 3-fold more interactions than in a single environment. However, the discovery of new PPIs began to saturate, indicating that most condition-specific PPIs can be captured in a limited number of conditions. Testing in many more conditions and with PPI assays orthogonal to PPiSeq will undoubtedly identify new PPIs, however a more important outcome could be the identification of coordinated network changes across conditions.

We continue in this paragraph to discuss the implications:

Using a test set of ~1.6 million (of ~18 million) protein pairs across nine environments, we find that specific parts of the protein interactome are relatively stable (core modules) while others frequently change across environments (accessory modules). However, two important caveats of our study must be recognized before extrapolating these results to the entire protein interactome across all environment space. First, we tested for interactions between a biased set of proteins that have previously been found to participate in at least one PPI as measured by mDHFR-PCA under standard growth conditions (Tarassov et al., 2008). Thus, proteins that are not expressed under standard growth conditions are excluded from our study, as are PPIs that are not detectable by mDHFR-PCA or PPiSeq. It is possible that a comprehensive screen using multiple orthogonal PPI assays would alter our observations related to the relative dynamics of different regions of the protein interactome and the features of mutable and immutable PPIs.

-Re: "This analysis shows that the number of PPIs present across all environments is much larger than the number observed in a single condition, but that it is feasible to discover most of these new PPIs by sampling a limited number of conditions." (pg 8). The main point is surely correct, but it is worth noting that extrapolation to the number of true interactions depends on the nine chosen environments being representative of all environments. The situation could change under more extreme, e.g., anaerobic, conditions.

We agree with the reviewer and make this point explicit, continuing from the paragraph quoted above on page 9, line 22:

Second, we tested a limited number of environmental perturbations under similar growth conditions (batch liquid growth). It is possible that more extreme environmental shifts (e.g. growth as a colony, anaerobic growth, pseudohyphal growth) would introduce new accessory modules or alter the mutability of the PPIs we detect. Nevertheless, results presented here provide a new mechanistic view of how the cell changes in response to environmental challenges, building on the previous work that describes coordinated responses in the transcriptome (Brauer et al., 2007; Gasch et al., 2000) and proteome (Breker et al., 2013; Chong et al., 2015).

-It stands to reason that proteins expressed in all conditions will yield less mutable interactions, if 'mutability' is primarily due to expression change at the transcriptional level. They should at least discuss that measuring mRNA levels could resolve questions about this. Could use Waern et al G3 2013 data (H202, SD, HU, NaCl) to predict the dynamic interactome purely by node removal, and see how conclusions would change

We agree with the reviewer that mRNA abundance could potentially be used as a proxy for protein abundance and have added this point on page 10, line 28:

Here we use homodimer abundance as a proxy for protein abundance. However, genome-wide mRNA abundance measures could be used as a proxy for protein abundance or protein abundance could be measured directly in the same pool (Levy et al., 2014) by, for example, attaching a full length mDHFR to each gene using “swap tag” libraries mentioned above (Weill et al., 2018; Yofe et al., 2016).

However, using mRNA abundance as a proxy for protein abundance in this study has several important caveats that would make interpretation difficult. First, mRNA and protein abundance correlate, but not perfectly (R2 = 0.45) (Lahtvee et al., 2017), and our findings suggest that post-translational regulation may be important to driving PPI changes. Second, mRNA abundance measures are for a single time point, while our PPI measures coarse grain over a growth cycle (lag, exponential growth, diauxic shift, saturation). Although we may be able to take multiple mRNA measures across the cycle, time delays between changes in mRNA and protein levels, combined with the fact that we do not know when a PPI is occurring or most prominent over the cycle, would pose a significant challenge to making any claims that PPI changes are driven by changes in protein abundance. We instead chose to focus on a subset of proteins (homodimers) where abundance measures can be coarse grained in the same way as PPI measures. In the above quote, we point to a potential method by which this can be done for all proteins. We also point to how a continuous culturing design could be used to better determine how protein (or mRNA proxy) abundance impacts PPI abundance on page 10, line 6:

Finally, our assays were performed across cycles of batch growth meaning that changes in PPI abundance across a growth cycle (e.g. lag, exponential growth, saturation) are coarse grained into one measurement. While this method potentially increases our chance of discovering a diverse set of PPIs, it might have an unpredictable impact on the relationship between fitness and PPI abundance (Li et al., 2018). To overcome these issues, strains containing natural or synthetic PPIs with known abundances and intracellular localizations could be spiked into cell pools to calibrate the relationship between fitness and PPI abundance in each environment. In addition, continuous culturing systems may be useful for refining precision of growth-based assays such as ours.

-The analysis showing that many interactions are likely due to post-translational modifications is very interesting, but caveats should be discussed. Where heterodimers do not fit the expression-level dependence model, some cases of non-fitting may simply be due to measurement error or non-linearity in the relationship between abundance and fitness.

We show the measurement error in Figures 1, S2, S3. While we agree with the reviewer that measurement error is a general caveat for all results reported, we do not feel that it is necessary to point to that fact in this particular case, which uses a logistic regression to report that PPI mutability was the best predictor of fit to the expression-level dependence model. We discuss the non-linearity caveat on page 9, line 41:

Our assay detected subtle fitness differences across environments (Fig S5B and S5C), which we used as a rough estimate for changes in relative PPI abundance. While it would be tempting to use fitness as a direct readout of absolute PPI abundance within a cell, non-linearities between fitness and PPI abundance may be common and PPI dependent. For example, the relative contribution of a reconstructed mDHFR molecule to fitness might diminish at high PPI abundances (saturation effects) and fitness differences between PPIs may be caused, in part, by differences in how accessible a reconstructed mDHFR molecule is to substrate. In addition, environmental shifts might impact cell growth rate, initiate a stress response, or result in other unpredictable cell effects that impact the selective pressure of methotrexate and thereby fitness (Figure S2 and S3).

-Line numbers would have been helpful to note more specific minor comments

We are sorry for this inconvenience. We have added line numbers in our revised manuscript.

-Sequence data should be shared via the Short-Read Archive.

The raw sequencing data have been uploaded to the Short-Read Archive. We mentioned it in the Data and Software Availability section on page 68, line 41.

Raw barcode sequencing data are available from the NIH Sequence Read Archive as accession PRJNA630095 (https://trace.ncbi.nlm.nih.gov/Traces/study/?acc=SRP259652).

Reviewer #3 (Significance (Required)):

Knowledge of protein-protein interactions (PPIs) provides a key window on biological mechanism, and unbiased screens have informed global principles underlying cellular organization. Several genome-scale screens for direct (binary) interactions between yeast proteins have been carried out, and while each has provided a wealth of new hypotheses, each has been sub-saturation. Therefore, even given multiple genome-scale screens our knowledge of yeast interactions remains incomplete. Different assays are better suited to find different interactions, and it is now clear that every assay evaluated thus far is only capable (even in a saturated screen) of detecting a minority of true interactions. More relevant to the current study, no binary interaction screen has been carried out at the scale of millions of protein pairs outside of a single 'baseline' condition.

The study by Liu et al is notable from a technology perspective in that it is one of several recombinant-barcode approaches have been developed to multiplex pairwise combinations of two barcoded libraries. Although other methods have been demonstrated at the scale of 1M protein pairs, this is the first study using such a technology at the scale of >1M pairs across multiple environments.

A limitation is that this study is not genome-scale, and the search space is biased towards proteins for which interactions were previously observed in a particular environment. This is perhaps understandable, as it made the study more tractable, but this does add caveats to many of the conclusions drawn. These would be acceptable if clearly described and discussed. There were also questions about data quality and assessment that would need to be addressed.

Assuming issues can be addressed, this is a timely study on an important topic, and will be of broad interest given the importance of protein interactions and the status of S. cerevisiae as a key testbed for systems biology.

*Reviewers' expertise:* Interaction assays, next-generation sequencing, computational genomics. Less able to assess evolutionary biology aspects.

References

Brauer, M.J., Huttenhower, C., Airoldi, E.M., Rosenstein, R., Matese, J.C., Gresham, D., Boer, V.M., Troyanskaya, O.G., and Botstein, D. (2007). Coordination of Growth Rate, Cell Cycle, Stress Response, and Metabolic Activity in Yeast. Mol. Biol. Cell 19, 352–367.

Breker, M., Gymrek, M., and Schuldiner, M. (2013). A novel single-cell screening platform reveals proteome plasticity during yeast stress responses. J. Cell Biol. 200, 839–850.

Chong, Y.T., Koh, J.L.Y., Friesen, H., Kaluarachchi Duffy, S., Cox, M.J., Moses, A., Moffat, J., Boone, C., and Andrews, B.J. (2015). Yeast Proteome Dynamics from Single Cell Imaging and Automated Analysis. Cell 161, 1413–1424.

Gasch, A.P., Spellman, P.T., Kao, C.M., Carmel-Harel, O., Eisen, M.B., Storz, G., Botstein, D., and Brown, P.O. (2000). Genomic Expression Programs in the Response of Yeast Cells to Environmental Changes. Mol. Biol. Cell 11, 4241–4257.

Hart, G.T., Ramani, A.K., and Marcotte, E.M. (2006). How complete are current yeast and human protein-interaction networks? Genome Biol. 7, 120.

Hilliker, A., Gao, Z., Jankowsky, E., and Parker, R. (2011). The DEAD-box protein Ded1 modulates translation by the formation and resolution of an eIF4F-mRNA complex. Mol. Cell 43, 962–972.

Isasa, M., Suñer, C., Díaz, M., Puig-Sàrries, P., Zuin, A., Bichmann, A., Gygi, S.P., Rebollo, E., and Crosas, B. (2015). Cold Temperature Induces the Reprogramming of Proteolytic Pathways in Yeast. J. Biol. Chem. jbc.M115.698662.

Jensen, L.J., and Bork, P. (2008). Not Comparable, But Complementary. Science 322, 56–57.

Lahtvee, P.-J., Sánchez, B.J., Smialowska, A., Kasvandik, S., Elsemman, I.E., Gatto, F., and Nielsen, J. (2017). Absolute Quantification of Protein and mRNA Abundances Demonstrate Variability in Gene-Specific Translation Efficiency in Yeast. Cell Syst. 4, 495-504.e5.

Obayashi, T., Kagaya, Y., Aoki, Y., Tadaka, S., and Kinoshita, K. (2019). COXPRESdb v7: a gene coexpression database for 11 animal species supported by 23 coexpression platforms for technical evaluation and evolutionary inference. Nucleic Acids Res. 47, D55–D62.

Sambourg, L., and Thierry-Mieg, N. (2010). New insights into protein-protein interaction data lead to increased estimates of the S. cerevisiae interactome size. BMC Bioinformatics 11, 605.

Tarassov, K., Messier, V., Landry, C.R., Radinovic, S., Molina, M.M.S., Shames, I., Malitskaya, Y., Vogel, J., Bussey, H., and Michnick, S.W. (2008). An in Vivo Map of the Yeast Protein Interactome. Science 320, 1465–1470.

Yu, H., Braun, P., Yıldırım, M.A., Lemmens, I., Venkatesan, K., Sahalie, J., Hirozane-Kishikawa, T., Gebreab, F., Li, N., Simonis, N., et al. (2008). High-Quality Binary Protein Interaction Map of the Yeast Interactome Network. Science 322, 104–110.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #3

Evidence, reproducibility and clarity

Summary

The manuscript "A large accessory protein interactome is rewired across environments" by Liu et al. scales up a previously-described method (PPiSeq) to test a matrix of ~1.6 million protein pairs of direct protein-protein interactions in each of 9 different growth environments.

While the study found a small fraction of immutable PPIs that are relatively stable across environments, the vast majority were 'mutable' across environments. Surprisingly, PPIs detected only in one environment made up more than 60% of the map. In addition to a false positive fraction that can yield apparently-mutable interactions, retest experiments demonstrate (not surprisingly) that environment-specificity can sometimes be attributed to false-negatives. The study authors predict that the whole subnetwork within the space tested will contain 11K true interactions.

Much of environment-specific rewiring seemed to take place in an 'accessory module', which surrounds the core module made of mostly immutable PPIs. A number of interesting network clustering and functional enrichment analyses are performed to characterize the network overall and 'mutable' interactions in particular. The study report other global properties such as expression level, protein abundance and genetic interaction degree that differ between mutable and immutable PPIs. One of the interesting findings was evidence that many environmentally mutable PPI changes are regulated post-translationally. Finally, authors provide a case study about network rewiring related to glucose transport.

Major issues

-The results section should more prominently describe the dimensions of the matrix screen, both in terms of the set of protein pairs attempted and the set actually screened (I think this was 1741 x 1113 after filtering?). More importantly, the study should acknowledge in the introduction that this was NOT a random sample of protein pairs, but rather focused on pairs for which interaction had been previously observed in the baseline condition. This major bias has a potentially substantial impact on many of the downstream analyses. For example, any gene which was not expressed under the conditions of the original Tarrasov et al. study on which the screening space was based will not have been tested here. Thus, the study has systematically excluded interactions involving proteins with environment-dependent expression, except where they happened to be expressed in the single Tarrasov et al. environment. Heightened connectivity within the 'core module' may result from this bias, and if Tarrasov et al had screened in hydrogen peroxide (H2O2) instead of SD media, perhaps the network would have exhibited a code module in H2O2 decorated by less-densely connected accessory modules observed in other environments. The paper should clearly indicate which downstream analyses have special caveats in light of this design bias.

-Related to the previous issue, a quick look at the proteins tested (if I understood them correctly) showed that they were enriched for genes encoding the elongator holoenzyme complex, DNA-directed RNA polymerase I complex, membrane docking and actin binding proteins, among other functional enrichments. Genes related to DNA damage (endonuclease activity and transposition), were depleted. It was unclear whether the functional enrichment analyses described in the paper reported enrichments relative to what would be expected given the bias inherent to the tested space?

-Re: data quality. To the study's great credit, they incorporated positive and random reference sets (PRS and RRS) into the screen. However, the results from this were concerning: Table SM6 shows that assay stringency was set such that between 1 and 3 out of 67 RRS pairs were detected. This specificity would be fine for an assay intended for retest or validate previous hits, where the prior probability of a true interaction is high, but in large-scale screening the prior probability of true interactions that are detectable by PCA is much lower, and a higher specificity is needed to avoid being overwhelmed by false positives. Consider this back of the envelope calculation: Let's say that the prior probability of true interaction is 1% as the authors' suggest (pg 49, section 6.5), and if PCA can optimistically detect 30% of these pairs, then the number of true interactions we might expect to see in an RRS of size 67 is 1% 30% 67 = 0.2 . This back of the envelope calculation suggests that a stringency allowing 1 hit in RRS will yield 80% [ (1 - 0.2) / 1 ] false positives, and a stringency allowing 3 hits in RRS will yield 93% [ (3 - 0.2) / 3] false positives. How do the authors reconcile these back of the envelope calculations from their PRS and RRS results with their estimates of precision?

-Methods for estimating precision and recall were not sufficiently well described to assess. Precision vs recall plots would be helpful to better understand this tradeoff as score thresholds were evaluated.

-Within the tested space, the Tarassov et al map and the current map could each be compared against a common 'bronze standard' (e.g. literature curated interactions), at least for the SD map, to have an idea about how the quality of the current map compares to that of the previous PCA map. Each could also be compared with the most recent large-scale Y2H study (Yu et al).

• Experimental validation of the network was done by conventional PCA. However, it should be noted that this is a form of technical replication of the DHFR-based PCA assay, and not a truly independent validation. Other large-scale yeast interaction studies (e.g., Yu et al, Science 2008) have assessed a random subset of observed PPIs using an orthogonal approach, calibrated using PRS and RRS sets examined via the same orthogonal method, from which overall performance of the dataset could be determined.

-The Venn diagram in Figure 1G was not very informative in terms of assessing the quality of data. It looks like there is a relatively little overlap between PPIs identified in standard conditions (SD media) in the current study and those of the previous study using a very similar method. Is there any way to know how much of this disagreement can be attributed to each screen being sub-saturation (e.g. by comparing replica screens) and what fraction to systematic assay or environment differences?

-In Figure S5C, the environment-specificity rate of PPIs might be inflated due to the fact that authors only test for the absence of SD hits in other conditions, and the SD condition is the only condition that has been sampled twice during the screening. What would be the environment-specific verification rate if sample hits from each environment were tested in all environments? This seems important, as robustly detecting environment-specific PPIs is one of the key points of the study.

Minor issues

-Re: "An interaction between the proteins reconstitutes mDHFR, providing resistance to the drug methotrexate and a growth advantage that is proportional to the PPI abundance" (pg 2). It may be more accurate to say "monotonically related" than "proportional" here. Fig 2 from the cited Freschi et al ref does suggests linearity with colony size over a wide range of inferred complex abundances, but non-linear at low complex abundance. Also note that Freschi measured colony area which is not linear with exponential growth rate nor with cell count. -Re: "Using putatively positive and negative reference sets, we empirically determined astatistical threshold for each environment with the best balance of precision and recall (positive predictive value (PPV) > 61% in SD media, Methods, section 6)." (pg 3). Should state the recall at this PPV.

-Authors could discuss the extent to which related methods (e.g. PMID: 28650476, PMID: 27107012, PMID: 29165646, PMID: 30217970) would be potentially suitable for screening in different environments.

• the term "mutable" is certainly appropriate according to the dictionary definition of changeable. The authors may wish to consider though, that in a molecular biology context the term evokes changeability by mutation (a very interesting but distinct topic). Maybe another term (environment-dependent interactions or ePPIs?) would be clearer. Of course this is the authors' call.

-Some discussion is warranted about the phenomenon that a PPI that is unchanged in abundance could appear to change because of statistical significance thresholds that differ between screens. This would be a difficult question for any such study, and I don't think the authors need to solve it, but just to discuss.

-More discussion would be helpful about the idea that immutability may to some extent favor interactions that PCA is better able to detect (possibly including membrane proteins?)

-Re: "As might be expected, we also found that mutable hubs, but not non-hubs, are more likely to participate in multiple protein complexes than less mutable proteins." (pg 6) This is a cool result. To what extent was this result driven by members of one or two complexes? If so, it would worth noting them.

-Re: "Borrowing a species richness estimator from ecology (Jari Oksanen et al., 2019), we estimate that there are ~10,840 true interactions within our search space across all environments, ~3-fold more than are detected in SD (note difference to Figure 3, which counts observed PPIs)." (pg 8) Should note that this only allows estimation of the number of interactions that are detectable by PCA methods. Previous work (Braun et al, 2019) showed that every known protein interaction assay (including PCA approaches) can only detect a fraction of bona fide interactions.

-Re: "This analysis shows that the number of PPIs present across all environments is much larger than the number observed in a single condition, but that it is feasible to discover most of these new PPIs by sampling a limited number of conditions." (pg 8). The main point is surely correct, but it is worth noting that extrapolation to the number of true interactions depends on the nine chosen environments being representative of all environments. The situation could change under more extreme, e.g., anaerobic, conditions.

-It stands to reason that proteins expressed in all conditions will yield less mutable interactions, if 'mutability' is primarily due to expression change at the transcriptional level. They should at least discuss that measuring mRNA levels could resolve questions about this. Could use Waern et al G3 2013 data (H202, SD, HU, NaCl) to predict the dynamic interactome purely by node removal, and see how conclusions would change

-The analysis showing that many interactions are likely due to post-translational modifications is very interesting, but caveats should be discussed. Where heterodimers do not fit the expression-level dependence model, some cases of non-fitting may simply be due to measurement error or non-linearity in the relationship between abundance and fitness.

-Line numbers would have been helpful to note more specific minor comments

-Sequence data should be shared via the Short-Read Archive.

Significance

Knowledge of protein-protein interactions (PPIs) provides a key window on biological mechanism, and unbiased screens have informed global principles underlying cellular organization. Several genome-scale screens for direct (binary) interactions between yeast proteins have been carried out, and while each has provided a wealth of new hypotheses, each has been sub-saturation. Therefore, even given multiple genome-scale screens our knowledge of yeast interactions remains incomplete. Different assays are better suited to find different interactions, and it is now clear that every assay evaluated thus far is only capable (even in a saturated screen) of detecting a minority of true interactions. More relevant to the current study, no binary interaction screen has been carried out at the scale of millions of protein pairs outside of a single 'baseline' condition.

The study by Liu et al is notable from a technology perspective in that it is one of several recombinant-barcode approaches have been developed to multiplex pairwise combinations of two barcoded libraries. Although other methods have been demonstrated at the scale of 1M protein pairs, this is the first study using such a technology at the scale of >1M pairs across multiple environments.

A limitation is that this study is not genome-scale, and the search space is biased towards proteins for which interactions were previously observed in a particular environment. This is perhaps understandable, as it made the study more tractable, but this does add caveats to many of the conclusions drawn. These would be acceptable if clearly described and discussed. There were also questions about data quality and assessment that would need to be addressed.

Assuming issues can be addressed, this is a timely study on an important topic, and will be of broad interest given the importance of protein interactions and the status of S. cerevisiae as a key testbed for systems biology.

Reviewers' expertise: Interaction assays, next-generation sequencing, computational genomics. Less able to assess evolutionary biology aspects.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

Report on Liu et al. "A large accessory protein interactome is rewired across environments" Liu et al. use a mDHFR-based, pooled barcode sequencing / competitive growth / mild methotrexate selection method to investigate changes of PPI abundance of 1.6 million protein pairs across different 9 growth conditions. Because most PPI screens aim to identify novel PPIs in standard growth conditions, the currently known yeast PPI network may be incomplete. The key concept is to define immutable" PPIs that are found in all conditions and "mutable" PPIs that are present in only some conditions. The assay identified 13764 PPIs across the 9 conditions, using optimized fitness cut offs. Steady PPI i.e. across all environments, were identified in membrane compartments and cell division. Processes associated with the chromosome, transcription, protein translation, RNA processing and ribosome regulation were found to change between conditions. Mutable PPIs are form modules as topological analyses reveals.

Interestingly, a correlation on intrinsic disorder and PPI mutability was found and postulated as more flexible in the conformational context, while at the same time they are formed by less abundant proteins.

I appreciate the trick to use homodimerization as an abundance proxy to predict interaction between heterodimers (of proteins that homodimerize). This "mass-action kinetics model" explains the strength of 230 out of 1212 tested heterodimers.

A validation experiment of the glucose transporter network was performed and 90 "randomly chosen" PPIs that were present in the SD environment were tested in NaCl (osmotic stress) and Raffinose (low glucose) conditions through recording optical density growth trajectories. Hxt5 PPIs stayed similar in the tested conditions, supported by the current knowledge that Hxt5 is highly expressed in stationary phase and under salt stress. In Raffinose, Hxt7, previously reported to increase the mRNA expression, lost most PPIs indicating that other factors might influence Hxt7 PPIs.

Points for consideration:

*) A clear definition of mutable and immutable is missing, or could not be found e.g. at page 4 second paragraph.

*) Approximately half of the PPIs have been identified in one environment. Many of those mutable PPIs were detected in the 16{degree sign}C condition. Is there an explanation for the predominance of this specific environment? What are these PPIs about?

*) 50 % overall retest validation rate is fair and reflects a value comparable to other large-scale approaches. However what is the actual variation, e.g. between mutable PPIs and immutable or between condition. e.g. at 16{degree sign}C.

*) What is the R correlation cutoff for PPIs explained in the mass equilibrium model vs. not explained?

*) 90 "randomly chosen" PPIs for validation. It needs to be demonstrated that these interaction are a random subset otherwise is could also mean cherry picked interactions ...

*) Figure 4 provides interesting correlations with the goal to reveal properties of mutable and less mutable PPIs. PPIs detected in the PPIseq screen can partially be correlated to co-expression (4A) as well as co-localization. Does it make sense to correlate the co-expression across number of conditions? Are the expression correlation condition specific. In this graph it could be that expression correlation stems from condition 1 and 2 and the interaction takes place in 4 and 5 still leading to the same conclusion ... Is the picture of the co-expression correlation similar when you simply look at individual environments like in S4A?

*) Figure 4C: Interesting, how dependent are the various categories?

*) Figure 4 F: When binned in the number of environments in which the PPI was found, the distribution peaks at 6 environments and decreases with higher and lower number of environments. The description /explanation in the text clearly says something else.

*) Figure 6: I apologize, but for my taste this is not a final figure 6 for this study. Investigation of different environments increases the PPI network in yeast, yes, yet it is very well known that a saturation is reached after testing of several conditions, different methods and even screening repetition (sampling). It does not represent an important outcome. Move to suppl or remove.

Significance

Liu et al. increase the current PPI network in yeast and offer a substantial dataset of novel PPIs seen in specific environments only. This resource can be used to further investigate the biological meaning of the PPI changes. The data set is compared to previous DHFR providing some sort of quality benchmarking. Mutable interactions are characterized well. Clearly a next step could be to start some "orthogonal" validation, i.e. beyond yeast growth under methotrexate treatment.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

The manuscript is clearly written and the figures appropriate and informative. Some descriptions of data analyses are a little dense but reflect what would appear long hard efforts on the part of the authors to identify and control for possible sources of misinterpretation due to sensitivities of parameters in their fitness model. The authors efforts to retest interactions under non-competition conditions allay fears of most concerns that I would have. One problem though that I could not see explicitly addressed was that of potential effects of interactions between methotrexate and the other conditions and how this is controlled for. Specifically, I could be argued that the fact that a particular PPI is observed under a specific condition could have more to do with a synthetic effect of treatment of cells with a drug plus methotrexate. Is this controlled for and how? I raise this because in a chemical genetic screen for fitness it was shown that methotrexate is particularly promiscuous for drug-drug interactions (Hillenmeyer ME ,et al. Science 2008). I tried to think of how this works but couldn't come up with anything immediately. I'd appreciate if the authors would take a crack at resolving this issue. Otherwise I have no further concerns about the manuscript.

Significance

Lui et al expand on previous work from the Levy group to explore a massive in vivo protein interactome in the yeast S. cerevisiae. They achieve this by performing screens cross 9 growth conditions, which, with replication, results in a total of 44 million measurements. Interpreting their results based on a fitness model for pooled growth under methotrexate selection, they make the key observation that there is a vastly expanded pool of protein-protein interactions (PPI) that are found under only one or two condition compared to a more limited set of PPI that are found under a broad set of conditions (mutable versus immutable interactors). The authors show that this dichotomy suggests some important features of proteins and their PPIs that raise important questions about functionality and evolution of PPIs. Among these are that mutable PPIs are enriched for cross-compartmental, high disorder and higher rates of evolution and subcellular localization of proteins to chromatin, suggesting roles in gene regulation that are associated with cellular responses to new conditions. At the same time these interactions are not enriched for changes in abundance. These results are in contrast to those of immutable PPIs, which seem to form a core background noise, more determined by changes in abundance than what the authors interpret must be post-translational processes that may drive, for instance, changes in subcellular localization resulting in appearance of PPIs under specific conditions. The authors are also able to address a couple of key issues about protein interactomes, including the controversial Party-date Hub hypothesis of Vidal, in which they could now affirm support for this hypothesis based on their results and notably negative correlation of PPIs to protein abundance for mutable PPIs. Finally, they also addressed the problem of predicting the upper limit of PPIs in yeast, showing the remarkable results that it may be no more than about 2 times the number of proteins expressed by yeast. Such an upper limit is profoundly important to modelling cellular network complexity and, if it holds up, could define a general upper limit on organismal complexity.

This manuscript is a very important contribution to understanding dynamics of molecular networks in living cells and should be published with high priority.

Reviewer #3:

In the manuscript "Kinetics of CDK4/6 inhibition determine different temporal locations of the restriction point" Kim et al., investigate the regulation of the Rb/E2F by CDK4/6 and CDK2 and how mitogen and stress signalling differently regulate kinetics of CDK4/6 inhibition before irreversible cell-cycle entry. Research into restriction point regulation recently experienced a revival due to advanced single cell approaches and the presented study falls into this category as well. Utilizing CDK4, CDK2 and APC/C activity reporters the authors investigate the position of the restriction point in response to external stimuli. Their main conclusions are that i) CDK4/6 activity alone initiates RB hyperphosphorylation and E2F activation, ii) that the CDK2-Rb feedback is the key signalling network controlling the restriction point, iii) that kinetics of CDK4/6 inhibition in response to mitogen removal and stress signalling explain previous observation in asynchronously cycling cells showing different locations of the restriction point and iv), that CDK2 activity alone without other mechanisms in S phase determines the temporal location of the restriction point with respect to CDK4/6 inhibition and S-phase entry.

I have major concerns with presented work regarding the design of the study in relation to question asked, the one-sided introduction and discussion and imprecise wording of restriction point events, the tendency to overstating/generalize conclusion of their findings, the novelty of their results in relation to old restriction point studies using serum starvation and release regimes and the more recent studies from the Meyer, Spencer and Bakal labs focusing on asynchronously growing cells, and the fact that their results and interpretations are completely at odds with the recent Dowdy and Dyson studies, which are not mentioned at all in either the introduction or discussion. Finally, to my opinion the authors have not yet provided the experimental proof for one of their major claims, namely that CDK4/6 activity alone initiates RB hyperphosphorylation and E2F activation. My detailed criticisms are listed in the major and minor points below.

Major points:

1) The authors give the impression in the introduction that they will focus on probing the possibility of different temporal locations of the restriction point depending on the external stimuli (p3, l60ff). However, they only use mitogen withdrawal and NCS-induced DNA damage as "stimuli" but then claim that "we demonstrate that different extracellular environments cause different kinetics of CDK4/6 inhibition (p10, l96ff)". Certainly, these two treatments (in addition to direct CDK4 and CDK2) are not sufficient for such a general statement and in the context of their writing, NCS-induced DNA damage is rather a cell-intrinsic and not an external stimulus/condition as claimed. Similarly, the authors derive from their NCS experiments general and overarching statements about restriction point regulation in response to stress. In fact, CDK4/6 is a target of several integrated stress pathways, e.g. UPR/PERK, which regulate the levels of cyclin D on the translational level (e.g. Brewer at al., PNAS 1999) and are independent on p21. The authors also claim to investigate whether other mechanisms in S phase are required to initiate the restriction point. To me this is another example of unclear wording and unfulfilled expectations as the only factor analysed is the APC/C, which is inactivated at the entry of S phase. From the introduction, discussion and the mentioned literature it is unclear to me why the authors expect that a mechanism in S phase, hence after commitment to proliferation, would feed back on the restriction point during G1 phase of the same cell.

2) Introduction and discussion are one-sided and completely omit recent findings of the Spencer lab (Min et al., PLOS Biology 2019) in relation to stress and most importantly the Dowdy (Narasimha et al. eLife 2014) and Dyson studies (Sandias et al., Mol Cell 2019), which are both at odds with a major claim of the presented work (see below).

3) The authors claim throughout the paper that CDK4/6 is sufficient to hyperphosphorylate Rb based on nuclei that can be stained by antibodies specific to 4 Rb phospho sites and in situ extraction experiments that claim to dissociate hyperphopshorylated Rb from the DNA. This claim cannot be made as their results are completely consistent with the alternative, namely that multiple Rb molecules within the same cell (nucleus) are mono-phosphorylated at the analysed sites, or at either of the 14 possible sites. This would be in agreement with the Dowdy and Dyson studies (Fig. 1 & Fig. 2). For the situ extraction experiments investigating nuclear-bound Rb there is no real data shown. Fig. 1J basically shows the segmentation strategy the authors employ and indicate that same cells have less nuclear Rb staining. There are no controls, (e.g. before after extraction) and proof that the assay works in their hands - e.g. treating the cells with CDK4/6 inhibitors and CDK2 inhibitors before the assay. The authors show in Fig 1. that E2F1 is already induced hours before mitosis, yet cells only progress much later into S. However, it is as likely that mono phosphorylation of RB is sufficient to initiate E2F1 transcription, this could be easily tested using the published mutant cell lines expressing Rb variants with only one phosphosite.

4) The authors claim that "However, previous studies showed that CDK2 inhibitors caused a loss of Rb phosphorylation and induced quiescence (Narasimha et al., 2014; Spencer et al., 2013)" (p5, l60). Reading these papers again it appears to me that this is a wrong statement/interpretation. Narasimha et al, show in Figure 3 that only CDK4 inhibition but not CDK2 inhibition results in a complete loss of Rb phosphorylation. The latter treatment resulted in RB mono phosphorylation (Fig 3i) and did not induce quiescence as the authors claim here. Instead, such cells remained in G1 phase and did not make the transition into G0. Also, the claim the Spencer et al., results are due to off-target effects of CDK2 inhibitors appears flawed, because the authors only detect those after a prolonged time (more than 9 hours), whereas Spencer et al, monitored the effect of such inhibitors on cells immediately after application. Hence, in my opinion this part, the corresponding data (Fig. S3), and interpretations should be removed.

5) In asynchronously treated cells CDK2 appears to be activated early after mitosis (Spencer et al., 2013), whereas in their experimental setup CDK2 and CDK4 activation are only assessed after mitogen starvation and release. I imagine from the timing that in asynchronously growing cells also CDK2 activity will be tightly coordinated with E2F transcription (Fig 1D) - hence, a main foundation for their study may depend on the experimental setup used and thus this should clearly be discussed. I also wonder how their results on the requirement of CDK4 for RB phosphorylation would be without the synchronization step.

Reviewer #2:

In this manuscript, Kim et al. investigate the events required for irreversible commitment to division by immortalized mammalian cells in culture. They do so by tracking single, live cells by video-microscopy using an assortment of fluorescent biosensors (augmented by fixed-cell immunofluorescence), and perturbing cell-cycle progression with cyclin-dependent kinase (CDK) inhibitors, DNA-damaging agents, or mitogen withdrawal. This is a complicated problem, which has resisted a comprehensive solution since the initial attempts to define a commitment or "Restriction" point (R point) in mammalian cells over 40 years ago. This study yields some intriguing results, and generally adds significant molecular detail to previous work on this problem by the PI and former colleagues in the Meyer lab. There are serious flaws, however, both conceptual and technical. Some of them are inherent in the approach, for example, the overreliance on small-molecule inhibitors that are not as selective as one would hope, and on live-cell biosensors that are neither as sensitive nor as specific (for individual CDKs) as they would need to be to justify some of the stronger mechanistic conclusions. Then there is the central take-home message (I think), which is based on the observation that mitogen withdrawal or DNA damaging agents have different windows of sensitivity during G1, such that the former needs to be applied earlier than the latter in order to prevent cell cycle entry. This leads to re-interpretation of the R point as a moving target, occurring at different points in the cell cycle depending on which perturbations cells encounter as they take the necessary steps to commence DNA replication. This makes little biological sense to me. The R point concept seems to lose much or all of its usefulness if it is not understood as a cellular state in which the irreversible commitment to division has been made, irrespective of what might befall an individual cell that has passed it. I think a more reasonable interpretation, of a superficially (at least) similar phenomenon, was put forth by Skotheim and colleagues, who found that the threshold level of CDK1/2 activity that predicted subsequent R-point passage was higher when all mitogens were withdrawn than when a single mitogenic signaling pathway was ablated, e.g. with a MEK inhibitor (Schwarz et al., 2018, ref 22). In this take, the R point per se is not mutable, but the strength of an antimitogenic signal can determine how quickly cells can put on the brakes before reaching it. I would urge the authors to avoid this phrasing, and aim for a bit more clarity in describing an admittedly complicated set of data. Below I Iist my major, specific concerns:

1) Probably the biggest problem for the current study emerged from a paper by Rubin and colleagues (Guiley et al., 2019, ref. 26), which showed, quite convincingly, that the "CDK4/6 inhibitors" Palbociclib, ribociclib and abemaciclib-used throughout the current study-almost certainly do not work in cells by direct inhibition of CDK4/6, but rather by binding CDK monomers and redistributing CDK inhibitor (CKI) proteins, notably p21, to CDK2. To be fair, this is a very recent paper, which, to their credit, the authors cite and try to address. But they address it only obliquely and, I'm afraid, inadequately; although they show that effects of Palbociclib et al. are partially independent of p21 (Fig. 3B,D), this doesn't rule out contributions by other CKIs such as p27 or p57, all of which could potentially be redistributing to CDK2 complexes if CDK4 complex assembly is impaired (Guiley et al. did not test this possibility and only evaluated CDK2-CKI binding in wild-type cells). Nor do they address the strong implication of Guiley et al., that loss of CDK4/6 activity is not the mechanism by which these compounds act. This is a hugely important point; the entire study (and several previous ones from the Meyer lab) depends on the ability to inhibit CDK4/6 or CDK1/2 with different inhibitors and distinguish the effects on various cellular phenotypes and biosensor signals, which is now in considerable doubt.

2) More generally, the study relies on small-molecule inhibitors of different CDKs that are at best only modestly selective for their intended targets. The problem with using Palbociclib in this way has been discussed above, and is a recent development, but it should be noted that major "off targets" for the "CDK4/6 inhibitors" include transcriptional CDKs such as CDK9, which are also potently inhibited by "CDK1/2" inhibitors such as roscovitine (and others). One could make the case that these drugs are hitting different targets, because they have different effects on different biosensors, but the specificity of those bioesensors was established in part by using the inhibitors, so the case that their effects occur solely or primarily through their intended targets is in the end circular.

3) The "CDK4/6 biosensor" has in fact been shown in a previous paper by the PI to detect CDK1/2 activity in addition to CDK4/6; there was residual signal after Palbociclib treatment in cells with high CDK2 activity. Setting aside the aforementioned problem of Palbociclib specificity, if I understand correctly, to "correct" for this lack of specificity, the authors subtract 35% to generate the signal they attribute to CDK4/6. This seems to assume that the relative contributions to this fluorescence by CDK4/6 and CDK1/2 will be in a fixed proportion, or am I missing something?

4) In previous papers from the Meyer lab, Rb hyperphosphorylation was "inferred" from concurrently increased immunofluorescence signals, in fixed cells, from a panel of phosphoRb-specific antibodies (Chung et al., 2019, ref. 18). I have my problems even with inferring stoichiometry from these types of measurements, but in this manuscript the language is even stronger: IF signals are flatly described (and interpreted) as "markers" of Rb hyperphosphorylation. This too is a major issue; a prevailing model, supported by biochemical data that are by necessity ensemble measurements, holds that CDK4/6 is primarily responsible for Rb monophosphorylation, whereas hyperphosphorylation coincides with and is dependent on activation of CDK2 (Narasimha et al., 2014, ref. 28). Although for the moment the larger concern-that anything the authors have done to inactivate CDK4/6 is likely to be indirectly inhibiting CDK2-renders this more technical point somewhat moot, conclusions-or even inferences-about hyper- versus mono-phosphorylated forms of Rb should be based on actual measurements of stoichiometry.

Reviewer #1:

This manuscript reports a series of studies probing the relative roles of CDK4/6 and CDK2 in inactivation of the retinoblastoma (Rb) protein and in determining the restriction point, which marks the commitment of a cell to S phase and subsequent cell division. The work builds off the recent development of live-cell reporters for CDK activity, and it primarily uses relationships between those signals to conclude that while CDK4/6 activity is sufficient for Rb inactivation and E2F activation, CDK2 activation determines passage through the restriction point. Though well-studied over the last two decades, the questions addressed here related to the G1-S cell cycle transition are still not sufficiently answered, and they are important to understanding fundamental cell biology and cancer biology. The use of single-cell imaging and application of a CDK4/6 sensor is an exciting approach to study Rb inactivation and the restriction point, and many of the experiments here are well designed. In addition, aspects of the authors' approach, including the use of multiple cell lines, make the observations robust. However, there are several significant concerns. While most of the concerns could be addressed through more analysis of experiments already performed and rewriting, more experiments are likely necessary to address the first point.

Significant concerns:

1) The study relies on interpretation of the adjusted "CDK4/6 sensor" signal as a specific reporter of CDK4/6 activity. Because this assumption of specificity is so critical, the authors should briefly review the evidence supporting it and better explain the accounting of other activities that may result in sensor phosphorylation. It is problematic that one of the conclusions in the discussion is that the "the CDK4/6 sensor may report other activities which can be targeted by CDK4/6 inhibitors," particularly as these inhibitors were used to validate specificity in ref 19 (Yang et al 2020). It is also important that mounting evidence here (for example Fig. 3A) and elsewhere show that CDK4/6 inhibitors such as palbociclib may also impact CDK2 activity.

The conclusion that CDK4/6 activity is sufficient for Rb phosphorylation is in large part based on the correlation of the CDK4/6 sensor response with measurements of Rb phosphorylation using phosphospecific antibodies (Fig. 1). However, the sensor was constructed using an Rb-based docking site, which is expected to give the sensor properties of Rb as a substrate. With the perspective that the sensor reports on Rb-like substrate phosphorylation, rather than CDK4/6 activity per se, the reported correlation is inevitable and cannot be used to support the conclusion. The sensor phosphorylation of course correlates with Rb phosphorylation, as it was designed precisely to behave that way. Some other independent measurement of CDK4/6 activity, for example activity toward a different substrate or measurement of the abundance of CDK4/6-CycD complexes is needed to avoid this circular reasoning.

The plausible interpretation that the sensor merely reports on the threshold of any CDK activity sufficient to phosphorylate Rb would also make other conclusions less novel, for example, that sensor phosphorylation correlates with E2F activation. If one replaces "CDK4/6 activity sensor" with "Rb-phosphorylation sensor," few conclusions from the first two figures are compelling. For this reason, it is critical that the authors further detect and quantify CDK4/6 activity in some independent way. Otherwise, the data as presented are not sufficient to support several of the main conclusions of the paper as stated, and the conclusions that likely could be fairly drawn lack novelty.

2) Experiments similar to those presented in Fig. S3 were published before in ref 19 (Yang et al 2020). In the previous paper, the effects of the drugs were used to validate the specificity of the CDK sensors. Here, the sensors are invoked to characterize the specificity and effects of the drugs. Again, this circular logic undercuts the validity of the conclusions. It is similarly plausible that either both the sensor and drugs have specificity or both lack specificity; the outcome of the set of experiments would be the same. These experiments are not as critical to the overall study, and the authors may consider removing this part of the manuscript, if further experiments are not possible.

3) These conclusions following presentation of the data in Fig. 3 are not well substantiated: "the temporal location of the restriction point with respect to stress and CDK4/6 inhibition is closely coupled with engagement of feedback pathways" and "our data demonstrates that inhibition of CDK4/6 activity before threshold-based activation of CDK2-Rb feedback causes cell-cycle exit." The experiments only measure CDK activity and not engagement of CDK2-Rb feedback, so there must be some assumption about the correspondence of a threshold of CDK2 activity to activation of the feedback. How is it known that feedback is engaged? This question persists throughout the study. The authors should more carefully define what CDK2-Rb feedback is and how its initiation is detected experimentally. Is it Rb hyperphosphorylation, mRNA expression of an E2F target gene, or protein levels of CycE? One of these should perhaps be measured in Fig. 3 to state the conclusion in terms of CDK2-Rb feedback rather than a CDK2 activity threshold. Alternatively, if further experimentation is not possible, the conclusions should be carefully stated in terms of CDK2 activity rather than invoking the idea of "CDK2-Rb feedback."

4) A number of recent studies have similarly used single cell reporter and other analyses to probe the relative roles of CDK4/6, CDK2, and APC-Cdh1 in the restriction point (including Rb inactivation) and S phase entry (e.g. refs 2-4, 16-19, 22, 26, 28). The authors need to better explain how the observations here fit into the paradigms being developed and disputed through this body of work. Several of the conclusions stated here have been reached before. For example, the order that CDK4/6, CDK2, and Apc-CDK1 activity changing en route to S phase, that CDK4/6 is sufficient for Rb hyperphosphorylation, and that CDK2 activity is a threshold for the restriction point have all been described and supported in some of the referenced papers and contradicted in other references. Yet, similar conclusions are stated here as if they are novel. This study still is important in that the use of a CDK4/6 activity reporter may be a powerful approach to investigating these questions. But the subtleties of how this work is distinct and/or confirming needs to be made more clear for the reader to understand its significance.

A related concern is that the results and conclusions described in Fig. 5 are not particularly surprising or novel. There is extensive literature characterizing high CDK2 activity, including its upregulation through CycE expression, as a mechanism of acquired tumor cell resistance to CDK4/6 inhibitors (see for example references reviewed in PMID: 32289274). Other published studies have examined the effects of ectopic CycE expression on accelerating G1-S, including in the absence of CycD activity or even the absence of Rb (see for example PMID: 8108147, PMID: 7601350, PMID: 1388095, PMID: 14645251, and PMID: 9192874). The authors should place their results in the context of these previous results and emphasize what insights are novel here.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Summary:

Although the reviewers all agreed that you are addressing an important problem, and that a single cell approach is likely to yield important insights, they had serious concerns over the specificity of the probes and reagents you are using, and the degree of advance that your study represents over the current literature. With regard to the latter, the referees strongly suggested that a more comprehensive literature review is needed to put your results in context.

Reviewer #3:

This work reports the results from a set of predominantly coarse-grained (CG) simulation of phospholipid interactions with the yeast fippase Drs2p:cdc50p in the outward facing state. Using the popular MARTINI force field, these simulations reveal multiple putative binding sites of lipid molecules and support a likelihood of the "credit-card" model of lipid transport. The authors have also analyzed the possible preference of different lipids at these sites. While these are interesting observations, they are severely limited by the CG nature of the model and lack strong corroborating support from either atomistic simulations or experiment.

1) While this work includes a substantial set of atomistic simulations, they do not appear to provide much useful information or provide much support to any of the central conclusions of the work.

2) Instead, virtually all key conclusions are based on MARTINI simulations. While this is indeed an outstanding CG model that has been successfully applied to an increasing number of problems (particularly self-assembly), it is highly questionable that MARTINI is appropriate for predicting binding sites. To the best of my knowledge, this model has not been demonstrated to be reliable for such purposes. It requires great caution and careful validation to establish and support the predicted binding sites.

Are there any collaborating experimental evidence to support these sites? The authors only made minimal efforts to validate this critical prediction, largely by noting that EM densities suggest multiple binding sites. This needs to be investigated thoroughly, such as by direct comparison of these locations.

Can one at least test if lipids can stably occupy those sites using atomistic simulations?

3) Membrane thinning is only observed in CG but not atomistic simulations; this is alarming, as membrane thinning should be able to be captured in atomistic simulations within a few 100 ns. This has been demonstrated clearly in several published simulations of scramblases (e.g., Bethel and Grabe PNAS 2016, among others). This calls the quality of the MARTINI simulations into question for capturing detailed properties of this flippase complex.

4) Free energy analysis was done with the MARTINI model, which greatly reduces its usefulness. As stated above, the MARTINI model is really not appropriate for such detailed free energy analysis of these putative binding sites.

Reviewer #2:

This manuscript "Computational Studies of Substrate Transport and Specificity in a Phospholipid Flippase" presents multiscale simulations to understand the details of a yeast flippase in lipid binding, membrane deformation, and protein hydration. Overall, an examination of the Drs2p-Cdc50p complex was carried out with 500-ns-long all-atom and 100-us-long coarse-grained simulations in different membrane models (pure PS, PE, PC and mixtures). Free-energy simulations were also employed to compare lipid binding free energies. A major finding is the identification of the anionic PS lipid binding to a water-filled substrate binding groove. However, I find the work lacks clarity, novelty, and biological insight.

1) My primary concern is that three different phospholipids were selected in this work: PS, PE, and PC, but only the PS lipid is anionic. First of all, it is quite obvious that the PS lipid is preferred in this limited set, due to the formal charge difference. The higher affinity of anionic lipids to transmembrane proteins has been extensively studied (too many to list, but here are a few recent examples PNAS 2020 117, 7803-7813; Structure, 2019, 27, 392-403.e3; Sci Rep. 2018, 8, 4456; Sci Rep. 2016, 6, 29502)

Second, according to prior experiments (Appl Environ Microbiol. 2014, 80, 2966-2972), the major phospholipids in yeast are phosphatidylcholine (PC), phosphatidylethanolamine (PE), phosphatidylinositol (PI), phosphatidylserine (PS), and phosphatidic acid (PA), with minor amounts of cytidinediphosphate-diacylglycerol (CDP-DAG). There are also glycosphingolipids, ergosterol, and proteins. None of the membrane models simulated in this work is an approximate to the realistic yeast cellular membrane. Because the lipid composition has important physiological impacts, I found a lack of justification of why key anionic lipids (like PI and PA) and ergosterol were not included.

2) In addition, it was claimed "As our atomistic simulations were limited to 0.5-1.0 𝜇𝑠 due to their high computational cost". I cannot agree with the authors, given the system size of ~340,000 atoms. It is not rare to see microsecond or multiple-microsecond all-atom simulations (of this size or larger) in current studies of membrane proteins. Further, longer simulations might be more likely to sample lipid exchange and competition within the groove, as well as relevant protein conformational changes (which cannot be captured in CG simulations).

3) Moreover, while I found the results presented in Fig. 5 quite interesting, the related paragraphs seem to lack the in-depth analysis and clarity to support "a 'credit-card'-like model" First, it is not clear to me how this lipid in Fig. 5 was selected. How did this lipid look in the outer leaflet vs. in the deep state of the groove? Second, there is no analysis of the event at ~21-23 us when the lipid starts to transition. What was the trigger of the event? Were there any specific interactions? Last but not the least, as the authors said "X-ray diffraction and Cryo-EM experiments on ATP8A1 and ATP11C show density for PL head groups", it is possible to compare the simulation results (lipid density) to the experimental density. It would greatly strengthen this paper if such analysis is included.

4) The "water-filled cavities" results overall may need more clarification and probably even experimental support. First of all, how were the AA simulations compared with CG simulations, in terms of the cavities? Given the ENM constraints, there were little conformational changes of the cavities (of the protein) in response to PS moving the groove. There might be some induced fit effect and the cavities may adopt different shapes when such effect is fully considered in the AA modeling. Second, is there any experimental evidence to support this observation from MD simulations? For example, mutation of the key residue Ile508, suggested by the authors to separate the two cavities.

Reviewer #1:

This is an outstanding paper. MD simulations at two resolutions are employed to provide convincing predictions regarding the lipid-binding to flippases in terms of mechanism of binding and specificity. The topic is of fundamental biology interest and the results provide deeper insights than are possible with experimental structural biology methods alone.

The simulations are certainly state-of-the-art in terms of methodology and are well ahead of the field in terms of simulation length.

The paper is written and presented clearly. The results are explained in detail and have the necessary statistical treatment to provide confidence in them. The discussion is based on the results and contextualised appropriately- there is no claim that cannot be supported by the results.

A number of important observations are reported including those concerning lipid tail orientations, water-filled cavities, and lipid binding affinity.

Overall the authors should be commended on a thorough computational study.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Summary:

In general, all reviewers agreed that the problem is of importance and the simulations have been well conceived and thoroughly conducted at the coarse-grained level. However, there is the concern that while MARTINI is able to capture many collective properties of lipid membranes, it is not sufficiently reliable for dissecting molecular recognition processes governed by subtle free energy differences, especially when electrostatics (difference in charge state) and protein conformational rearrangements are expected to play major roles. In absence of direct supporting experimental verification, this concern undermines the central conclusions of the study.

Reviewer #2:

Here the authors expand on their prior modeling of origin activity (Platel 2015) in xenopus extracts. Their prior work, while successful in some estimates, failed to reproduce the tight distribution of interorigin ("eye to eye") distances. Here the authors generate a series of nested models (MM1-MM4) of increasing complexity to describe the distribution and frequency of observed initiation events in an unperturbed S-phase. Not surprisingly, the fit improves with the increasing complexity of each model. The authors then built an even more complex model based on prior published work to generate in silico data for which they tested their MM4 model. I admit to being a little lost at this point as to why the authors were using simulated data to assess their model and identify key parameters. Finally, the authors compare prior published experimental data from an unperturbed S-phase and one with an abrogated intra s-phase checkpoint (chk1 inhibition) and three parameters stood out J (rate limiting factor), 𝜃 (fraction of the genome with high origin initiation activity), and Pout (probability of remaining origins to fire) which suggests that Chk1 limits the probability of origin activation outside of the regions of the genome with high origin activation efficiency and modulates the activity of the rate limiting factor (J). These conclusions are consistent with prior observations in other systems. In summary, the authors apply elegant modeling approaches to describe xenopus in vitro replication dynamics and the effects of Chk1 inhibition, but the work fails to reveal new principles of eukaryotic origin regulation and replication dynamics. The most powerful modeling approaches are those that reveal a new or unexpected mode of regulation (or parameter) that can then be experimentally tested.

Additional points:

This was a very specialized manuscript and would be difficult to read for general biologists. The terms/parameters were only defined in a table and many of the figures would not be parsable by a broad audience.

Figure 1. Sets off the challenge at hand -- that the previous model couldn't account for the distribution of "eye to eye" distances; but this is never assessed in similar format with the newer model. I assume this is captured in the appendix 1 figures, but was uncles if this was eye length or gap length.

Reviewer #1:

The current work by Goldar and colleagues uses numerical simulations to model the spatiotemporal DNA replication program in an in vitro Xenopus DNA replication system. By comparing modeled data and experimental DNA combing data generated during unperturbed S-phase replication and upon intra-S checkpoint inhibition (which the authors published previously), the authors find that DNA replication in Xenopus extracts can be modeled by segmenting the genome in regions of high and low probability of origin activation, with the intra-S-phase checkpoint regulating origins with low but not high firing probability. Recapitulating the kinetics of global and local S-phase replication under different conditions through mathematical simulations represents an important contribution to the field. However, one concern I have pertains to the generality of the model, as the authors did not explore whether the model can accurately simulate replication under other conditions (e.g., checkpoint activation).

Major comments:

1) In figure 1a and 1c, the authors show data that were previously published by the authors. Yet, the displayed values in 1a and 1c differ from those displayed in Figure 10 of Platel et al, 2015. This discrepancy should be explained.

2) The authors test whether their model can simulate replication when S-phase is perturbed by Chk1 inhibition, but not under opposite conditions of Chk1 activation. This important analysis should be included.

3) Although the MM4 model developed by the authors is in agreement with previously published experimental DNA combing data measured in the Xenopus system, it is unclear whether it can also accurately predict the replication program in other systems. Comparing simulated data with experimental data from another metazoan system would serve as an important additional validation of the authors' model.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Summary:

This paper uses numerical simulations to model DNA replication dynamics in an in vitro Xenopus DNA replication system, both in unperturbed conditions and upon intra-S-checkpoint inhibition. The current work extends previous studies by the authors that recapitulated some but not all features of the replication program. The new model is superior as it can model both the frequency and the distribution of observed initiation events. Although the reviewers found the work in principle interesting and well executed, they have identified limitations of the study, both with respect to model validation and the extent to which the findings represent new biological insights into origin regulation and replication dynamics.

Reviewer #3:

The manuscript consists of a nice confirmation study and further validate the PET-index (Stender et al., 2016) as well as the EEG classification (Sitt et al., 2014; Engemann et al., 2018). The introduction is clear, the method is clear as well, results are well described and the discussion is concise and precise. The clinical impact of the study would greatly benefit from the availability of the PET index code on a platform such as GiHub to allow all centers with a PET scanner to use this index and provide a better diagnosis for DoC patients.

Major comments:

1) Regarding the behavioural assessment (i.e., number of CRS-r), is there a minimum of CRS-R performed? This should be stated in the method. Based on the table, some patients received only 2 CRS-R, while the rate of misdiagnosis with 2 CRS-R is as high as 26% for UWS patients (Wannez et al 2017). This is an important limitation. The number of CRS-R should be included in supplementary material, in a table providing all individual data (see next comment). Some UWS patients with a high index (>3.07) may have received only 2 CRS-R, which would have an important impact on the validity of the results.

2) Were the EEG and PET acquisitions done on the same day? Which CRS-R was taken? The best or the one done on the day of the PET-scan? As the study compared the validity of the PET index and EEG classification, the fact that the two exams may not have been performed on the same day, and knowing that DoC patients fluctuate a lot, is a clear limitation and should be clearly acknowledged and discussed in the limitation section.

3) For the PET voxel-based analysis, the significance threshold was set at p<0.005 uncorrected. Why did the authors use this threshold? It seems a bit arbitrary or convenient for the authors. It would be interesting and more transparent to present the corrected results too (e.g. in Supplementary Material).

4) It is crucial to add a limitation section. The study has many limitations (not 5 CRS-R, heterogeneity of the population, PET-EEG and behavioural assessments not done on the same day, while comparing their respective accuracy, PET isn't easily available which limits the clinical impact of the present study, etc.).

5) Individual data should be added (initial diagnostic, gender, age, etiology, best crsr, number of crs-r, index, eeg classification, outcome etc.) in supplementary material. The excel file provided is terrible to read. Could the authors at least tabulate the columns and provide a legend? In any case, I strongly suggest adding a table in supplementary material with the individual data.

6) The references should be carefully checked. Some of them are in the text but not in the list, and some of them are in the list but not referenced in the text. The reference "Wannez et al 2018" does not seem to be the appropriate one.

Reviewer #2:

The study is a prospective cohort study evaluating both PET and EEG regarding the diagnosis and prognosis in VS/MCS patients. Thus, it represents a logical advancement from Stender et al 2016 and Bekinschtein et al 2009 towards clinical evaluation of the retrospectively established methods. To my knowledge there is no other prospective data set examining these methods. The authors plausibly show that the methods are capable of improving the diagnosis. The included number of subjects of 57 sufficient given the high effort necessary for this multimodal assessment. The results regarding the prognosis using the combined methods though significant certainly needs a targeted study with a fixed design before use in clinical practice.

In the following I would propose some minor improvements:

1) I would move the first two sentences of paragraph 2 (31 ff) to the discussion. They introduce a new concept that is not necessary to understand your major points in the introduction. I would stick to your story a) DoCs are important clinically because we don't know who is aware of what (a potential nightmare for the patient) b) PET seems to be really robust at telling but is actually not evaluated prospectively c) EEG might also help but in the past was not very robust in prospective studies d) Maybe a combination of both helps too. Second problem is what to tell relatives how the prognosis is. Actually, we know only little mainly as a side finding of Stender 2014 and 2016. In my opinion the latter points are told nicely.

2) I would remove the regional differences as a discriminator. I have two concerns about them. The first is technical in nature: you applied an anatomical atlas to potentially deformed brains after injury. The paper does not convince me that this worked sufficiently because it is not described in detail and from my experience it is very difficult to segment this type of brains. The second concern is that the result does not really support your main findings and is thus dispensable. I would recommend to focus on the main points: PET is really robust in your sample (even the cut-off from Stender et al 2016 is pretty much reproducible) and EEG is also pretty robust (although sensitivity drops from 94% in-sample to 58% out-of-sample). Also, the combination works well. I think these are the main findings that have potential to make it into clinical routine.

3) I would also focus the discussion on two points. First, the clinical impact of your findings. I think if you would deliver a fully automatized tool to reproduce your data pipeline people world-wide would be willing to use PET for their VS patients. As a second point you should also discuss the concept of the cortically mediated state and how your work is related to that.

In conclusion, I think the study presented is technically and conceptually strong and provides a valuable step towards clinical routine application of the demonstrated methods. The language is also enjoyable to read.

Reviewer #1:

The authors intended to test whether FDG-PET pseudo-quantitative metabolic index of the best preserved hemisphere (MIBH), as well as EEG-based classification (the auditory local-global paradigm)
, and combination of the two methods, were accurate complementary markers to discriminate VS from MCS. Their results showed that an MIBH was accurate 
and robust procedure across sites to diagnose MCS, which can even be improved in combination with EEG-based classification allowing the detection of covert cognition and 6- month responsiveness recovery in unresponsive patients. Additionally, their results indicated 
that the behavioral diagnosis of MCS does not correspond to an elusive and generic conscious 
state, but rather to a CMS that reveals the preservation of metabolic activity in specialized 
cortical networks. These results provide valuable information for the clinic use of MIBH and local-global paradigm in the future. There are several issues which should be mentioned:

1) As the authors put the "methods and materials" before the results, they should describe the patients’ information in a clear way in the "methods and materials", not in the results.

2) The authors may need to provide more information about the EEG design. For example, what is the exact experiment design, ITI, stimulus number, and so on. More importantly, the authors need to provide the exact number of the left epochs after the rejection of the bad epochs for each patient.

3) The authors indicated that the auditory local-global paradigm could be used to detect the consciousness. Furthermore, they also mentioned the cognitive-motor dissociation patients (CMD). If they can discuss the distinction of local-global paradigm and motor imagery tasks (or other tasks) which were used to detect the CMD, this will be very helpful.

4) The results about accuracy of MIBH to discriminate between MCS and VS are not strongly related to results about how MCS did not correspond to an elusive and generic conscious 
state. The latter is more interesting. I would suggest the authors put them into two independent papers.

5) Please provide more information about the "MCS items are associated with metabolic specific of subscales", such as how many patients in the analysis for each subscale?

6) Please clarify why there are results about Motor CRS-R subscale: one in Fig.5 and the other one in supplementary Figure e-1.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Summary:

All reviewers in general agree that your study is solid with clear-cut results. In particular, the multimodal assessments of both PET and EEG, regarding the diagnosis and prognosis in VS/MCS patients, were carefully executed. As such, the results provide valuable information for future prognosis research guiding clinic use, e.g., a targeted study with a fixed design.

Reviewer #3:

1) As I state below the paper is carefully done (with a few minor issues) using a difficult and sophisticated biophysical technique, FCS to assess the changes in beta catenin diffusion within the cell following Wnt signaling. So it passes the test on being an original piece of work executed well. However what has been learned is quite limited. A few interactions, such as the slow diffusion in the cytoplasm can be interpreted several ways. It is very helpful to have concentrations in the nucleus and cytoplasm for beta catenin for future modeling. They could have tried to use single cross correlation with labeled APC or axin or the proteasome to derive more important information about the path through the destruction sequence. But that may be too hard to ask for at this stage. They could have combined their measurements with appropriate mutants or knockouts. I come down close to the line, high on the importance of the problem and the methods and execution; lower on the current take home lesson.

2) The support for the somewhat limited conclusions is strong as it is.

3) There are some technical issues. There is some concern with the FCS data itself. Figure 5F and 5G are of some concern. The curve doesn't drop to 1 at long correlation time (>100ms) and there are big fluctuations in the region of short correlation times (<0.1 ms). This could be due to the very long time course (120s) used in the experiment. Have the authors tried to image the same spot multiple times in short intervals (etc 10s), or try to analyze 10s sub-trace of the original long trace to see if the conclusions hold? This type of error could influence the calculation of the diffusion coefficient of complexes of CNNTB1. They also affect the quantification of concentration. In line 352-353 the authors mentioned the nuclear concentration of CNNTB1 increases 2.1 fold based on FCS measurement, which is smaller than the fluorescent intensity change. Is this the result of errors such as this.

For confocal imaging analysis, the description was not clear as to whether there is background subtraction during the intensity quantification. If there is, the authors should mention it in the method explicitly. If not, the background could decrease the fold change estimation.

In the model description line 877, equation (6), k7x6 should be k7x5

Line 901 equation (15), there is no unit for the binding affinity

Normally, a fraction of the fluorescent protein is not bright; the authors may not have a tool to measure the dark component but they should mention how it may affect the quantification in the discussion.

Reviewer #2:

The manuscript by S.M.A. de Man et al. presents a study on the cellular response to Wnt activation and on the intracellular kinetics of beta catenin (CTNNB1). The authors have developed cell lines expressing GFP reporters of CTNNB1 using CRISPR CAS9. They present different convincing controls on the specificity of the reporter and decided to analyze the temporal behavior of the best reacting clone. Then, they investigate the temporal evolution of fluorescent signals in the cell cytoplasm and nucleus upon Wnt signaling activation. They quantify the kinetics of the relocalization of CTNNB1 from the cytoplasm to the nucleus upon different strength of activation of the Wnt signaling and GSK3 inhibition. Using FCS, they identify that a dual diffusion model fits better the experimental data than a classical single diffusion model, suggesting the presence of complexes of different sizes. They measure the diffusion parameters and concentrations of the complexes in the nucleus and in the cytoplasm. Using a dynamical model, the authors reveal that, to recapitulate the experimental observations, the regulation of CTNNB1 upon Wnt signaling has to be controlled at three levels, the destruction complex, the nuclear transport and the binding affinity to the chromatin.

Overall, the study is solid, presenting novel information on the kinetics of CTNNB1 during Wnt signaling. The results are consistent with the classical view on the regulation of beta catenin during Wnt signaling. I have few comments essentially on the methodology.

Specific comments:

-The authors have designed a new cell line allowing for tracing the kinetics of beta catenin over time following Wnt signaling activation. They follow the relative changes in concentration in the nucleus and cytoplasm upon activation of Wnt signaling. Normalized changes render difficult to evaluate if the difference in the increase in the cytoplasm and the nucleus is due to a higher increase in the nucleus or simply due the absence of beta catenin in the nucleus at the onset of the process therefore enhancing the quantification. A non-normalized plot showing the increase in grey levels in the nucleus and cytoplasm should be added to complement the quantification and identify the differences between nuclear and cytoplasmic beta catenin. It would also help the reader to compare with the results of concentrations extracted from the FCS.

-The response in figure 4 upon Wnt signaling activation and GSK3 inhibition are different (with the absence of a plateau in the case of GSK3 inhibition). The explanation of this difference is unclear as it is. I would suggest the authors to detail a bit more their thoughts on the reason for the difference. Could this simply be that Wnt activation clusters just a subset of GSK3 at the membrane and that inhibition can reach a higher level of depletion of GSK3 in the cytoplasm?

-How GSK3 inhibition treatment affects the FCS measurements, particularly concentrations and different complexes compositions? The differences with Wnt3 activation could provide additional information on the nature of the identified complexes.

-The dynamical model presented in the paper shows a non-monotonous change in the concentration of beta catenin in the cytoplasm after activation. This seems to be due to the kinetics of nuclear transport and does not seem to be present in the experimental observations. Can the authors comment on this point? Is there a way by modulating parameters associated to transport to suppress this discrepancy?

-Finally, the model is consistent with the experimental observations but the authors did not check with any type of perturbation how the model would compare with the experiments. For instance, how does the model compare with experiments in the case of GSK3 inhibition, or when nuclear transport is affected. Adding a perturbation case would significantly strengthen the connection between model and experiment and the message of the manuscript.

-labels of the figure 4 and respective movies are inverted

-The figure 1 only presents the classical model and no new concept/data. The figure 1 and figure 2 should be merged to my point of view.

-The labels in the table 1 Wnt (ON -OFF) are inverted.

Reviewer #1:

CTNNB1 is a core component of canonical Wnt signalling that is frequently mutated in cancers. A constitutively active destruction complex (degradosome) binds and phosphorylates CTNNB1 earmarking it for proteasomal degradation, this complex is inactivated upon Wnt3a/GSK3β inhibition leading to CTNNB1 stabilisation and nuclear translocation. The authors have successfully employed CRISPR mediated endogenous tagging of CTNNB1 and determined its cellular concentration and diffusion dynamics in HAP1 cells, in both the cytoplasm and nucleus by live-cell imaging and analysis. They provide the relative subcellular CTNNB1 concentration for the nucleus and cytoplasm, like previous studies in other cell lines (Tan et al., 2012) and in Xenopus (Lee et al., 2003). In addition their results suggest CTNNB1 resides in slow moving complexes that persist upon Wnt but become slightly more mobile, these results are intriguing but raise several unanswered questions, such as whether these complexes represent the destruction complex (cytoplasm) or enhanceosome (nucleus). The work has been completed to a high standard but I have several concerns listed below.

1) The authors acknowledge significant cell-cell heterogeneity. This is particularly noticeable in Fig.4A upon Wnt3a and CHIR99021 treatment. Fig.4B suggests all cells are analysed regardless of heterogeneity and the only exclusion criteria mentioned in the methodology is cells with a cytoplasm of less than 10pixels. Fig.4C/D does not seem to reflect the variation observed in Fig.4A? What is the spread pre-normalisation before and after treatment? How is the relative increase in nuclear/cytoplasmic intensity affected by cell size? Nuclear and cytoplasmic area? This may affect the relative fold increase and the cytoplasmic area seems highly variable at the confluence of cells shown.

2) Using point FCS the authors determined two diffusion speeds corresponding to monomer and complexed CTNNB1 in both the nucleus and cytoplasm. A modest increase in cytoplasmic diffusion speed of complexed CTNNB1 was observed after Wnt3a (0.461μm2/s-1) but far from the speed of the monomer (14.9μm2/s-1) suggesting it remains complexed upon Wnt3a. In addition the fraction of complexed CTNNB1 (~40%) remains largely unaltered. Is the same true under CHIR299021 treatment? Point FCS samples a very small area of the cell cytoplasm/nucleus and therefore gives a small representation of the subcellular pool (which is likely heterogeneous), only a single point appears to have been analysed per-cell and within the 21 cells analysed clear outliers can be observed (Fig.6A/B), this has not been adequately discussed. What is the variation in diffusion measured at different points within a single cell? Some discussion has been made as to these complexes reflecting the destruction complex/proteasome or the enhanceosome but this really needs to be tested in order to make any conclusions about these observations. Especially as cytoplasmic complexes are maintained under Wnt conditions, this would challenge the notion that CTNNB1 disassociates from the destruction complex upon Wnt. Ideally endogenous tagging of other destruction complex components with a different fluorophore would be done to address this, if these complexes do represent the destruction complex and remain bound after Wnt this would have significant implications for our understanding of complex inactivation and greatly enhance the manuscript.

3) The N&B analysis averages out monomeric and complexed CTNNB1 intensity across an image stack around a single ROI within each cell. The authors interpret Fig.6C to mean SGFP2-CTNNB1 is present as a monomer whether in a complex or not. This is based on the fact the relative brightness averages at 1.0 similar to a monomeric GFP control. However, the spread of relative brightness is large, and often less than <1 so a relative brightness of 1 cannot refer to a monomeric SGFP2-CTNNB1? Does cellular concentration affect relative brightness? If so transiently expressed monomer and dimer GFP may not be the best controls. Aggregation is spatially homogeneous and limited by the diffusion rate of protein/complexes - which your FCS measurements suggest is consistent with a large complex. Thus a single average may not represent the diversity of protein complexes, eN&B could be used (Cutrale et al., 2019). As mentioned in point 3, like FCS, you are only sampling a small region of the cell, which may or may not contain a destruction complex for example. Super-resolution imaging techniques such a STORM or LLSM may help with visualisation of cell complex heterogeneity and give a different impression of complex occupancy. I don't think the N&B data is sufficient to say complexes don't exist that contain more than one SGFP2-CTNNB1 molecule.

4) The computational model relies on a number of assumptions determined in other studies that may not reflect the HAP1 cells used in this study. Lee et al., was performed in Xenopus and Tan et al., 2012 found a number of differences in their mammalian cell studies. Important information regarding the concentration of destruction complex components has also been omitted, this information is important for future comparisons of cell-type specific behaviours.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Summary:

The authors investigate how cells respond to WNT signaling by altering beta catenin (CTNNB1) dynamics. They generated a number of cell lines in which they use different light microscopy techniques –such as FCS and number & brightness (N&B) measurements– to quantitatively investigate the diffusion behavior and complex formation of intracellular CTNNB1. The results are in general well explained, reasoned and technically well-controlled (except for some, which raised concerns that were pointed out by the reviewers). The main finding of the paper is that CTNNB1 seems to reside in slow-moving complexes (that exist both in the presence and absence of WNT) that become slightly more mobile after WNT addition. As pointed out by the reviewers, these results can be interpreted in different ways, and it is not clear whether these complexes represent the destruction complex (cytoplasm) or enhanceosome (nucleus). In summary, yet the work shows some technical proficiency which could address some critical issues in Wnt signaling, the authors would need to identify the issues that could be resolved by the technique and then design experiments to resolve them in the future.

Reviewer #4:

This paper presents CytofRUV, a new tool to remove technical batch effects in CYTOF data, inspired by tools used in the transcriptomics field. There is still a strong need for such tools and I expect this tool to be a valuable addition to the cytometry field. I especially appreciate the authors' effort in providing multiple evaluation measures and informative figures to estimate the properties of the batch effects before and after normalization. There is currently no one-fits-all solution for batch normalization, and having sufficient quality control along the way is absolutely invaluable.

I recommend no major changes to the manuscript, but mainly some additional guidance in the reader's interpretation of some results, and some smaller suggestions to improve figures. Some of the more unexpected results are not commented on in the text and it would be helpful if some interpretation could be given in those cases.

-Many methods cause an increased batch silhouette score compared to raw, does this mean that in those cases the methods increase the batch effects?

-Also the Hellinger distances sometimes become bigger than originally. Would there be any way to check if this distance would be small given an adapted manual gating? Or could there be any reason that actually some cell types are indeed differing in proportion in the different batches, so you would not expect the batch correction to "restore" this (as no cells are added or removed by the correction)? As both CytoNorm and CytofRUV apply the normalization on a cluster-by-cluster basis, I am also not sure why the cluster proportions afterwards would become more similar. Can you give any further intuition about this?

-While there is a section regarding "keeping biological differences" this is only explored on the population level in the individual samples. I would also find it of interest to read something about biological differences between samples which are preserved (e.g. maybe quantifying the differences between the healthy controls?)

Reviewer #3:

The manuscript in review discusses a new method to address technical variances in CYTOF data called CytofRUV and based on Remove Unwanted Variation methodology. CYTOF datasets are prone to significant batch-to-batch variation due to the technical nature of signal registration and this method adds to the group of previously published algorithms aimed to solve the same task.

The manuscript is well-written and the narrative flows well. The authors come up with compelling examples of batch effect in CYTOF data (e.g. Fig.2) that honestly not only call for robust algorithmic normalization but make me somewhat question the claimed reliability of the CYTOF technology to deliver precise measurement of protein expression without robust replicates built into every experimental design of CYTOF experiments; this publication would surely raise awareness of existing issues. Authors also line up a series of metrics to quantify the efficiency of theirs and alternative methods for data normalization, and propose a strong battery of visual cues built into their Shiny app to evaluate the algorithm results.

1) The algorithm performance deserves more discussion that is currently outsourced to the reference to original RUV paper (Molania et al). How computationally demanding is it? What computational resources were used? How does it scale to large datasets? How parametrization (choice of k value) affects the results specifically for CYTOF data (this is slightly touched upon in the Molania et al paper, but the data context is very different)?

2) Are any of the metrics mentioned in the paper built into the R package/Shiny app? From the paper, it looks like the only outputs that the interface presents are the four visual plots but no evaluation metrics of how the normalization affected/improved the data.

3) Besides silhouette scores, were there any other attempts to verify the data integrity post processing? For instance, how reproducible are clustering results after normalization if the processed data are clustered from scratch and compared to clustering performed before normalization?

4) Based on existing datasets and metric outputs, would the authors suggest a way to estimate the minimal number of replicates (as discussed in lines 488-492) required for the specific panel/sample/instrument type to provide necessary power to preserve the resolution of the data post normalization?

Reviewer #2:

The authors have presented a novel approach based on RUV-III for normalizing CyTOF data leveraging replicate samples across batches. The article is clear, well laid out, thoughtful and presents well-substantiated conclusions. The RUV class of method has been applied across high throughput technologies including RNASeq, single-cell RNASeq, nanostring and others and it is a natural extension to single cell cytometry. I have few issues with the paper. My one minor concern is the conflation of the term cell subpopulation with cluster. I don't think this detracts from the conclusions of the paper, but the former typically is reserved for cells of a consistent and verified phenotype. FlowSOM and just about all other clustering methods do not necessarily produce clusters that correspond to consistent cell sub populations (the phenotype of the cells included in a cluster can and does vary). I think to make statements about sub populations, the authors would have to look at manual phenotype assignments as well. I am not suggesting that it is necessary, and I find the evaluation of the method with respect to clusters much more compelling and natural. However, I would request that the authors make the distinction between clusters and cell sub populations in this context.

After looking at the software implementation I think some discussion of the computational complexity and limitations of the method and implementation is warranted, particularly time and memory considerations. Could the method scale to large data sets (100s or 1000s of samples with several 100k cells each), which are typical in clinical studies? Do all data need to be loaded into working memory for the current implementation, or in general?

Reviewer #1:

The article describes CytofRUV, an algorithm for normalization of mass cytometry datasets. The article is well written, the data is publicly available, and the source code is usable and well-documented. My comments are provided below:

Major comments:

1) I believe the focus of this article can be improved. The abstract is a bit confusing. If the article is focused on the algorithm, the focus of the abstract should not be on leukemia. This can be used in many settings. Similarly, much of the article (including 4 of the main figures) are dedicated to establishing that this one dataset indeed does have a batch effect issue. Other datasets are not introduced until the very end of the manuscript. However, for an article focused on the development of a new bioinformatics method, I believe the focus should be on evaluation of the algorithm on a broad range of datasets (which the authors have already done, but should be presented more prominently).

2) Comparison with prior algorithms is only presented in a qualitative manner. Quantification of these comparisons, followed by appropriate statistical tests, would strengthen this article. I don't believe a new algorithm needs to outperform existing algorithms in every test (as it runs against the no free lunch theorem) but quantification should be provided regardless.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 2 of the manuscript.

Summary:

The authors present a new Cytof normalization approach based on RUV III that has proven useful for other technologies including RNASeq, single-cell RNAseq and nanostring. The reviewers all agreed that this was a strong manuscript that makes an important contribution to an area of the field that remains under-served.

Reviewer #3:

The relative contributions of both asymptomatic infections and super spreading events to the ongoing SARS-COV-2 pandemic are critical, controversial questions. As far as I know this may be the first paper to utilize the approach combining phylogenetic inferences from genomic data with time series case data to estimate these parameters from available data applied to the ongoing SARS-COV-2 pandemic. However, with so many papers coming out so quickly it's possible I missed this.

Here, the authors combine viral phylogenetics with time series case data to estimate parameters (including temporally structured estimates of the reproductive number) about the SARS-COV-2 pandemic in 12 locations globally. They find that the number of undetected infections ranges substantially by location from 13% to 92% and the precision of their estimates improves substantially with the number of viral genomes included from each location and this is visualized in Figure 2.

However, in its current form it suffers from some shortcomings..

SARS-COV-2 evolves slowly relative to other viruses and this can lead to high levels of phylogenetic uncertainty in recovered trees and this can have a strong influence on parameter estimates. According to the methods and the supplemental material the authors inferred a single phylogenetic tree for each location. The authors should be encouraged to infer a distribution of trees for each location and condition their analyses across this additional uncertainty. If this has already been done then the manuscript needs to be augmented to make this clear.

Abstract:

This section requires a thorough edit to improve clarity, in its current form it is rather discombobulated and needs to better link aims to results to conclusions.

Introduction:

The first 2 paragraphs of the introduction should be switched. The introduction should start with the big questions - in this case why it is important in the big picture of epidemiology to estimate parameters like the total number of infections - and then introduce the study system in play to address the big questions in this case SARS-COV-2.

The third paragraph addresses other ways to directly estimate the number of infected through serological surveys. Missing from this paragraph is acknowledging the assumption that markers of immunity lasts long enough for such surveys to be effective in detecting past infected individuals.

The final paragraph of the introduction outlines the aims and is rather lacking in scientific detail namely what are the hypotheses? What are the alternatives? What are the predictions and tests of hypotheses in play? What specific hypotheses are the authors testing by applying their method? This requires clarification.

Methods:

Generally, the methods lack sufficient detail to replicate what the authors have done.

In the Viral genomes section of the methods it is stated that several locations were excluded due to "multiple circulating lineages" however nearly all of the locations included (e.g. Guangdong, Hubei, Shanghai, UK) also have multiple circulating lineages. What was done here needs to be clarified greatly.

Phylogenetic inference as performed in IQ-TREE is fine however as previously mentioned the authors need to minimally infer a distribution of trees for each region to condition their subsequent analyses across.

In the section on sub-sampling the sequences to the dominant lineages, how was lineage assignment done? Using Pangolin? Or another classification system? More detail is needed.

A bit more detail on how the authors determined convergence was achieved would be valuable. For example, how was visual confirmation of convergence done? Via visual inspection of parameter traces? A generalist reader may need more detail than has been provided.

Results:

More detail is needed in the figure legend for Figure 1. For example unless I misunderstand this it is mentioned that the red lines are HPD intervals on those days but it is actually a shaded area with a measure of central tendency as a red line.

Discussion:

Overall, the discussion puts the results in appropriate context. It seems though that caveats associated with these analyses were not appropriately acknowledged. A bit more thought should be put into appropriate acknowledgements of things which may affect the authors estimates and interpretations of findings.

On balance I do think that the approach utilized in this manuscript makes a potentially useful contribution to addressing the current pandemic and it is to my knowledge this approach has not yet been applied to SARS-COV-2. I would like to see additional analyses (incorporation of phylogenetic uncertainty) and a thorough edit and revision for clarity.

Reviewer #2:

The authors presented a Bayesian inference framework to fit a branching process model that incorporates both viral genomes and time series of case data to estimate the undetected COVID-19 infections. While the method seems to be valid, the application of the method on the data is subject to some uncertainties especially for locations in Asia, such as Japan, Shanghai and Hong Kong. Please see below for my comments/suggestions:

Major comments:

1) My biggest concern is that in many of the locations in Asia in Table 1/Figure 1, no sustained local outbreak has been detected. So far the majority of cases in Hong Kong were imported cases (https://www.chp.gov.hk/files/pdf/local_situation_covid19_en.pdf ). By the end of Feb 2020, more than 50% of cases in Guangdong of China were imported cases from Hubei. How would the sequence analysis and model fit be if imported cases are excluded?

2) As mentioned above, the proportion of imported cases would likely affect the estimation of the Rt and undetected infections. What if the method is applied to imported cases and local separately for some of the locations such as Hong Kong (in which the imported/local case status is clear for every case)?

Reviewer #1:

In this work the authors use previously-developed methods linking viral sequence data and reported case counts to estimate the percentage of undetected infections and the effective reproduction number Rt through time in a number of locations. This is an extremely important topic. It remains the case that despite the urgency, there has not been consistent population-based viral testing and the fraction of COVID-19 cases that are reported remains largely unknown. This is an important topic and if genomics can help it is very valuable.

However, there are some concerns about the methods for this specific application. Validation on simulated data, and exploration of robustness to some of the assumptions and limitations, could help.

Dates of confirmation may differ from dates of symptom onset by many days. This is discussed briefly but the impact of a shift is not explored. The bias may additionally depend on the population size, with more bias towards the beginning when there are few cases and few sequences. It could also impact the sequencing; this is discussed briefly but could be explored to some extent by shifting the dates and re-estimating.

The authors subsampled the sequences to the dominant lineages. More information about how this was done would be helpful. In addition, of course without information to link viral genomes to reported case counts, the same adjustment cannot be made to the reported cases -- could this impact the results? It is not quite clear how multiple lineages, introductions, geographical mixing in the phylogeny are treated. For example, consider an example in which the California sequences have some Minnesota ones embedded in them, scattered in a clade. If the Minnesota sequences in entirety are treated as one phylogeny (without any of the CA tips) then there would be very long branches between these and other Minnesota sequences, and the likelihood would reflect no branching events on these branches. In reality there were plenty of events but they were in CA. Meanwhile those branching events do not occur in the CA tree either, because their descendants have been pruned out of the CA analysis. In any case it is not clear what precisely is meant by not including locations with co-circulating lineages, nor how geographical mixing is treated.

The probability of sequencing, and its variation over time, may affect the model's inferences, because in times of more dense sequencing the intervals in the tree will be shorter (and conversely). The model may not be able to distinguish this from changes in prevalence and reporting fraction. Should there be a rho_t that applies to the sequencing data?

I wonder if the authors are able to model tips that occur in the reported data, handling these dates differently. It seems that the only link is through the conditional independence of the yi and zi information (condition on the xi information). I also wonder about the impact of phylogenetic uncertainty.

There seems to be a possible identifiability issue with rho_t and x_t, because surely a higher x and lower rho could give the same likelihood, particularly since we can't sequence cases that we can't detect.

How do the estimates of the reporting fraction compare to those obtained for example with the model by Russell et al ( https://cmmid.github.io/topics/covid19/global_cfr_estimates.html ) or with other estimates of under-reporting? (Some of these are given in the results but CIs are wide).

I would have liked to see more information for how this was done: "we computed the smallest number of individuals that could contribute to 80% of infections during each week (Figure 4)". Similarly, detailed methods are not given for the 'time to detect an outbreak' results.

It would be interesting to see the comparison between the estimated reporting fractions and the testing data available at (for example) https://covidtracking.com which allows downloads of data on testing through time by state. It is mentioned in the discussion; information about testing is available for many places (US states and otherwise) .

I am also concerned about the large population assumption that is inherent in the mathematics behind the core equation for lambda_t (which the authors should either derive or give the citation for). This equation requires that the mean of the number of offspring in the data is equal to the mean of the offspring distribution, which only happens in the limit when the present and past populations are both large. The same assumption is required for the variance. Particularly in the early stages the large population assumption is unlikely to be met.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 3 of the manuscript.

Summary:

This paper uses a combination of sequence and case data to estimate the ascertainment rate of COVID19 in different settings. The methods are known but this is the first application to SARS-CoV-2 data, and the topic is of very high importance. The reviewers had some substantial concerns about the methodology and the clarity of description.

Reviewer #3:

In this manuscript the authors used high throughput light microscopy and image analysis to study the effects of essential gene knockdown via an arrayed CRISPRi library in M.smegmatis.

There are many technical advances to this paper, and the experiments are well executed. The data and its analysis adds value to the mycobacterial field. I particularly appreciated the thoughtful Discussion, which honestly laid out the limitations for the author's work.

However, in some areas, the lengthy manuscript came across as a bit unfocused. For example, in addition to describing the methods of their technique, the author's validate or give examples of what their data contain (identification of cryptic putative RM system, histidine auxotroph phenotypes, effects of disrupting mycolic acid biosynthesis). They then discuss the potential to use CRISPRi to conform compound MOA. This is a lot of information (10 figures with many subpanels), but none of these threads are really taken to completion. I appreciate the amount of work that doing that would take, so I'm not suggesting that as a revision. But, reshuffling or restructuring some of these sections, may help to guide the reader towards the utility of these data.

Lastly, and I think importantly, after reading this manuscript, I was left with the lingering question: for any essential gene that I'm interested in, would these data help to make hypotheses about its function. And ... I'm not sure... The data as presented in Figure 6 do not help this case. While some functionally related genes cluster together, many do not, especially for genes that fall into cluster 2.

With some textual changes to streamline the manuscript, I think the manuscript could be improved.

Reviewer #2:

de Wet et al. screen a CRISPRi library of M. smeg. essential genes for morphological phenotypes. Using a sensitive analytical approach, they find that most essential knockdown strains have morphological phenotypes. They further show that functionally related genes cluster by morphology in multidimensional space. Finally, they associate morphological changes with antibiotics to probe antibiotic MOA. This manuscript will be of interest to researchers studying essential genes in Mycobacteria.

General Comments:

1) "Moreover,to verify the reproducibility of the imaging workflow, replicate imaging was performed on separate days for 134 strains." Does this mean that the authors don't have replicate data for 29 strains? If so, imaging of these strains must be repeated to verify reproducibility. Have the authors validated any phenotypes with a second guide RNA to rule out off target effects?

2) MSMEG_3213 isn't an example of defining the function of an uncharacterized gene--instead it simply validates existing database predictions. Further, the data presented here do not demonstrate that MSMEG_3213 is the methylase of an R-M pair.

3) The his gene depletion phenotypes are likely due to translation defects that result from uncharged tRNAs. This is consistent with tRNA synthetase/ribosomal protein knockdown phenotypes presented in this manuscript, as well as the observation that translation inhibition by knockdown or serine hydroxymate produced elongated cells in Bacillus subtilis (PMID: 27238023).

Reviewer #1:

General assessment:

This manuscript addresses the lag in identifying functions of genes annotated in bacterial genomes. It is an epic presentation of a line of investigation from inception through assay development and validation to identifying previously unknown functional associations. Beyond these initial novel insights, the developed phenoprinting approach and the resulting UMAP space provide a solid foundation for future conditional gene function and initial drug mechanism of action studies.

Substantive concerns:

None

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Summary:

This manuscript combines a CRISPRi library in Mycobacterium smegmatis with high throughput light microscopy and image analysis to investigate the effects of essential gene knockdown on bacterial morphology. The reviewers all agree that there are many technical advances presented in this paper, the experiments are well executed, and the data and its analysis is significant for the field. However, there are some questions regarding the reproducibility of the data and the utility of these data as a predictive tool. The reviewers believe that these questions should be straightforward to address, as described more below.

Note: This rebuttal was posted by the corresponding author to Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

We thank the reviewers for their close reading and constructive comments on our manuscript. We believe that their insight has substantially strengthened our manuscript. Please find our response/revision plan for each comment below (in blue). Note, because of the substantial changes to the figures and the additional experiments that are we are undertaking, we have not initially revised the text. The proposed textual revisions will be included in the full revision.

Reviewer #1 (Evidence, reproducibility and clarity (Required)):

The Katz lab has contributed greatly to the field of epigenetic reprogramming over the years, and this is

another excellent paper on the subject. I enjoyed reviewing this manuscript and don't have any major

comments/suggestions for improving it. The findings presented are novel and important, the results are clear

cut, and the writing is clear.

It's important to stress the novelty of the findings, which build upon previous studies from the same lab (upon

a shallow look one might think that some of the conclusions were described before, but this is not the case).

Despite the fact that this system has been studied in depth before, it remained unclear why and how

germline genes are bookmarked by H3K36 in the embryo, and it wasn't known why germline genes are not

expressed in the soma.

To study these questions Carpenter et al. examine multiple phenotypes (developmental aberrations,

sterility), that they combine with analysis of multiple genetic backgrounds, RNA-seq, CHIP-seq, single

molecule FISH, and fluorescent transgenes.

Previous observations from the Katz lab suggested that progeny derived from spr-5;met-2 double mutants

can develop abnormally. They show here that the progeny of these double mutants (unlike spr-5 and met-2

single mutants) develop severe and highly penetrate developmental delays, a Pvl phenotype, and sterility.

They show also that spr-5; met-2 maternal reprogramming prevents developmental delay by restricting

ectopic MES-4 bookmarking, and that developmental delay of spr-5;met-2 progeny is the result of ectopic

expression of MES-4 germline genes. The bottom line is that they shed light on how SPR-5, MET-2 and

MES-4 balance inter-generational inheritance of H3K4, H3K9, and H3K36 methylation, to allow correct

specification of germline and somatic cells. This is all very important and relevant also to other organisms.

**(very) Minor comments:**

-Since the word "heritable" is used in different contexts, it could be helpful to elaborate, perhaps in the

introduction, on the distinction between cellular memory and transgenerational inheritance.

We are happy to elaborate on this in the revised manuscript.

-It might be interesting in the Discussion to expand further about the links between heritable chromatin

marks and heritable small RNAs. The do hint that the result regarding the silencing of the somatic transgene

are especially intriguing.

We are happy to expand this in the revised manuscript.

Reviewer #1 (Significance (Required)):

This is an exciting paper which build upon years of important work in the Katz lab. The novelty of the paper

is in pinpointing the mechanisms that bookmark germline genes by H3K36 in the embryo, and explaining

why and how germline genes are prevented from being expressed in the soma.

Reviewer #2 (Evidence, reproducibility and clarity (Required)):

Katz and colleagues examine the interaction between the methyltransferase MES-4 and spr-5; met-2 double

mutants. Their prior analysis (PNAS, 2014) showed the dramatic enhancement in sterility and development

for spr-5; met-2; this paper extends that finding by showing these effects depend on MES-4. The results are

interesting and the genetic interactions dramatic. The examination by RNAseq and ChIP helps move the

phenotypes into a more molecular analysis. The authors hypothesize that SPR-5 and MET-2 modify

chromatin of germline genes (MES-4 targets) in somatic cells, and this is required to silence germline genes

in the soma. A few issues need to be resolved to test these ideas and rule out others.

**Main comments:**

The authors' hypothesis is that SPR-5 and MET-2 act directly, to modify chromatin of germline genes (MES-

4 targets), but alternate hypothesis is that the key regulated genes are i) MES-4 itself and/or ii) known

regulators of germline gene expression e.g. the piwi pathway. Mis regulation of these factors in the soma

could be responsible for the phenotypes. Therefore, the authors should analyze expression (smFISH and

where possible protein stains) for MES-4 and PIWI components in the embryo and larvae of wildtype, double

and triple mutant strains. These experiments are essential and not difficult to perform.

In our RNA-seq analysis we see a small elevation of MES-4 itself (average 1.18 log2 fold change across 5 replicates). This does not seem likely to be solely driving such a dramatic phenotype. Nevertheless, it is possible that the small increase in expression of MES-4 itself could be contributing. To determine if MES-4 is being ectopically expressed in spr-5; met-2 double mutants, we have obtained a tag version of MES-4 from Dr. Susan Strome and will use this to examine the localization of MES-4 protein in spr-5; met-2 double mutants. We are definitely interested in the potential interaction between PIWI components and the histone modifying enzymes that we have explored in this study. However, since RNAi of MES-4 is sufficient to rescue the developmental delay of spr-5; met-2 mutants, we have chosen to focus on that interaction in this paper. In the future, we hope to examine the role of PIWI components in this system.

A second aspect of the hypothesis is that spr-5 and met-2 act before mes-4 and that while these genes are

maternally expressed, they act in the embryo. There really aren't data to support these ideas - the timing and

location of the factors' activities have not been pinned down. One way to begin to address this question

would be to perform smFISH on the target genes and on mes-4 in embryos and determine when and where

changes first appear. smFISH in embryos is critical - relying on L1 data is too late. If timing data cannot be

obtained, then I suggest that the authors back off of the timing ideas or at least explain the caveats.

Certainly, figure 8 should be simplified and timing removed. (note: Typical maternal effect tests probably

won't work because if the genes' RNAs are germline deposited, then a maternal effect test will reflect when

the RNA is expressed but not when the protein is active. A TS allele would be needed, and that may not be

available.)

To determine the timing of the ectopic expression of MES-4 targets, we have performed smFISH on two MES-4 targets in embryos. Thus far, these experiments show that MES-4 targets are ectopically expressed in the embryo, but only after the maternal to zygotic transition. This is consistent with our proposed model. A figure containing this data will be added to the revised manuscript. In addition, our model is predicated on the known embryonic protein localization of SPR-5 and MES-4. Maternal SPR-5 protein is present in the early embryo up to around the 8-cell stage, but absent in later embryos (Katz et al., 2009). In addition, in mice, the SPR-5 ortholog LSD1 is required maternally prior to the 2-cell stage (Wasson et al., 2016 and Ancelin et al., 2016). In contrast, MES-4 continues to be expressed in the embryo until later embryonic stages where it is concentrated into the germline precursors Z2 and Z3 (Fong et al., 2002). This is consistent with SPR-5 establishing a chromatin state that continues to be antagonized by MES-4. There is evidence that MET-2 is expressed both in early embryos and later embryos. However, since the phenotype of MET-2 so closely resembles the phenotype of SPR-5 (Kerr et al., 2014), we have included it in our model as working with SPR-5. Further experimentation will be required to substantiate the model, but we believe the model is consistent with all of the current data.

Writing/clarity:

-It would be helpful to include a table that lists the specific genes studied in the paper and how they behaved

in the different assays e.g. RNAseq 1, RNAseq 2, MES-4 target, ChIP. That way, readers will understand

each of the genes better.

We are happy to include a table in the revised manuscript.

-At the end of each experiment, it would be helpful to explain the conclusion and not wait until the

Discussion. For readers not in the field, the logic of the Results section is hard to follow.

This seems like a stylistic choice. Traditionally, papers did not include any conclusions in the results section, and it is our preference to keep our paper organized this way. However, if the reviewer would still like us to change this, we are happy to do so.

-The model is explained over three pages in the Discussion. It would be great to begin with a single

paragraph that summarizes the model/point of the paper simply and clearly.

The discussion in the revised manuscript will altered to include this.

**Specific comments:**

-Figure 1 has been published previously and should be moved to the supplement.

In our original paper (Kerr et al.) we reported in the text that spr-5; met-2 mutants have a developmental delay. However, we did not characterize this developmental delay. Nor did we include any images of the double mutants, except for one image of the adult germline phenotype. As a result, we believe that the inclusion of the developmental delay in the main body of this manuscript is warranted.

-Cite their prior paper for the vulval defects e.g. page 6 or show in supplement.

We are happy to include a citation of our previous paper for the vulval defects in the revised manuscript.

-The second RNAseq data should be shown in the Results since it is much stronger. The first RNAseq,

which is less robust, should be moved to supplement.

The revised manuscript will include this alteration.

-Figure 3 is very nice. Please explain why the RNAs were picked (+ the table, see comment above), and

please add here or in a new figure mes-4 and piwi pathway expression data in wildtype vs double/triple

mutants.

We performed RT-PCR on 9 MES-4 targets. These 9 targets were picked because they had the highest ectopic expression in spr-5; met-2 mutants and largest change in H3K36me3 in spr-5; met-2 mutants versus Wild Type. Amongst these 9 genes, we performed smFISH on htp-1 and cpb-1 because they are relatively well characterized as germline genes.

The revised manuscript will include added panels to supplemental figure 2 showing the expression of PIWI pathway components.

-Figure 3 here or later, please show if mes-4 RNAi removes somatic expression of target genes.

We are currently carrying out this experiment. Once it is completed, the data will hopefully be added to the paper.

-Is embryogenesis delayed?

Embryogenesis seems to be sped up in spr-5; met-2 mutants. A supplemental figure will be added to the revised manuscript showing this. It is unclear why embryogenesis is sped up. However, this confirms that the developmental delay is unique to the L1/L2 stages.

-Figure 4 since htp-1 smFISH is so dramatic, it would be helpful to include htp-1 in the lower panels.

htp-1 will be added to the lower panels in the revised manuscript.

-Figure 4, please add an extra 2 upper panels showing all the genes in N2 vs spr-5;met-2, for comparison to

the mes-4 cohort.

As a control, we will add panels showing a comparison to all germline genes, excluding MES-4 targets. This new data shows that germline genes that are not MES-4 targets do not have ectopic H3K36me3. This data, which further suggests that the phenomenon is confined to MES-4 targets, is consistent with our results showing that MES-4 RNAi is sufficient to suppress the developmental delay.

-Figure 6. Please show a control that met-1 RNAi is working.

We performed RT-PCR to try and confirm that met-1 RNAi was working. Despite controls repeating the MES-4 suppression and verifying that RNAi was working, we were unable to demonstrate that met-1 was knocked down. As a result, we will remove this result from the paper. Importantly, this does not affect the conclusion of the paper.

-To quantify histone marks more clearly, it would be wonderful to have a graph of the mean log across the

gene. showing the mean numbers would help clarify the degree of the effect. we had an image as an

example but it does not paste into the reviewer box. Instead, see figure 2 or figure 4

here: https://www.nature.com/articles/ng.322

We will attempt to include this analysis in the revised manuscript.

Reviewer #2 (Significance (Required)):

Katz and colleagues examine the interaction between the methyltransferase MES-4 and spr-5; met-2 double

mutants. Their prior analysis (PNAS, 2014) showed the dramatic enhancement in sterility and development

for spr-5; met-2; this paper extends that finding by showing these effects depend on MES-4. The results are

interesting and the genetic interactions dramatic. The examination by RNAseq and ChIP helps move the

phenotypes into a more molecular analysis.

This work will be of interest to people following transgenerational inheritance, generally in the C. elegans

field. People using other organisms may read it also, although some of the worm genetics may be

complicated. Some of the writing suggestions could make a difference.

I study C. elegans embryogenesis, chromatin and inheritance.

Reviewer #3 (Evidence, reproducibility and clarity (Required)):

In the paper entitled "C. elegans establishes germline versus soma by balancing inherited histone

methylation" Carpenter BS et al examined a double mutant worm strain they had previously produced of the

H3K4me1/2 demethylase spr-5 and the predicted H3K9me1/me2 methylase met-2. These mutant worms

have a developmental delay that arises by the L2 larval stage. They performed an analysis of what genes

get misexpressed in these double mutants by performing RNAseq and compare this to datasets generated

from other labs on an H3K36me2/me3 methylase MES-4 where they see a high degree of overlap. They

validate the misexpression of some germline specific genes in the soma by in situ and validate that there is a

dysregulation of H3K36me3 in their double mutant worms. They further find that knocking down mes-4

reverts the developmental delay.

I think that the authors need to make more of an effort to be a bit more scholarly in terms of placing their

work in the context of the field as a whole and also need to add a few additional experiments as well as

reorganize a bit before this is ready for publication. Remember that the average reader is not necessarily an

expert in C. elegans or this particular field and you really want to try and make the manuscript as accessible

to everyone as possible.

**Major Points**

1)It would be good to see western blots or quantitative mass spec examining H3K36me3 in the WT and spr-

5;met-2 double mutant worms. I believe this was also previously reported by Greer EL et al Cell Rep 2014 in

the single spr-5 mutant worm so that work should be cited here in addition to the identification of JMJD-2 as

an enzyme involved in the inheritance of H3K4me2 phenotype.

The ectopic H3K36me3 is confined to a small set of MES-4 targets. We don’t even see ectopic H3K36me3 at non-MES-4 germline genes (see above). Therefore, we don’t expect to see any global differences in bulk H3K36me3. Greer et al reported that there are elevated H3K36me3 levels in spr-5 mutants. This discrepancy may be due to different stages (embryos, germline) present in their bulk preparation. Alternatively, the met-2 mutant may counteract the effect of the spr-5 mutation on H3K36me3. Regardless, we believe that the genome-wide ChIP-seq is more informative than bulk H3K36me3 levels.

We will add a citation for the Greer paper in the revised manuscript.

2)Missing from Fig.5 is mes-4 KD by itself. This is needed to determine whether these effects are specific to

the spr-5;met-2 double mutants or more general effects that KD of mes-4 would decrease the expression of

all these genes to a similar extent. Then statistics should be done to see if the decrease in the WT context is

the same or greater than the decrease in the double mutants.

The MES-4 targets are generally expressed only in the germline and defined by having mes-4 dependent H3K36me3. Knocking down mes-4 would be expected to prevent the expression of these genes in the germline, but this is difficult to test because mes-4 mutants basically don’t make a germline. Regardless, knocking down mes-4 by itself would only assess the role of MES-4 in germline transcription, not the ectopic expression that is being assayed in spr-5; met-2 mutants in Fig 5. Importantly, it remains possible that spr-5; met-2 mutants might also result in an increase in the expression of MES-4 targets in the germline. However, the experiments performed in this manuscript were conducted on L1 larvae, which do not have any germline expression, to eliminate this potential confounding contribution.

**Minor Points**

1)A greater attempt needs to be made to be more scholarly for citing previously published literature. This

includes work on the inheritance of H3K27 and H3K36 methylation in C. elegans and other species as well.

A few papers which seem germane to this story which should be cited in the intro are (Nottke AC et al PNAS

2011, Gaydos LJ et al Science 2014, Ost A et al Cell 2014, Greer EL et al Cell Rep 2014, Siklenka K et al

Science 2015, Tabuchi TM et al Nat Comm 2018, Kaneshiro KR et al Nat Comm 2019). This problem is not

restricted to the intro.

Although many of these excellent papers are broadly relevant to this current work, they are not necessarily directly relevant to this paper. For this reason, they were not originally cited. Nevertheless, we will attempt to cite these papers in the revised version when possible.

2)I think that the authors need to be a little less definitive with your language. Theories should be introduced

as possibilities rather than conclusions. Should remove "comprehensive" from intro as there are many other

methods which could be done to test this.

Throughout the manuscript, we have tried to be clear what the data suggests versus what is model based on the data. Nevertheless, to further clarify this, we are happy to remove “comprehensive” from the intro.

3)The authors should describe what PIE-1 is. Is this a transcription factor?

PIE-1 is a transcriptional inhibitor that is thought to block RNA polII elongation by mimicking the CTD of RNA polII and competing for phosphorylation. We are happy to add a reference to this function in the revised manuscript.

4)The language needs clarification about MES-4 germline genes and bookmark genes. Are these bound by

MES-4 or marked with K36me2/3?

The revised manuscript will be modified to make this definition more clear.

5)I think Fig S1 E+F should be in the main figure 1 so readers can see the extent of the phenotype.

The original single image of the spr-5; met-2 adult germline phenotype (including the protruding vulva) was included in our previous publication. In this manuscript, we have now quantified this phenotype, which is why it is included in the supplement here. However, because the original picture was included in our original publication, we prefer to leave it as supplemental.

6)For Fig S2 it would be good to do the same statistics that is done in Fig 2 and mention them in the text so

the readers can see that the overlap is statistically significant.

We are happy to include these statistics in the revised manuscript.

7)Fig S2.2 should be yellow blue rather than red green for the colorblind out there.

Thanks for pointing this out. We are happy to change the colors in the revised manuscript.

8)When saying "Many of these genes involved in these processes..." the authors need to include numbers

and statistics.

We will amend the revised text to make the definition of the MES-4 genes more clear.

9)Should use WT instead of N2 and specify what wildtype is in methods.

We will use WT instead of N2 in the revised manuscript.

10)Fig. 2A + B could be displayed in a single figure. And Fig 2D seems superfluous and could be combined

with 2C or alternatively it could be put in supplementary.

Figure 2A and 2B were purposely separated to make it clear how many of the overlapped changes are up versus down. In the revised manuscript, Figure

2D will be moved to the supplement.

11)Non-C. elegans experts won't understand what balancers are. An effort should be made to make this

accessible to all. Explaining when genes are heterozygous or homozygous mutants seems relevant

here.

The text of the revised manuscript will be amended to make it more accessible for non-C. elegans readers.

12)The GO categories (Fig. S2) should be in the main figure and need to be made to look more scientific

rather than copied and pasted from a program.

The GO categories were included to be comprehensive and do not contribute substantially to the main conclusion of the paper. This is why they are supplemental. In the revised manuscript, we will edit the GO results so that they look more scientific.

13)Fig. 7 seems a bit out of place. If the authors were to KD mes-4 and similarly show that the phenotype

reverts that would help justify its inclusion in this paper. Without it seems like a bit of an add on that belongs

elsewhere.

We believe that the somatic expression of a transgene in spr-5; met-2 mutants adds to our potential understanding of how this double mutant may lead to developmental delay. This is true, regardless of whether of whether the somatic transgene expression is mes-4 dependent or not.

Reviewer #3 (Significance (Required)):

I think this is an interesting and timely piece of work. A little more effort needs to be put in to make sure it is

accessible to the average reader and has sufficient inclusion of more of the large body of work on

inheritance of histone modifications. I think C. elegans researchers as well as people interested in

inheritance and the setup of the germline will be interested in this work.

REFEREES CROSS COMMENTING

I agree with Reviewer #2's comments on experiments to include or exclude alternative models. I also agree

about their statement about rewriting to make it more accessible to others who aren't experts in this

specialized portion of C. elegans research. All in all it seems like the experiments which are required by

reviewer #2 and myself as well as the rewriting should be quite feasible.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #3

Evidence, reproducibility and clarity

In the paper entitled "C. elegans establishes germline versus soma by balancing inherited histone methylation" Carpenter BS et al examined a double mutant worm strain they had previously produced of the H3K4me1/2 demethylase spr-5 and the predicted H3K9me1/me2 methylase met-2. These mutant worms have a developmental delay that arises by the L2 larval stage. They performed an analysis of what genes get misexpressed in these double mutants by performing RNAseq and compare this to datasets generated from other labs on an H3K36me2/me3 methylase MES-4 where they see a high degree of overlap. They validate the misexpression of some germline specific genes in the soma by in situ and validate that there is a dysregulation of H3K36me3 in their double mutant worms. They further find that knocking down mes-4 reverts the developmental delay.

I think that the authors need to make more of an effort to be a bit more scholarly in terms of placing their work in the context of the field as a whole and also need to add a few additional experiments as well as reorganize a bit before this is ready for publication. Remember that the average reader is not necessarily an expert in C. elegans or this particular field and you really want to try and make the manuscript as accessible to everyone as possible.

Major Points

1)It would be good to see western blots or quantitative mass spec examining H3K36me3 in the WT and spr-5;met-2 double mutant worms. I believe this was also previously reported by Greer EL et al Cell Rep 2014 in the single spr-5 mutant worm so that work should be cited here in addition to the identification of JMJD-2 as an enzyme involved in the inheritance of H3K4me2 phenotype.

2)Missing from Fig.5 is mes-4 KD by itself. This is needed to determine whether these effects are specific to the spr-5;met-2 double mutants or more general effects that KD of mes-4 would decrease the expression of all these genes to a similar extent. Then statistics should be done to see if the decrease in the WT context is the same or greater than the decrease in the double mutants.

Minor Points

1)A greater attempt needs to be made to be more scholarly for citing previously published literature. This includes work on the inheritance of H3K27 and H3K36 methylation in C. elegans and other species as well. A few papers which seem germane to this story which should be cited in the intro are (Nottke AC et al PNAS 2011, Gaydos LJ et al Science 2014, Ost A et al Cell 2014, Greer EL et al Cell Rep 2014, Siklenka K et al Science 2015, Tabuchi TM et al Nat Comm 2018, Kaneshiro KR et al Nat Comm 2019). This problem is not restricted to the intro.

2)I think that the authors need to be a little less definitive with your language. Theories should be introduced as possibilities rather than conclusions. Should remove "comprehensive" from intro as there are many other methods which could be done to test this.

3)The authors should describe what PIE-1 is. Is this a transcription factor?

4)The language needs clarification about MES-4 germline genes and bookmark genes. Are these bound by MES-4 or marked with K36me2/3?

5)I think Fig S1 E+F should be in the main figure 1 so readers can see the extent of the phenotype.

6)For Fig S2 it would be good to do the same statistics that is done in Fig 2 and mention them in the text so the readers can see that the overlap is statistically significant.

7)Fig S2.2 should be yellow blue rather than red green for the colorblind out there.

8)When saying "Many of these genes involved in these processes..." the authors need to include numbers and statistics.

9)Should use WT instead of N2 and specify what wildtype is in methods.

10)Fig. 2A + B could be displayed in a single figure. And Fig 2D seems superfluous and could be combined with 2C or alternatively it could be put in supplementary.

11)Non-C. elegans experts won't understand what balancers are. An effort should be made to make this accessible to all. Explaining when genes are heterozygous or homozygous mutants seems relevant here.

12)The GO categories (Fig. S2) should be in the main figure and need to be made to look more scientific rather than copied and pasted from a program.

13)Fig. 7 seems a bit out of place. If the authors were to KD mes-4 and similarly show that the phenotype reverts that would help justify its inclusion in this paper. Without it seems like a bit of an add on that belongs elsewhere.

Significance

I think this is an interesting and timely piece of work. A little more effort needs to be put in to make sure it is accessible to the average reader and has sufficient inclusion of more of the large body of work on inheritance of histone modifications. I think C. elegans researchers as well as people interested in inheritance and the setup of the germline will be interested in this work.

REFEREES CROSS COMMENTING

I agree with Reviewer #2's comments on experiments to include or exclude alternative models. I also agree about their statement about rewriting to make it more accessible to others who aren't experts in this specialized portion of C. elegans research. All in all it seems like the experiments which are required by reviewer #2 and myself as well as the rewriting should be quite feasible.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

Katz and colleagues examine the interaction between the methyltransferase MES-4 and spr-5; met-2 double mutants. Their prior analysis (PNAS, 2014) showed the dramatic enhancement in sterility and development for spr-5; met-2; this paper extends that finding by showing these effects depend on MES-4. The results are interesting and the genetic interactions dramatic. The examination by RNAseq and ChIP helps move the phenotypes into a more molecular analysis. The authors hypothesize that SPR-5 and MET-2 modify chromatin of germline genes (MES-4 targets) in somatic cells, and this is required to silence germline genes in the soma. A few issues need to be resolved to test these ideas and rule out others.

Main comments:

The authors' hypothesis is that SPR-5 and MET-2 act directly, to modify chromatin of germline genes (MES-4 targets), but alternate hypothesis is that the key regulated genes are i) MES-4 itself and/or ii) known regulators of germline gene expression e.g. the piwi pathway. Mis regulation of these factors in the soma could be responsible for the phenotypes. Therefore, the authors should analyze expression (smFISH and where possible protein stains) for MES-4 and PIWI components in the embryo and larvae of wildtype, double and triple mutant strains. These experiments are essential and not difficult to perform.

A second aspect of the hypothesis is that spr-5 and met-2 act before mes-4 and that while these genes are maternally expressed, they act in the embryo. There really aren't data to support these ideas - the timing and location of the factors' activities have not been pinned down. One way to begin to address this question would be to perform smFISH on the target genes and on mes-4 in embryos and determine when and where changes first appear. smFISH in embryos is critical - relying on L1 data is too late. If timing data cannot be obtained, then I suggest that the authors back off of the timing ideas or at least explain the caveats. Certainly, figure 8 should be simplified and timing removed. (note: Typical maternal effect tests probably won't work because if the genes' RNAs are germline deposited, then a maternal effect test will reflect when the RNA is expressed but not when the protein is active. A TS allele would be needed, and that may not be available.)

Writing/clarity:

-It would be helpful to include a table that lists the specific genes studied in the paper and how they behaved in the different assays e.g. RNAseq 1, RNAseq 2, MES-4 target, ChIP. That way, readers will understand each of the genes better.

-At the end of each experiment, it would be helpful to explain the conclusion and not wait until the Discussion. For readers not in the field, the logic of the Results section is hard to follow.

-The model is explained over three pages in the Discussion. It would be great to begin with a single paragraph that summarizes the model/point of the paper simply and clearly.

Specific comments:

-Figure 1 has been published previously and should be moved to the supplement.

-Cite their prior paper for the vulval defects e.g. page 6 or show in supplement.

-The second RNAseq data should be shown in the Results since it is much stronger. The first RNAseq, which is less robust, should be moved to supplement.

-Figure 3 is very nice. Please explain why the RNAs were picked (+ the table, see comment above), and please add here or in a new figure mes-4 and piwi pathway expression data in wildtype vs double/triple mutants.

-Figure 3 here or later, please show if mes-4 RNAi removes somatic expression of target genes.

-Is embryogenesis delayed?

-Figure 4 since htp-1 smFISH is so dramatic, it would be helpful to include htp-1 in the lower panels.

-Figure 4, please add an extra 2 upper panels showing all the genes in N2 vs spr-5;met-2, for comparison to the mes-4 cohort.

-Figure 6. Please show a control that met-1 RNAi is working.

-To quantify histone marks more clearly, it would be wonderful to have a graph of the mean log across the gene. showing the mean numbers would help clarify the degree of the effect. we had an image as an example but it does not paste into the reviewer box. Instead, see figure 2 or figure 4 here: https://www.nature.com/articles/ng.322

Significance

Katz and colleagues examine the interaction between the methyltransferase MES-4 and spr-5; met-2 double mutants. Their prior analysis (PNAS, 2014) showed the dramatic enhancement in sterility and development for spr-5; met-2; this paper extends that finding by showing these effects depend on MES-4. The results are interesting and the genetic interactions dramatic. The examination by RNAseq and ChIP helps move the phenotypes into a more molecular analysis.

This work will be of interest to people following transgenerational inheritance, generally in the C. elegans field. People using other organisms may read it also, although some of the worm genetics may be complicated. Some of the writing suggestions could make a difference.

I study C. elegans embryogenesis, chromatin and inheritance.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

The Katz lab has contributed greatly to the field of epigenetic reprogramming over the years, and this is another excellent paper on the subject. I enjoyed reviewing this manuscript and don't have any major comments/suggestions for improving it. The findings presented are novel and important, the results are clear cut, and the writing is clear.

It's important to stress the novelty of the findings, which build upon previous studies from the same lab (upon a shallow look one might think that some of the conclusions were described before, but this is not the case). Despite the fact that this system has been studied in depth before, it remained unclear why and how germline genes are bookmarked by H3K36 in the embryo, and it wasn't known why germline genes are not expressed in the soma.

To study these questions Carpenter et al. examine multiple phenotypes (developmental aberrations, sterility), that they combine with analysis of multiple genetic backgrounds, RNA-seq, CHIP-seq, single molecule FISH, and fluorescent transgenes.

Previous observations from the Katz lab suggested that progeny derived from spr-5;met-2 double mutants can develop abnormally. They show here that the progeny of these double mutants (unlike spr-5 and met-2 single mutants) develop severe and highly penetrate developmental delays, a Pvl phenotype, and sterility. They show also that spr-5; met-2 maternal reprogramming prevents developmental delay by restricting ectopic MES-4 bookmarking, and that developmental delay of spr-5;met-2 progeny is the result of ectopic expression of MES-4 germline genes. The bottom line is that they shed light on how SPR-5, MET-2 and MES-4 balance inter-generational inheritance of H3K4, H3K9, and H3K36 methylation, to allow correct specification of germline and somatic cells. This is all very important and relevant also to other organisms.

(very) Minor comments:

-Since the word "heritable" is used in different contexts, it could be helpful to elaborate, perhaps in the introduction, on the distinction between cellular memory and transgenerational inheritance.

-It might be interesting in the Discussion to expand further about the links between heritable chromatin marks and heritable small RNAs. The do hint that the result regarding the silencing of the somatic transgene are especially intriguing.

Significance

This is an exciting paper which build upon years of important work in the Katz lab. The novelty of the paper is in pinpointing the mechanisms that bookmark germline genes by H3K36 in the embryo, and explaining why and how germline genes are prevented from being expressed in the soma.

Author Response

Reviewer #1:

Summary:

In this paper, the authors utilize CRISPR-Cas9 to generate two different DMD cell lines. The first is a DMD human myoblast cell line that lacks exon 52 within the dystrophin gene. The second is a DMD patient cell line that is missing miRNA binding sites within the regulatory regions of the utrophin gene, resulting in increased utrophin expression. Then, the authors proceeded to test antisense oligonucleotides and utrophin up-regulators in these cell lines.

Overall opinion (expanded in more detail below).

The paper suffers from the following weaknesses:

1) The protocol used to generate the myoblast cell lines is rather inefficient and is not new.

2) Many of the data figures are of low quality and are missing proper controls (detailed in points 5,7,10, 12, 13,14)

Detailed critiques:

1) The title needs to be changed. The method used by the authors is inefficient. The title should instead focus on the two cell lines generated.

We appreciate the reviewer’s comments: thanks to them, we have realized the focus of the manuscript should be in the new models we described and less in the methodology used to create them.

Originally, we wanted to share the problems we faced when applying new CRISPR/Cas9 edition techniques to myoblasts: our conversations with other researchers in the field confirmed that many were having similar problems. However, the reviewer is right in the fact that there are many ways around this problem. We do describe ours and we are working in a new version of the manuscript with additional data to characterize our new models further and where the method used to create them, although included, is not the main focus of the manuscript. In this new version we will change the title accordingly.

2) Line 104: The authors declare that the efficiency of CRISPR/Cas9 is currently too low to provide therapeutic benefit for DMD in vivo. There are lots of papers that show efficient recovery of dystrophin in small and large animals following CRISPR/Cas9 therapy. The authors should cite them properly.

Thank you for your appreciation. We have reviewed the literature again to include new evidences of efficient dystrophin recovery as well as other studies with lower efficiency.

3) Figures 1, 2,3, and 4 can be merged into one figure.

4) Figure 2A and 2B can be moved to supplementary.

5) Figure 2C and 2D are not clear. Are the duplicates the same? Please invert the black and white colors of the blots.

Thank you for your comments. We have inverted the colors of the blots and changed the marks used in figure 2C and 2D to clarify that duplicates are indeed the same sample, assayed in duplicates. We have also merged figures 1 and 4 and moved figures 2 and 3 to supplementary in this new version.

6) Figure 3: In order to optimize the efficiency of myoblast transfection, the plasmids containing the Cas9 and the sgRNA should have different fluorophores (GFP and mCherry). This approach would increase the percentage of positive edited clones among the clones sorted.

We think the reviewer may have misunderstood our methodology: we are not using a plasmid with the Cas9 and another with the sgRNA, we are using two plasmids, both containing Cas9 and each a different sgRNA. We did try to use two different plasmids, one expressing GFP and one expressing puromycin resistance, but we found out that single GFP positive cell selection plus puromycin selection was too inefficient. We could have tried with two different fluorophores, but we tested the tools we had in our hands first and were successful at obtaining enough clones to continue with their characterization, so we did so instead of a further optimization to our editing protocol.

7) Figure 4A: In the text, the authors state that only 1 clone had the correct genomic edit, but from the PCR genotyping in this figure shows at least 2 positive clones (number 4 and 7).

Thank you for your appreciation. As you said, we got two positive clones (as we also indicate in figure 3B) but we completed the full characterization of one of them (clone number 7= DMD-UTRN-Model). In the new version of the manuscript we explain this further.

8) Figure 4C: The authors should address whether one or both copies of the UTRN gene was edited in their clones.

Thank you for your comment. Both copies of the UTRN gene were edited in our clones. We have included this information both in the text and in the figure 4 legend.

9) Figure 4 B and D: The authors should report the sequence below the electropherograms.

Thank you for this correction, we have included the sequence under the electropherograms.

10) Figure 5B: This western blot is of poor quality. Also, the authors should specify that the samples are differentiated myoblasts. Lastly, a standard protein should be included as a loading control.

Thank you for your comment. Poor quality of dystrophin and utrophin western blots was the main reason to validate a new method in our laboratory to measure these proteins directly in cell culture (1) like an alternative to western blotting. Since then, the myoblot method has been routinely used by us and in collaboration with other groups and companies. We included the western blot as it is sometimes easier for those used to this technique to be able to assess a blot in which there is no dystrophin expression. As you pointed out, our samples were all differentiated myotubes, not myoblasts, and we have modified this accordingly. Thank you very much for pointing out this mistake

On the other hand, as described in the methods, Revert TM 700 Total Protein Stain (Li-Cor) and alpha-actinin were included as standards in dystrophin and utrophin western blots, respectively.

11) Figure 5E: We would like to see triplicates for the level of Utrophin expression.

We thank the reviewer for his/her recommendation, but we do not consider western blotting a good quantitative technique, we have included western blots to show the expression/absence of protein at the same level. We have included many more replicates than needed to show at the level of utrophin by myoblots. We acknowledge that western blotting is the preferred method for some reviewers, so in the new version of our manuscript we clearly indicate the value we give to each technique, being myoblots our choice for quantification.

12) Figure 6: A dystrophin western blot should be included to demonstrate protein recovery following antisense oligonucleotide treatment. Also, the RT-PCR data could be biased as you can have preferential amplification of shorter fragments.

Thank you for your recommendation but as we have explained before, myoblots have been validated in our laboratory to replace western blot for accurate dystrophin quantification in cell culture.

13) Figure 6A: Invert the black and white colors. The authors should also report the control sequences and sequences of the clones under the electropherograms.

Thank you for your suggestion, we have inverted the colors and added the sequences under the electropherograms.

14) Figure 6B: Control myoblasts should be included in figure 5C.

Thank you for this correction, we will include control myoblasts in the new manuscript version.

15) Figure S2A: Invert the black and white colors.

Thank you for your suggestion, we have inverted the colors.

Reviewer #2:

The work from Soblechero-Martín et al reports the generation of a human DMD line deleted for exon 52 using CRISPR technology. In addition, the authors introduced a second mutation that leads to upregulation of utrophin, a protein similar to dystrophin, which has been considered as a therapeutic surrogate. The authors provide a careful description of the methodology used to generate the new cell line and have conducted meticulous evaluations to test the validity of the reagents.

However, if the main purpose of this cell line is to perform drug or small molecule compound screenings, a single line might not be sufficient to draw robust conclusions. The generation of additional DMD lines in different genetic backgrounds using the reagents developed in this study will strengthen the work and will be of interest to the DMD field.

Thank you for your appreciation. We think that a well characterized immortalized culture, like the one we describe is sufficient for compound screening, as described in other recently published studies (2), (3). About the other suggestion, we have indeed used our method to generate other cultures for collaborators, but they will be reported in their own publications, as they are interested in them as tools in their own research projects.

Further, the future use of the edited DMD line with upregulated utrophin is unclear. The utrophin upregulation adds a complexity to this line that might complicate the assessment of screened compounds. In contrast, this line could be used to test if overexpression of utrophin generates myotubes that produce increased force compared to the control DMD line.

We think we may have not explained our screening platform well enough. Our suggestion is to offer our newly generated culture ALONGSIDE the original unedited culture: the original is treated with potential drug candidates, while the new one may or may not be treated, if these drug candidates are thought to act by activating the edited region (see an example in the figure below). In this case, the new culture will be a reliable positive control to the effects that may be reported in the unedited cultures by the drug candidates. We will make this clear in the new version of the manuscript.

Created with BioRender.com

In summary, while there is support and enthusiasm for the techniques and methodological approach of the study, the future use of this single line might be dubious and could be strengthened if additional lines are generated.

We share the reviewer’s enthusiasm for this approach, and we have included in the new version of the manuscript further characterization of this new cell culture that we think would demonstrate its usefulness better.

Reviewer #2:

The work from Soblechero-Martín et al reports the generation of a human DMD line deleted for exon 52 using CRISPR technology. In addition, the authors introduced a second mutation that leads to upregulation of utrophin, a protein similar to dystrophin, which has been considered as a therapeutic surrogate. The authors provide a careful description of the methodology used to generate the new cell line and have conducted meticulous evaluations to test the validity of the reagents.

However, if the main purpose of this cell line is to perform drug or small molecule compound screenings, a single line might not be sufficient to draw robust conclusions. The generation of additional DMD lines in different genetic backgrounds using the reagents developed in this study will strengthen the work and will be of interest to the DMD field.

Further, the future use of the edited DMD line with upregulated utrophin is unclear. The utrophin upregulation adds a complexity to this line that might complicate the assessment of screened compounds. In contrast, this line could be used to test if overexpression of utrophin generates myotubes that produce increased force compared to the control DMD line.

In summary, while there is support and enthusiasm for the techniques and methodological approach of the study, the future use of this single line might be dubious and could be strengthened if additional lines are generated.

Reviewer #1:

Summary:

In this paper, the authors utilize CRISPR-Cas9 to generate two different DMD cell lines. The first is a DMD human myoblast cell line that lacks exon 52 within the dystrophin gene. The second is a DMD patient cell line that is missing miRNA binding sites within the regulatory regions of the utrophin gene, resulting in increased utrophin expression. Then, the authors proceeded to test antisense oligonucleotides and utrophin up-regulators in these cell lines.

Overall opinion (expanded in more detail below).

The paper suffers from the following weaknesses:

1) The protocol used to generate the myoblast cell lines is rather inefficient and is not new.

2) Many of the data figures are of low quality and are missing proper controls (detailed in points 5,7,10, 12, 13,14)

Detailed critiques:

1) The title needs to be changed. The method used by the authors is inefficient. The title should instead focus on the two cell lines generated.\

2) Line 104: The authors declare that the efficiency of CRISPR/Cas9 is currently too low to provide therapeutic benefit for DMD in vivo. There are lots of papers that show efficient recovery of dystrophin in small and large animals following CRISPR/Cas9 therapy. The authors should cite them properly.

3) Figures 1, 2,3, and 4 can be merged into one figure.

4) Figure 2A and 2B can be moved to supplementary.

5) Figure 2C and 2D are not clear. Are the duplicates the same? Please invert the black and white colors of the blots.

6) Figure 3: In order to optimize the efficiency of myoblast transfection, the plasmids containing the Cas9 and the sgRNA should have different fluorophores (GFP and mCherry). This approach would increase the percentage of positive edited clones among the clones sorted.

7) Figure 4A: In the text, the authors state that only 1 clone had the correct genomic edit, but from the PCR genotyping in this figure shows at least 2 positive clones (number 4 and 7).

8) Figure 4C: The authors should address whether one or both copies of the UTRN gene was edited in their clones.

9) Figure 4 B and D: The authors should report the sequence below the electropherograms.

10) Figure 5B: This western blot is of poor quality. Also, the authors should specify that the samples are differentiated myoblasts. Lastly, a standard protein should be included as a loading control.

11) Figure 5E: We would like to see triplicates for the level of Utrophin expression.

12) Figure 6: A dystrophin western blot should be included to demonstrate protein recovery following antisense oligonucleotide treatment. Also, the RT-PCR data could be biased as you can have preferential amplification of shorter fragments.

13) Figure 6A: Invert the black and white colors. The authors should also report the control sequences and sequences of the clones under the electropherograms.

14) Figure 6B: Control myoblasts should be included in figure 5C.

15) Figure S2A: Invert the black and white colors.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 2 of the manuscript. Lee Rubin (Harvard University) served as the Reviewing Editor.

Summary:

While the paper by Soblechero-Martín et al., may present an ultimately useful method for modifying genes in skeletal muscle, the reviewers felt that, at the current time, the robustness of the methods and the amount of data presented were insufficient. The reviews below point towards additional experiments that could be done to improve this paper.

Author Response

Reviewer #1:

This study is an in silico analysis of data from the Cancer Genome Atlas (TCGA) on hepatitis B virus (HBV)-positive liver tumours and human papillomavirus (HPV)-positive cervical and head and neck tumours and association with viral load, genotytpe(s) and expression. It is unclear to me the rationale behind including two unrelated DNA tumour viruses in the study, especially as the number of HBV-positive samples is much less than for HPV. Overall the manuscript seems to be a validation of a bioinformatic tool rather than reporting significant research findings.

We strongly believe that a global summary of key oncoviral-associated tumors makes sense in this context precisely because of the fundamental importance viral genotype is already known to have. While HBV and HPV are of course quite different viruses, there is extensive clinical evidence that linking outcomes to specific viral genotypes and phenotypes is of great value, which we expand upon in our work via a working demonstration of ViralMine. For this reason we think it is crucial to present both virally related cohorts together as they support each other, demonstrate robustness our methods across completely different systems while allaying concerns about fine-tuning, and create a cohesive picture of the effect of viral genotype across the molecular landscape of two key onco-viruses. As the reviewer notes this does implicitly demonstrate the utility of ViralMine but we do emphasize that it also does uncover significant research findings.

Concerning the HBV/HPV sample sizes, in fact the number and percentage of infected HCC samples is substantially higher than that of cervical or head and neck HPV samples as discussed in detail on page 4 of our manuscript.

Use of the TCGA has allowed analysis of a reasonably large number of RNASeq data sets. However, once the authors drill down to individual genotypes, numbers become quite small, which may compromise some of the observation. For example, the large discrepancy between numbers of HPV16 (173) and 18(39)-positive cases makes it difficult to make firm conclusions about the significance of differentially expressed cellular genes for each set of cancers. Similarly, in Figures 4 and 6 they compare HPV18 (23 cases) with HPV45 (39 cases) and HPV18/45 coinfections (number not stated but likely far fewer).

While there is an imbalance in group size between HPV genotypes in the cervical cancer cohort, the test statistic used by the DESeq2 pipeline to identify differentially expressed genes does account for class imbalance and even in the most extreme case we have analyzed the dispersion parameter estimates are easily verified as accurate. In fact accurately inferring group-wise dispersion parameters given unequal group sizes is a well-known problem, and in any case this problem only becomes acute when one group becomes so small (~1 sample) that it becomes difficult to estimate its common dispersion parameter. That situation clearly does not arise here. Additionally, in Figure 4b, it should be noted that we are comparing ALL HPV co-infected cervical tumor samples (92 cases) against single-infection samples (193 cases), which the reviewer may find more confidence in and which is obviously statistically reasonable. Furthermore, while the comparison of cervical cancer HPV18 (n=10), HPV45 (n=9), and HPV18/45 coinfected (n=39) cases in Figure 6b does compare relatively small patient groups, the significant difference in neoantigen population TCR binding affinity is confirmed by a one-sided, non-parametric KS-Test and shown to be robust to subsampling, which formally demonstrates that the signal is not artefactual. Therefore from a statistical point of view the concerns raised about class imbalance and power are not fundamental and were addressed in the original manuscript draft. Thus, we believe we can completely address the reviewer’s concerns by:

In Figure 3a, Figure 4a and b, signify the group sizes (n=X) compared in the barcode plots to improve transparency in the contrasts, and additionally add group numbers to Figure 6a and b. Further, we will include a new supplementary figure demonstrating that a bootstrap resampling of the HPV group neoantigens to balance for group size validates that the difference in TCR binding affinity distributions is robust.

Much of the information that they derive from their analyses is not novel. For example, they report no preferential sites of HPV integration. Despite what they claim, quite a bit is known about HPV co-infection in cervical cancers and it is not uncommon but varies according to geographical regions, which was not a variable they used.

We acknowledge that other oncoviral survey papers have provided evidence of preferential integration (as we originally cited, as well as referenced in Dall et al. (2008), Zhang et al. (2016)). However, these and other previous characterizations of recurrent HPV integration do not attempt to organize these sites by either genotype or co-infection status, which was our explicit and stated aim, principally because they could not efficiently and accurately determine these parameters from in-situ tumor RNA. As we found no preference in integration along these axes of variation (which we acknowledged openly in the manuscript as being expected when using RNA rather than DNA), we deliberately chose not to present these results as a main finding and included them in supplemental results for the sake of completeness.

We also agree that HPV co-infection in cervical lesions is not per-say a novel finding, although to be clear most literature focuses on side-by-side infections of HPV with another virus (HHV, EBV, HIV, etc.), or uses the term to describe groupings of sub-variants or isolates under the same viral genotype header (Mirabello et al. (2016)). Additionally, most of the literature focuses on HPV co-infection in cervical neoplasia or high-grade lesions and cervical cancer risk (Chaturvedi et al. (2011); Senapati et al. (2017)) rather than assessing HPV co-infection in the tumoral tissue itself, post oncogenesis. As such, we believe that our approach at looking at in situ cervical tumor infections and the relatively high rate of HPV co-infections we observe does merit particular notice compared with previous studies. Furthermore, the analyses linking this cross-genotype co-infection phenotype with tumor gene expression, survival adjusted for major known clinical covariates, and tumor immunogenicity measures has not been reported elsewhere to our knowledge.

For HPV, viral exon-level RNASeq analysis is irrelevant because HPV gene expression is polycistronic and is subject to changes by random viral integration events in individual cases. Therefore, it is unlikely that general overall viral gene expression signatures will be diagnostic besides, from multiple studies we understand that what matters in cervical cancer is the level of expression of the E6/E6 isoforms/E7 oncogenes.

We agree that the post-transcriptional polycistronic nature of HPV expression makes it difficult to elucidate the effect of differing HPV gene-level expression on ultimate HPV gene translation and protein expression. However, our related yet distinct question here is on the effect HPV genotype and cancer type has on HPV gene transcriptional differences (as seen in Figure 7), so we believe we are within the limits of reasonable interpretation. Additionally, while E6 and E7 expression are well known to drive oncogenesis, it seems crucial to quantify the expression of these viral oncogenes across viral genotype and tissue type, which has not been done previously to our knowledge. Finally, even if we somehow accept that the average tumoral viral gene exon expression itself is best described as a random variable, which we do not, it remains to be explained why we observe and report persistent genotype-specific expression patterns across completely different cell-types.

The references chosen for the HPV part of the study are either rather out of date or not representative of the extensive literature.

We acknowledge that we have cited only a portion of the vast HPV-related cancer literature, so we have made an effort to include more recent surveys and studies as references.

Reviewer #2:

1) The authors comment that averaged infection phenotypes such as viral load or predominant genotype may be replaced by more granular measures, such exon-level viral expression or the ratio of expressed viral genotypes. In reality, viral expression, and the ratio of expressed viral genotypes, are still 'tumor averages' in the way that the authors have analysed them. HP associated tumors are heterogeneous, and without in situ analysis, it is hard to discern which transcripts are involved in driving the cancer phenotype, and which are found in associated precancerous tissue.

We concede that the viral genotypes quantified by our method represent a computed average measure across the tumor, as would any measurement of any quantity in a bulk sequencing assay. However, the information provided by the admixture of genotypes and exon-level viral expression does provide an additional measure of granularity over previous bulk measures, and allows additional analyses not explored previously to our work. To make a comparison, this criticism could identically apply to cell-type decomposition algorithms like Cibersort, which despite their problems and inherent limitations do provide insightful information. We agree with the reviewer that with more targeted in situ analyses would allow for a truly specific association of particular viral transcripts with tumor phenotype, and would serve as a useful validation of some of our results, but this certainly does not invalidate the tumor aggregated genotype and co-infection presence associations we present here. We agree with the reviewer that multiple biopsies would allow for intra-tumoral heterogeneity to be taken into account in our study, however no major public resources (e.g. TCGA) include such data and we believe that such an undertaking lies out of any reasonable scope of this work.

2) The authors use the term co-infection quite widely. For HPV, previous studies have shown that coinfection within cells in an individual cancer or neoplasia is rare, although independent infections by different HPV types can occur side-by-side. I expect something similar with HBV, although the study would need a higher level of analysis to establish this. The use of terminology, and the way in which data is interpreted, needs to be much more rigorous.

We agree with the reviewer that the use of ‘co-infection’ in this context is unclear, as co-infection on a cellular level with two different HPV/HBV genotypes is impossible to determine by bulk RNA sequencing analysis. We will clarify ‘co-infection’ as strictly a mixture of independent HPV infections contained in the same tumor tissue.

We will clearly define our meaning of ‘co-infection’ in the introduction as the aggregated mixture of HPV genotypes expressed in the tumor tissue (‘side-by-side’ infections), to remove ambiguity as to our cohort characterization.

3) Viral load is generally used in the field as a measure of viral genome or genome-fragment abundance. This is already a misuse of the terminology, as the term implies virus numbers, or even infectious virus numbers. Here the term is used to refer to viral transcript abundance. The authors need to say precisely what they're measuring, and need to be aware that they are measuring the average across a heterogeneous tumour, which may have areas of high grade neoplasia, cancer, and even low-grade neoplasia. My feeling is that the level of analysis is too great, given the uncertainties regarding the heterogeneous nature of tissue that is being analysed, and the different cells with different levels of viral gene expression that are most likely present.

We agree that as the reviewer frames it, our use of ‘viral load’ should be clarified as ‘viral transcript abundance’ as determined from the tumor RNASeq data in variance-stabilized units of log2 counts per million reads mapped across the viral contig. We do note however that it has been previously indicated that levels of viral transcripts do correlate well with virus numbers in infected tissue. Concerning the last comment of the reviewer, we wish to point out that our analysis goes no further in either analytic complexity nor in drawing inference from expression data than any published other study based on tumor bulk RNA-sequencing data. All samples will contain a mixture of cells and we emphasize that we are only measuring average signals, viral or host tumor specific, across this mixture.

To address these comments we will change all references to viral load to normalized viral transcript abundance, to remove ambiguity. We can once again emphasize that our conclusions hold only in a strict averaged sense.

4) Several of the figures don't obviously support the conclusions. For instance, it is not clear how the data shown in figure S2 supports the title of the S2 figure legend. Surely some statistical analysis is needed to support the conclusion stated in the legend. Given previous studies, I'm not at all convinced that the distribution of causative HPV genotypes is the same between SCC and Adenocarcinoma. An additional limitation of these large cancer association studies, comes from limitations in pathology diagnosis, which cannot always accurately distinguish borderline SCC/adenocarcinoma cases. With the large-scale transcriptional analysis, maybe the authors can use molecular information available in their samples to look at this.

As the reviewer points out, we agree the statistical evidence backing our claim of no association between cervical histology and HPV infection genotype or co-infection should be added. This calculation was actually carried out and only reported in the text, but we will amend the figure to include the results and apologize for this key omission. We also note in passing that we are not making any claims about ‘causative’ HPV genotypes for the respective subtypes, but rather much more conservative statements about association. Concerning the reviewer’s concern about the quality of the phenotypic data reported in the TCGA, we heartily agree but are unable to really do much else. Indeed, concerning the last interesting comment about utilizing molecular information in our samples to distinguish SCC/adenocarcinoma subtypes, we did not find reliable gene expression signatures which could be used to validate or correct the phenotypic results.

We will add in the spearman correlation rho and test significance results for the correlation between cervical cancer histological type and both viral phenotypes represented in figure S2.

5) The APOBEC analysis is quite rudimentary in the text, and does not discuss the different members of the APOBEC family. Similarly, the different effects of single and multiple HPV infections on the IFR3 responsive genes is poorly developed at the biological level, which most probably reflects the general way in which the utility of the approach.

We agree with the reviewer that our APOBEC expression analysis in the HPV+ cervical cohort could be more comprehensive, and therefore the interpretations of the results may be too far reaching. We believed the initial result to be of sufficient interest in the context of a very similar result from Zapatka et. al (2020), but concede it may make more sense as a supplemental result alone without additional evaluation or discussion of the greater APOBEC family. Additionally, the pathway analysis involving the differentially expressed genes from the co-infected and non-coinfected cervical tumors most likely should be moved to a supplemental result as well without further analyses to support the enrichment trends, following how we reported the HBV associated liver cancer co-infection DEG results (figure S5).

We will move Figure 3d to a supplemental figure, and limit our comments in the results to just an observation in reference to Zapatka et. al., and delete any associated interpretation. We will move Figure 3c to a new supplemental figure as well, and remove the suggestion of expanded antiviral activation in co-infected tumors.

Reviewer #2:

The title of the manuscript suggests a detailed analysis of cancers using in situ gene expression approaches, which aims to provide new insight into tumour heterogeneity and co-infection. The manuscript is in fact an analysis of viral transcription and the presence of cellular mutations in a collection of tumours associated with HPV and HBV infection. Much of the starting data for the analysis has been drawn from the TCGA database. It is a little unclear as to whether the authors are pitching this paper as a methodological development manuscript, but I think that this is what it is at its heart. The ability to deconvolute RNA sequencing data from virus-associated tumours is interesting, and could be widely used as a research tool. However, much of the manuscript is concerned with interpreting the data, and I think the interpretation goes well beyond what can feasibly be achieved from the analysis of transcripts in extracts of total tumour tissue. The authors term 'co-infection' most likely refers to heterogeneous mixtures of viral infected cells which are competing with each other in the tumour. In my view, the biological interpretations are not particularly useful at the level that they are presented, but could serve as the starting point for future research. This manuscript could be repackaged as a description of a new analytical tool, or the most exciting aspects drawn out with the addition of biological studies to explain what the transcriptional analysis may mean. This would be a complex process, and would be facilitated by focus on either HPV or HBV, as trying to extend conclusions to the two disparate virus families in one manuscript is probably unrealistic. Without any analysis of tumour tissue using in situ analysis or single cell sequence analysis, or a combination of the two, there is little new information that can be drawn regarding the biology of disease development. My suggestion would be to repackage this as an analytical methodology publication, rather than a biology discovery manuscript.

1) The authors comment that averaged infection phenotypes such as viral load or predominant genotype may be replaced by more granular measures, such exon-level viral expression or the ratio of expressed viral genotypes. In reality, viral expression, and the ratio of expressed viral genotypes, are still 'tumor averages' in the way that the authors have analysed them. HP associated tumors are heterogeneous, and without in situ analysis, it is hard to discern which transcripts are involved in driving the cancer phenotype, and which are found in associated precancerous tissue.

2) The authors use the term co-infection quite widely. For HPV, previous studies have shown that coinfection within cells in an individual cancer or neoplasia is rare, although independent infections by different HPV types can occur side-by-side. I expect something similar with HBV, although the study would need a higher level of analysis to establish this. The use of terminology, and the way in which data is interpreted, needs to be much more rigorous.

3) Viral load is generally used in the field as a measure of viral genome or genome-fragment abundance. This is already a misuse of the terminology, as the term implies virus numbers, or even infectious virus numbers. Here the term is used to refer to viral transcript abundance. The authors need to say precisely what they're measuring, and need to be aware that they are measuring the average across a heterogeneous tumour, which may have areas of high grade neoplasia, cancer, and even low-grade neoplasia. My feeling is that the level of analysis is too great, given the uncertainties regarding the heterogeneous nature of tissue that is being analysed, and the different cells with different levels of viral gene expression that are most likely present.

4) Several of the figures don't obviously support the conclusions. For instance, it is not clear how the data shown in figure S2 supports the title of the S2 figure legend. Surely some statistical analysis is needed to support the conclusion stated in the legend. Given previous studies, I'm not at all convinced that the distribution of causative HPV genotypes is the same between SCC and Adenocarcinoma. An additional limitation of these large cancer association studies, comes from limitations in pathology diagnosis, which cannot always accurately distinguish borderline SCC/adenocarcinoma cases. With the large-scale transcriptional analysis, maybe the authors can use molecular information available in their samples to look at this.

5) The APOBEC analysis is quite rudimentary in the text, and does not discuss the different members of the APOBEC family. Similarly, the different effects of single and multiple HPV infections on the IFR3 responsive genes is poorly developed at the biological level, which most probably reflects the general way in which the utility of the approach.

Reviewer #1:

This study is an in silico analysis of data from the Cancer Genome Atlas (TCGA) on hepatitis B virus (HBV)-positive liver tumours and human papillomavirus (HPV)-positive cervical and head and neck tumours and association with viral load, genotytpe(s) and expression. It is unclear to me the rationale behind including two unrelated DNA tumour viruses in the study, especially as the number of HBV-positive samples is much less than for HPV. Overall the manuscript seems to be a validation of a bioinformatic tool rather than reporting significant research findings.

Use of the TCGA has allowed analysis of a reasonably large number of RNASeq data sets. However, once the authors drill down to individual genotypes, numbers become quite small, which may compromise some of the observation. For example, the large discrepancy between numbers of HPV16 (173) and 18(39)-positive cases makes it difficult to make firm conclusions about the significance of differentially expressed cellular genes for each set of cancers. Similarly, in Figures 4 and 6 they compare HPV18 (23 cases) with HPV45 (39 cases) and HPV18/45 coinfections (number not stated but likely far fewer).

Much of the information that they derive from their analyses is not novel. For example, they report no preferential sites of HPV integration. Despite what they claim, quite a bit is known about HPV co-infection in cervical cancers and it is not uncommon but varies according to geographical regions, which was not a variable they used.

For HPV, viral exon-level RNASeq analysis is irrelevant because HPV gene expression is polycistronic and is subject to changes by random viral integration events in individual cases. Therefore, it is unlikely that general overall viral gene expression signatures will be diagnostic besides, from multiple studies we understand that what matters in cervical cancer is the level of expression of the E6/E6 isoforms/E7 oncogenes.

However, such an in silicio approach to quantify various aspects of virus-associated tumours could be a useful prognostic clinical tool in the future.

The references chosen for the HPV part of the study are either rather out of date or not representative of the extensive literature.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript. Margaret Stanley (University of Cambridge) served as the Reviewing Editor.

Summary:

The reviewers agree that the study is technically impressive but the biological data generated is not particularly novel and there are criticisms of the interpretation of the data. The study may have value as a methodological and bioinformatics tool.

Reviewer #3:

In this paper, Arcaro and colleagues investigate the relationship between bumps along the macaque STS and functional selectivity for faces. Through a series of analyses, they convincingly demonstrate a strong structural-functional relationship between face patches and these small sulcal bumps. They show that this correspondence outperforms functional probabilistic atlases, and does not result from functional specialization per se, as visually-deprived monkeys show similar anatomical folding patterns. As someone familiar with the field of vision and cognitive neuroscience, I can say that this paper is thorough, employs careful single-subject analyses, and I honestly do not have much to add to improve what is already a great paper.

Points:

For clarification, were the borders of each bump drawn by hand on the cortical surface (e.g. what's show in Figure 2B)? Saying so in the text will help future researchers replicate the identification process.

Monkey M3 looks odd; what do you think is going on there? I know there is individual variability, but the AL patch in that monkey seems atypical in its position in both hemispheres. For most monkeys it almost looks like you could mirror their STS from one hemisphere and predict relatively well their other hemisphere, but in M3 the AL patch doesn't look symmetric.

The previous point got me thinking, was data across hemispheres within a monkey collapsed before statistical testing? Are there hemispheric differences in bump volume or spacing? Apologies if I missed that in the text.

In the visually-deprived monkeys, were there any anatomical differences at all within the bumps? Volume differences? Thickness of the cortex that comprises a bump? If this is the topic of another paper and the authors excluded it purposely, I understand, but it might speak to how functional emergence interacts with existing structure (in this case the bumps).

Did I miss something, or is there really a reference to Julius Caesar's Gaul in the discussion? Is that what "Gallia" is referring to? I appreciate a deep historical reference (if that's what this is) but I'm worried that this will go over most readers' heads. Happy to leave it for poetic purposes, but just noting that it will likely be confusing.

Reviewer #2:

Summary:

Neuroimaging and electrophysiological experiments demonstrate a series of face-selective regions in the macaque superior temporal sulcus (STS). In normalised space, these regions partially align across individuals. The present report demonstrates that for some of these regions, local surface properties ("bumps") provide additional reliable information about the likely location of face-selective patches (in fMRI) and cells (in intracranial recordings). That pre-cursors of these bumps are identified both pre-natally, and in macaques reared with abnormal visual experience of faces, indicates that these bumps do not arise due to the normal development of face-selective cortical activity. Similar bumps are found in some other primates, although much of the relevant imaging and electrophysiology data that would help to assess homologies is not yet available.

General assessment:

This is a well-presented study that addresses a topic of ongoing interest with highly rigorous methods. On a narrow reading that holds close to the data, the paper offers an interesting observation that would seem to have mainly practical implications (e.g. in informing localisation for future electrophysiological work). In contrast, the effort to draw wider theoretical implications for understanding the visual organisation of STS seems to rely on unpicking the main observation that prompted the report in the first place, and on inferences and speculations that extend too far beyond the data that are reported.

Substantive points:

If "bumps" are the relevant physiological markers -- and demonstrating this is the thrust of most of the paper -- then it seems important to understand what a "bump" is. That is, what underlying properties or developmental processes are implied by the presence of a cortical bump, in contrast to regions with less prominent local curvature? The authors only very briefly review some possible mechanisms in the Discussion, and I felt more a complete exploration of this issue would have been useful.

However, having established a structure-function correlation empirically, at the same time the paper provides many indirect lines of evidence to suggest that this relationship may be tangential at best. As the authors note, "STS bumps are not sufficient to produce face selectivity in the absence of face experience". Nor are bumps necessary to produce face selectivity, given the apparent absence of bumps related to MF and AF. Further, the overlap between bumps and faces patches is variable over individuals, and incomplete: the bumps are large, and not entirely comprised of face-selective populations. The authors also note studies that reveal broadly similar tri-partite STS organisation of retinotopic responses, and of body and colour-selective patches. For example, images of bodies tend (in macaque fMRI) to activate regions that are adjacent to face patches, suggesting that there would be a similar anatomy/function relationship for this visual category too. Finally, the authors note that the kinds of physiological processes that are likely to produce bumps are too generic to produce a face-specific mechanism. The authors' speculation, in light of such considerations, is that anatomical bumps in STS are in fact the indirect signals of three distinct, coherent, and complex visual areas that may contribute to a range of visual processes. The main difficulty with the manuscript, as I see it, is that while these wider possibilities are what give the paper the potential to engage a broad neuroscience audience, they are simply too far removed from the actual observations that are reported here. Substantial additional evidence would need to be mustered to support the (admittedly interesting) picture of arealisation in STS that the authors paint. Without such evidence, what remains is mainly a structure-function observation that is interesting, and perhaps practically useful for further studies, but with uncertain theoretical implications.

Reviewer #1:

This paper reports a correspondence between structural markers, convexities ("bumps") along the superior temporal sulcus (STS), and face-selective patches in the macaque inferior temporal cortex. They localized three face patches with fMRI and each of these face patches overlapped with one of three bumps. These bumps were also present in monkeys that lacked face patches because of being reared without exposure to faces. These data provide some evidence for a correspondence between structure and function in inferior temporal cortex in macaques, in line with recent evidence for a link between structure and function in the temporal lobe of humans. This is interesting work showing novel data on a potential correspondence between structure and function in macaque temporal cortex. They examined, for monkey studies, a relatively large number of subjects and employed two functional measurements, fMRI and multi-unit recordings. However, I have some concerns regarding the correspondence between the face patches and the anatomical structure that need to be addressed.

Main comments:

1) The authors employed an automatic procedure to compute the convexity of the pial/white matter, which is excellent because it is objective. However, I found it difficult to differentiate neighboring bumps in some of the animals (Figure 2 S1). One reason for this is the way Figure2 S1 was made, showing the bumps with different colors that occlude to some extent the underlying convexity map. The authors should show the convexity map for each monkey and then in a separate panel show the identified bumps, so that one can judge the correspondence between the convexity map and the bumps. Also, the group average data shown in Figure 2C look not very convincing to me: I find it difficult to differentiate the posterior from the middle bump: it looks like one long continuous convexity instead of two with a clear border in between. This could be due to the averaging across monkeys. That is why Figure 2S1, that shows the data of the individual monkeys, is important but that figure needs to be improved by showing the convexity maps alone (see above).

2) The overlap between the bump surfaces and the patches depend on how the two are defined. As said above, I found it difficult to identify the individual bumps. The surface area/size of a face patch depends on the statistical threshold (and number of runs etc) that is used to define it and thus is arbitrary to some extent. These two factors make it difficult to evaluate the degree of overlap between patches and bumps and to interpret the DICE overlap analysis. The authors should address this by using several thresholds to define the face patch surface and examine how this affects the DICE outcome and analyses using centroids.

3) Because the face patches appear to be a (in some cases) small part of a bump and its location can vary within the bump, how predictive is the bump then about the location of the face patch? The correspondence between structure and function appears to be rather coarse: I have the impression from the comparison of the centroids of the bumps and face patches (Figure 4) that there is a reasonable correspondence between ML and the middle bump, but that it is weaker for PL and AL. Furthermore, it is highly variable amongst animals. For instance, in M3, face patch AL appears to lie in between the middle and anterior bump. This suggests that the bumps might not determine the presence of a face patch but that perhaps the presence of a bump and a face patch are unrelated mechanistically.

4) The authors' work ignores the most anterior face patch, AM, which is located outside the STS (as in fact also PL typically is (in fact, also in the present study)). It has been suggested that AM is important for face identification, having a high tolerance for identity-preserving transformations such as viewpoint (see the work by Freiwald and Tsao), and thus is difficult to ignore. How does AM fit into the proposed correspondence between STS bumps and face patches?

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Summary:

The reviewers agreed that the paper reports an interesting finding: a potential correspondence between structure and function in macaque temporal cortex. However, they also noted that this correspondence was only partial and variable across individuals. Furthermore, the reviewers were unsure of the broader theoretical implications of this finding.

Reviewer #2:

In this work the authors seek to disentangle the reason for a well-documented effect regrading reduced model-based tendencies among high compulsive individuals. The authors collected behavioral and EEG data from ~200 participants performing a two-stage decision task. Main findings show a latent compulsivity factor is associated with weaker transition-type effects at the task's 2nd stage. Specifically, high compulsive individuals show smaller reaction-times and parietal-occipital alpha-band power differences between uncommon and common transitions. These findings are interpreted as evidence in favor of less accurate model as a reason for reduced deployment of model-based strategies in compulsive individuals. Authors further note reduced theta power for compulsive individuals during 1st stage choice.

I am generally very impressed with this manuscript. I think the authors are addressing an important question that has a lot of promise in pushing the field forward. I also believe that given the number of participants, this is a relatively well powered EEG and behavioral study. Yet, I have one major concern as detailed below:

The authors relay on 2nd stage effects to estimate to what extent individuals are more or less aware of the transition structure (i.e., to what extent individuals are surprised by an uncommon state, or unsurprised by the common one). However, unlike Konovalov & Krajbich, 2020 who used a mouse tracking procedure to capture participants' 2nd stage expectation, both the RT and alpha band scores might be confounded due to 1st stage choice strategy. Individuals with stronger deployment of model-based strategies in the 1st stage tend to get more often to the best 2nd stage choice by means of a common transition. In contrast, the choices made by MF individuals at the 1st stage will not direct them more often to the best 2nd stage option by means of a common transition. This means that for a MF individual, the overall value difference for the two options offered at the 2nd stage will be similar in common and rare transitions, while for a MB individual the value difference will be higher in common vs. rare transitions. This is even when both MB and MF agents have a perfect knowledge regarding the task transition structure, and are equally surprised by an uncommon transition. Since the 2nd stage decision is easier on average on common vs. rare transitions for MB agents, they should also exert stronger transition effects compared with MF agents on 2nd stage estimates. One such effect might be greater alpha-band on rare transitions reflecting a greater mental effort (as the authors note). Also, when the decision is easier due to larger value difference, shorter RTs are to be expected (e.g., Pedersen et al., 2017 on pbr; Shahar et al., 2019 on plos-cb). This means that transition effect on both alpha-band and RTs is expected due to the use of MB strategies in the 1st stage, even if transition probability is perfect. Indeed, the authors report lower MB deployment at the 1st stage for compulsive individuals, which is in-line with their weaker transition-related effects on the 2nd stage.

Reviewer #1:

In this report, the authors test a hypothesis about the nature of high-level ("model-based") vs. low-level ("model-free") learning across the spectrum of behavioral compulsivity. Prior literature has suggested that high-compulsive individuals have a deficit in either forming a model of the world, or implementing that model due to competition from learned low-level action-outcome tendencies. This report tested a large number of participants with concurrent EEG (N=192) across a range of compulsivity on the well-known two-step reinforcement learning task.

The authors note that they "replicated prior work in findings that individual differences in compulsivity and intrusive thought ... were associated with reduced model-based planning" with analyses of accuracy (pg. 8). Analysis of RT revealed a novel effect of compulsivity on model-based planning, which was replicated using archival data of the same task. E-phys findings indicated that the candidate biomarkers of control in P300 and frontal midline theta were unrelated or not specifically related to model-based planning deficits in compulsivity, respectively (more on this below). However, the novel biomarker of posterior alpha power during the transition period was indeed linked with model-based planning deficits in compulsivity. This is novel.

This report is extremely well motivated by prior literature, it is very well written, and very well executed. Supplemental controls for age and IQ, tests of the specificity of EEG effects with compulsivity, and tests of the specificity of this compulsivity dimension on dependent measures in relation to associated personality variables (e.g. anxious depression & social withdrawal, also raw item measures) all work together to bolster the conclusions. This is a very carefully presented report.

Despite these virtues and advantages, the take-home message that I leave with is that EEG is not ideally suited for revealing the nature of compulsivity on model-based planning. P300 was irrelevant, frontal theta was possibly indirectly related (see below), and only posterior alpha was indicative of the compulsivity-related findings revealed in the behavioral analysis. This is unfortunately the least useful assessment of cognition used here, as it reflects the lowest level of control or decision making amongst these EEG measures. This perceptual effect is likely more of a consequence of the behavior than a candidate mechanism underlying it. This conclusion unfortunately diminishes the utility of these findings.

Regarding theta: Theta power and compulsivity were related to RT change, and they were related to each other, even though theta was not related to model-based planning (presumably tested via accuracy / choice). Although these patterns are carefully interpreted, it isn't perfectly clear how these were tested and I suspect there may be more that could be tested / inferred here. First, theta may still be related to the latent feature of "model-based choice" even if it is not significant due to the manifest measure based on choice patterns. This requires some careful unpacking of semantics and what latent constructs can be inferred from which manifest variables, but it is always a good idea to question what a single measure can infer about complex cognitive states. Second, taking this theoretical issue and including a methodological point, the single trial theta-RT relationship may still be altered by compulsivity even if theta power is not. Power and power-RT correlations have been presented as different measures of control that can be differently affected by a host of variables. This could presumably be tested by a thetaRTcompulsivity interaction, and could be visualized as a correlation between the individual theta*RT beta weight (Y-axis) with compulsivity on the X-axis.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Summary:

The authors aimed to disentangle the processes underlying compulsive individuals' difficulties forming models of the world, or implementing such models due to competition from lower-level action-outcome tendencies. To this end, they obtained behavioral and EEG data from ~200 participants performing a well-established two-step reinforcement learning task. The authors note that they "replicated prior work in findings that individual differences in compulsivity and intrusive thought ... were associated with reduced model-based planning" with analyses of accuracy. RT analyses revealed a novel effect of compulsivity on model-based planning, which was replicated using archival data of the same task. EEG findings indicated that the P300 and frontal midline theta, both well-established measures of cognitive control, were unrelated or not specifically related to model-based planning deficits in compulsivity, respectively. Posterior alpha power during the transition period, a novel marker, was linked with model-based planning deficits in compulsivity.

Reviewer #4:

The author investigated the relationship between spontaneous (SR), peak (PR), and steady-state (SS) firing rate in sensory neurons (across modalities) by extracting data from approximately ten studies, published between 1928 and 2017. The relationship between SR, PR, and SS is surprisingly simple: SS =sqrt(PRxSR). The author concludes that this is a universal law of sensory adaptation.

General Assessment: The claims of universality are not supported by the analysis.

Major comments: The primary claim of a universal law of adaptation is based on a meta-analysis of fewer than 20 several hand-picked papers. This is contrary to good scientific practice of meta-analyses. To truly assess the universality of the rule, the author should define a time period, a set of journals, and possibly some other criteria for exclusion/inclusion and then study the relationship across all publications that meet these criteria. Without such a clearly defined approach, the reader cannot know whether the examples were cherry-picked.

The comparisons of (extracted) experimental data and the model are entirely "by eye"; statistical analysis is lacking.

Even within the chosen sample, universality is clearly a step too far and the author's explanations of why the universal law fails are not particularly convincing ("the visual system is complex"). There may be something to the claim that the law only applies "in the absence of interaction from others cells in the neural circuitry", but this should be part of the study (i.e investigate only those papers that studied neurons that were isolated in this sense), not as an ad-hoc explanation of discrepancies.

The manuscript only states the "universal law" but leaves an explanation to future work. This is unsatisfactory. Detailed neuronal models exist that explain adaptation (e.g. in terms of the opening of potassium channels). These alternative biophysical explanations need to be considered.

Reviewer #3:

This manuscript by Wong proposes that steady state responses to a constant sensory stimulus-the responses observed after adaptation-are well predicted by a simple relationship between the spontaneous firing rate and the peak firing rate, namely their geometric mean. The author provides evidence extracted from measurements made in previous published studies, across species and modalities.

The paper presents a simple and somewhat interesting observation. However, it is difficult to accept the claim and support publication for several reasons:

1) The comparisons between the predicted and measured responses are entirely qualitative, and there is no alternative model considered. The predictions in Table 1 are pretty good but in many cases the arithmetic mean works reasonably as well (unless peak rates are very high). The steady state will lie somewhere between peak and spontaneous. Where is the quantitative evidence that the geometric mean is better than an alternative? What other relationships might better map the quantities on to each other?

2) There is little context for the observation: if true, why should we care that Eq 1,2 hold? The discussion hints that the observation is consistent with theoretical principles. If this were laid out in a compelling way, it would greatly increase the impact and relevance of the observation. As it stands, the observation has little context. The implications are unclear.

3) It is not clear how the studies considered here (i.e. where the data came from) were chosen. Surely there are many studies of sensory responses to the constant stimuli. How did the author choose this small subset (~10 studies)? For a 'universal' law, one would want to see many studies considered. In addition, in the studies considered here, the values were extracted in an ad hoc manner.

4) The discussion points out many cases in which the rule does not apply (whenever neurons are embedded in a circuit as opposed to being primary sensory neurons). This limits the appeal of the proposal, unless one can provide theory/explanation for why such a relationship should hold in the periphery but not in more central structures.

5) Previous work has dispelled the notion of a steady state response, arguing that responses continue to decrease with adaptation duration, following a power law dependence (Drew and Abbott, 2006, J Neurophysiol 96: 826). If so, the rule proposed here is unlikely to hold across adaptation duration, again suggesting they are not broadly applicable.

Reviewer #2:

This paper proposes a universal law of adaptation that occurs during sustained sensory stimulation. The law states that the sustained response of sensory afferents equals the square root of the product of the spontaneous and transient, peak response. The author shows several examples of previously published results to support the claim, some dating back to the seminal studies by Adrian. The author states that the law can be derived from a theory of sensory processing but does not provide further information on this (he refers to a publication in preparation).

This is interesting work and the paper is well-written. However, I am not convinced by this claim of a universal law of adaptation. First, it does not appear to be universal, and, second, the empirical data that are provided to support its universality are not convincing yet.

1) The law is not universal: in his Discussion, the author lists exceptions to the rule, in the visual system, auditory system and even for somatosensory afferents. Explanations are given of why the law does not hold in some of these cases, but the exceptions show that the law is not universal. Even when it is not universal, the theory should be able to predict in which cases it holds and when it does not hold.

2) I am not convinced by the evidence presented in Figure 2. In several instances, the slope of the relationship between the log peak and log sustained (steady state) activity does not seem to be equal to the predicted 1/2: e.g. in panels b and c .The author should have computed the slope and tested whether it was 1/2.

Reviewer #1:

This study reports an interesting observation, namely that the firing rate after sensory adaptation appears to be equal to the geometric mean of the peak firing rate and the spontaneous firing rate. However, there are concerns about the theoretical motivation and general empirical evidence supporting this observation.

1) Theoretical motivation: still unclear even after discussion, although we are told it exists. "The derivation of Eqs 1-2 of will be the subject of a later publication."

2) Is this relationship supposed to hold for each stimulation or on average? The author seems to be only working with averages.

It is not clear why exactly these (quite old) studies were selected. What was the criteria to include these studies in the meta-analysis? A number of exceptions are later discussed however.

Alternative of in-depth analysis of existing datasets requested from other authors was explicitly not done. Could also address the trial-wise validity.

"Not only does adaptation show time-varying changes in firing rate, but the variability makes it difficult to know exactly which value to choose. Averaging the data is not feasible without extracting a large number of data points, and this was not possible from noisy images. As such, with the exception of two studies, ... a visual estimation of the average activity in the final portion of the adaptation curve was used."

The error introduced by visual estimation remains unknown.

3) Counter-example in one of the few easily accessible papers, in the ferret, reference 16 (https://pubmed.ncbi.nlm.nih.gov/22694786/#&gid=article-figures&pid=fig-6-uid-5 ). Another counterexample appears in Fig 8 of this randomly chosen paper, although maybe the mechanoreceptor of the cricket doesn't count due to some exclusion criterion, since it is an interneuron. (https://journals.physiology.org/doi/full/10.1152/jn.1997.77.1.207?url_ver=Z39.88-2003&rfr_id=ori:rid:crossref.org&rfr_dat=cr_pub 0pubmed)

4) The law doesn't hold for a number of exceptions, this is not announced until the discussion (missing in abstract).

5) The discussion ignores existing literature on information content and possible function of the sustained response, and of adaptation in general (e.g. gain control).

6) Introduction: failure to cite recent reviews on this topic, e.g. "has been repeated many times.... More modern methodologies..." cites nothing after 1970s.

7) At which time point is the relationship supposed to hold true? What happens when stimulation time becomes very long? Does the firing rate reach steady state in all of these studies?

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 2 of the manuscript.

Reviewer #3:

This study provides very informative trends regarding long-term (~4-month) recording with Neuropixels probes in chronically implanted, freely moving rats. This is accomplished by recording across many animals (n = 18) and many recording locations and analyzing the number of single (and multi) units that can be automatically isolated as a function of time since implant, recording location, and other features (e.g. shank orientation). The authors perform these experiments with a modular system that allows the implanting of multiple probes simultaneously in a single rat (here they mostly implanted 1 probe, sometimes 2, once 3) and that allows the removal of probes for re-use in another animal, both of which are also valuable contributions. The analysis of neuron yield is framed in terms of a sum of 2 decaying exponentials model (an initial fast decay of one subpopulation of neurons followed by a slower decay of the remainder) that the authors fit to find the primary features determining neuron yield. The major trends they report include: substantially better yield over time in regions anterior to the bregma and ventral to the most dorsal 2mm of the brain surface. They also show that re-used probes perform essentially as well as new probes in terms of noise and unit quality (e.g. average unit amplitude), and also neuron yield (at least for medial frontal cortex, but see below).

Major comments:

The results averaged over many animals and the model are good for extracting the major trends, but there are hints of significant and important variability across animals or probes. Points 1-3 are about this variability, potential sources of variability, and displaying the variability whether or not potential causes can be found.

1) The results shown in Figure 2, especially the averages in Figure 2H,K, indicate severe losses in unit yield over time for probes implanted posterior of bregma and electrode sites in the dorsal 2mm of the rat brain. However, Figure 2B shows at least one animal (open circles) for which high neuron yield was obtained in motor cortex and dorsal striatum for at least 4 months. First, is this from 1 or 2 probes? Whether it is from 1 or 2 probes, the stability of the recording over time from day 1 is much greater than the other animals, and much better than what is expected from Figure 2H. Is the preservation of units over time for this animal due to the stability of units in dorsal striatum (presumably mostly >2mm below the surface) or also motor cortex?

2) There are some additional potential causes that could also account for yield differences, and one of these is age of the animal at the time of implant. The authors should list age at implant in their table in Figure 4-supplement 1. The authors should display yield over time as a function of age at implant, and also try adding age as one of the regressors for their model of neuron yield.

3) Another potential cause is whether the probe is new or reused. The authors showed that probe re-use did not result in statistically different yield for the medial prefrontal cortex. But is this also true for the other brain regions? Does the data in Figure 2 include implants of both new and re-used probes, or only new probes? The authors should try to add whether the probe was new or re-used as a regressor in their neuron yield model.

Regarding points 1-3, whether or not it is possible to add age or probe newness as regressors in the model, the authors should create a supplementary figure that shows the single unit yield curves as in Figure 2A-C for all probes in all animals: one panel per major brain region (e.g. splitting motor cortex from dorsal striatum from ventral striatum), with one curve per probe. There should be a legend for each panel that gives the (AP,ML,DV) coordinates of the approximate midpoint of the probe's location within that brain region. The legend should also indicate for each probe/curve: the animal, age at time of implant, probe newness, probe tip depth, estimated number of electrodes recorded from in that region, and shank orientation. This will repeat some pieces of information that's in the tables, however it's very useful to see all this information together in a form that would be very valuable for readers, especially experimenters who may want to record from some of the more posterior and dorsal areas. The information that could be gleaned would include knowledge of the variance in yield over time across implant attempts, so they could see if, say, 1 of 3 attempts to implant in a given area may give very good long-term yield.

4) It is stated starting on Line 172 that "The relative number of units corresponding to the fast- and slowly-decaying subpopulations did not significantly vary across brain regions along either anatomical axis, nor did the rate of decay of the fast population (Figure 2--supplement 3). This suggests that the rapid decline in yield observed in the days after surgery may be due to a process that is relatively uniform across brain regions."

The support for this statement can be seen in the indicated Figure 2-supplement 3. On the other hand, the point is made (and shown in Figure 2-supplement 4) that there is no loss of units in mPFC over time. This is apparently at odds with the Line 172 statement and model assumption of a fixed fraction of fast-decaying units. Was a model tried in which alpha varies with location? If the Line 172 statement is ultimately kept, there should at least be a comment made there that the most anterior, ventral regions appear to differ from the model's assumption/interpretation.

Reviewer #2:

In this paper, the authors report a device that can be used to implant and later explant Neuropixels probes in freely moving rats. The device consists of an adaptor, an internal holder and an external chassis. The chassis protects the probe, is attached to the animal's head via adhesive cement and acrylic. The internal part can be explanted at the end of the experiment, allowing the NP probe to be re-used.

The work builds on existing technology in important ways: the authors examined the long-term yield across different brain regions, they more extensively assessed the feasibility of probe reuse compared to previous work, and they evaluated probe performance over a long period of time and also after explanation (measuring the input referred noise of explanted probes in saline). It was also impressive that they used a cohort of 18 rats to evaluate performance of both the animals and the probe, and that they were able to implant up to 3 NP probes at a time. Because of the importance of using freely moving animals in Neuroscience research, and the differences between rats and mice that necessitate modifications on existing technology, this paper is timely and likely to be very useful to a sizeable group of researchers. My suggestions are aimed at furthering the usefulness of this "Tools and Resources" paper for investigators who wish to use this important technology.

At the moment, the majority of the paper seems aimed at evaluating the performance of the device as a function of time, depth and location. This performance evaluation was useful, very carefully done, and makes important points that aid in the interpretation of other papers (such as the unusual stability of recordings in mPFC reported in previous papers). Nonetheless, readers are likely interested in the paper because they wish to make and implant the device in order to benefit from the scholarly analysis done here. The manuscript does contain very helpful technical details, but these are hard to find and are not front-and-center in the main text. For instance, the material from the "Neuropixels implant procedure" is really helpful and would be critical for anyone who wants to use this technique. But at the moment, that information is in a google doc linked from the associated GitHub, a long way from the main manuscript. This information should be in the main manuscript, either in Results or Methods. Also use of consistent nomenclature across documents would help a lot. I believe the part referred to as the "chassis" in the main text is referred to as the "external" on the google doc with the instructions. Similarly, the part referred to as the "internal" in the google doc is called an "internal holder" in the manuscript.

A reader hoping to use the device might also benefit from more information on the grounding procedure. The text in the "Implantation" section of the methods was helpful, but more information would be useful, such as where on the probe the ground wire should be connected and how one should fix the grounding wire (tapping the wire and covering with Metabond?). Also, it would be nice to know how one should protect the grounding wire from being touched by the animal. Figure 6 in the google doc protocol is really helpful and should definitely be in the main manuscript. An additional figure showing how to connect the wire to the ground during the surgery would be quite useful. Finally, are the craniotomy and durotomy necessary for grounding? Could one simply connect the grounding wire to a couple of screws on the skull?

Reviewer #1:

This manuscript presents new techniques for obtaining chronic recordings using multiple neuropixel probes in rats. The resources, I imagine, will be of high value to the neuroscience community at large. They also address short and long terms unit stability, probe recovery and impact of the probe on behavior. I have only a few minor comments.

I understand the authors rationale to avoid manual curation but there have been reports of inconsistencies in the identification of units across different sorters. Did the authors consider comparing their kilosort unit identification with manual curation or another sorting software?

The authors speculate in the discussion about the possible reason for the slow loss of units. It wasn't quite clear to me however, what types of changes might improve this loss?

Figure 2 is perhaps one of the most informative findings but I wonder how applicable this will be to future probe iterations. Do the authors have a hypothesis for what features of the probe might contribute (or not contribute) to the long term loss of units?

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 2 of the manuscript. Lisa Giocomo (Stanford University School of Medicine) served as the Reviewing Editor.

Summary:

This manuscript presents new techniques for obtaining chronic recordings using multiple neuropixel probes in rats. The study provides very informative trends regarding long-term (~4-month) recording with Neuropixels probes in chronically implanted, freely moving rats. This is accomplished by recording across many animals (n = 18) and many recording locations and analyzing the number of single (and multi) units that can be automatically isolated as a function of time since implant, recording location, and other features (e.g. shank orientation). The authors perform these experiments with a modular system that allows the implanting of multiple probes simultaneously in a single rat (here they mostly implanted 1 probe, sometimes 2, once 3) and that allows the removal of probes for re-use in another animal, both of which are also valuable contributions. The work builds on existing technology in important ways: the authors examined the long-term yield across different brain regions, they more extensively assessed the feasibility of probe reuse compared to previous work, and they evaluated probe performance over a long period of time and also after explanation (measuring the input referred noise of explanted probes in saline). Because of the importance of using freely moving animals in Neuroscience research, and the differences between rats and mice that necessitate modifications on existing technology, this paper is timely and likely to be very useful to a sizable group of researchers.

Author Response

Reviewer #1

This paper investigates the role of Lhx6 and other transcription factors in the development of GABAergic neurons in the hypothalamus. The authors report that a small fraction of hypothalamic GABAergic neurons express Lhx6 and further depend on this expression for their survival. Dlx1/2, Nkx1-1 and Nkx2-2 define 5 subpopulations and at least three of these populations depend on these TFs to maintain Lhx6 expression. A strength of the paper is the multimodal analysis and the fact that descriptive assays like RNAseq and ATACseq are followed up with specific knockouts of candidate transcription factors. However, the relationships between the developmental populations identified and adult subtypes of hypothalamic neurons remain unclear. Although the results will surely interest those already interested in hypothalamic development, it is not clear that broader developmental or functional principles have been identified. The authors make much of the fact that the identified populations do not resemble forebrain interneurons defined by Lhx6 expression, but it is not clear why this should have been expected. Many developmental transcription factors are utilized both across diverse brain regions and across tissues outside of the brain. Perhaps the emphasis of this point could be tempered.

We thank the Reviewer for his/her comments, although we respectfully but strongly disagree with the statement that “it is not clear that broader developmental or functional principles have been identified”. This manuscript aims to provide a broad overview, and by no means exhaustive, an overview of the molecular mechanisms controlling the development of hypothalamic neurons that express Lhx6. Although these neurons comprise only approximately 2% of all hypothalamic GABAergic neurons, they are highly heterogeneous at the molecular level. Using traditional methods such as histology and more recent methods such as scRNA-Seq, we have not found a selective marker of hypothalamic Lhx6+ neurons other than Lhx6 itself. However, we have found multiple spatially distinct domains in hypothalamic Lhx6+ neurons that express specific sets of transcription factors such as Dlx1/2, Nkx2-1, and Nkx2-2, as we and others have previously observed in developing hypothalamic nuclei.

In addition, a subpopulation of these neurons later gives rise to a subset of Lhx6+ neurons of the zona incerta, which have been previously shown by us to promote sleep. Unlike all previously described sleep-promoting neurons, Lhx6+ zona incerta neurons are only one of few neuronal subtypes that can regulate both REM and NREM, which likely reflects molecular and functional heterogeneity among these neurons.

Our thus manuscript speaks to both broader developmental principles by demonstrating the molecular heterogeneity of hypothalamic Lhx6+ cells that arises through the action of diverse transcriptional networks, and broader functional principles by identifying developmental networks that potentially control the specification, differentiation, and survival of sleep-promoting neurons.

We believe that there are several compelling reasons for including a direct comparison of hypothalamic and cortical Lhx6 neurons, both of which arise from different regions of the forebrain (or secondary prosencephalon, if using the prosomere model). First, the role of Lhx6 in development of telencephalic interneurons is extensively studied, with 72 publications ((Pubmed: Lhx6 AND development AND (cortex OR telencephalon OR interneuron), accessed 7/27/20), and virtually all our understanding of how Lhx6 controls neuronal development has been acquired from this work. It is thus critically important that we directly connect our findings to a prior understanding of the mechanism of action of Lhx6.

Second, current work in the field of developmental neuroscience in general, is heavily focused on studying telencephalic development. It is very much an open question, however, whether telencephalic structures are themselves particularly good models for studying the development of physiologically vital brain regions, such as the hypothalamus. By identifying many key differences in the function of this extensively studied gene between Lhx6+ MGE-derived neural precursors and hypothalamic Lhx6+ neurons, we establish some important caveats in generalizing studies of telencephalic development even to nearby forebrain structures.

Nonetheless, we certainly agree with the Reviewer that the organization and clarity of the manuscript can be substantially improved. To this end, we have revised the manuscript carefully to improve clarity, focusing on its key findings.

The presentation of the manuscript could be improved by clarifying the relationships between embryonic and more mature structure within the hypothalamus. For example, It is extremely hard to follow the evidence split across figures 5, S6 and S7 for parsing the cell groups by TF expression.

We have revised the manuscript carefully to improve clarity. We have moved scRNA-Seq analysis of postnatal Lhx6-expressing neurons as Fig 3, and embryonic Lhx6-expressing neurons as Fig. 4, to improve the overall flow of the manuscript.

The ATAC seems to be used only to bolster the impression that the populations identified by gene expression are different. The description of footprinting seems to imply an effort to analyze binding sites for specific factors (e.g. to identify targets of the TFs studied), but the statistical approach employed and even the conclusions reached are not fully spelled out. As such, this part of the study is underdeveloped or not well enough described.

Specific details of the ATAC-Seq analysis are extensively described in the Method section, with each bioinformatics package (and package version) listed and, when non-default parameters were used, parameters clearly stated. However, we have added details of the statistical approaches used for data analysis to the revised manuscript.

There is little use in conducting ATAC-Seq analysis without a matched RNA-Seq dataset, as changes in peaks (open chromatin regions) do not necessarily correlate with changes in gene expression levels. By integrating ATAC-Seq data with differential gene expression obtained using RNA-Seq, we have been able to identify changes in motif accessibility and candidate transcription factor footprinting that to identify changes in gene regulatory networks that control Lhx6 expression in both hypothalamus and cortex. We have revised the manuscript to make this clearer, and better explain the findings of this part of the study.

Reviewer #2:

Kim and colleagues used a combination of state-of-art sequencing and mouse genetic tools to study the mechanisms that control the development of a subset of GABAergic neurons in the developing hypothalamus.

While neurodevelopment of GABAergic neurons has been extensively studied in the developing telencephalon, little is known about their counterparts in the developing hypothalamus. The authors focused their work on a specific subset of GABAergic neurons that express the LIM homeodomain factor Lhx6. Lhx6 is a master regulator of GABAergic neuron differentiation, specification, and migration in cortical interneurons. In contrast, Lhx6-expressing neurons make up only 2-3% of GABAergic neurons in the hypothalamus. The authors' previous work demonstrated that these neurons play a critical role in sleep homeostasis. Therefore, understanding how these neurons are formed and maintained is of great importance.

The authors show that hypothalamic Lhx6 is necessary for neuronal differentiation and survival. Furthermore, by profiling and comparing multiple RNA-seq, scRNA-seq, and ATAC-seq datasets, they were able to identify three transcription factors Nkx2.1, Nkx2.2, and Dlx1/2 that each delineates non-overlapping subdomains of Lhx6 neurons and are necessary for Lhx6 expression in the hypothalamus. Finally, the authors demonstrate that mature Lhx6 neurons manifest extensive molecular heterogeneity that is distinct from their counterparts in the telencephalon.

We thank the Reviewer for his/her comments, and for appreciating the key findings of the manuscript.

The work presented is of high quality and is a technological tour de force. The scope and depth of the study are unparalleled among similar studies of hypothalamic neurodevelopment. That said I only have a couple of minor suggestions.

1) In Figure S2, the number of tomato+ cells appear to be reduced, but not eliminated. Do the authors think that Lhx6 is necessary for the survival of all Lhx6 neurons, or just a subset? The use of the floxed Bax allele is clever, but is there evidence directly supporting increased cell death? Can the authors completely rule out the possibility of the mismigration of cell bodies after the postnatal deletion of Lhx6?

We appreciate the Reviewer for his/her comments. We conclude that Lhx6 is necessary for the survival of all Lhx6 neurons due to the lack of read-through transcription in Lhx6-CreER/CreER mice (Fig 2), and the rescue of Lhx6-deficient mice that is seen using conditional Bax mutants (Fig. 2). The fact that numbers of cells labeled with Lhx6-CreER are rescued by the deletion of this key positive regulator of apoptosis strongly implies that Lhx6-deficient neurons simply die. Finally, we observe very few Lhx6-expressing hypothalamic neurons that undergo even short-range tangential migration (Fig. 1), and observe no evidence for an increase in these cells in the analysis described in Fig. 2.

The fact that postnatal loss of function of Lhx6 leads to a more modest cell loss than the constitutive mutant may simply reflect a reduced overall requirement for Lhx6 in regulating neuronal survival in the postnatal hypothalamus or may indicate that the survival of a specific subset of Lhx6+ neurons is no longer Lhx6-dependent at this age. We cannot currently distinguish between these alternatives, and state this fact in the text.

2) In Figure 4, the authors acknowledged that the ectopic gene expression in Lhx6CreER/lox; Baxlox/lox mice could be due to the loss of function of Bax. If so, would Lhx6CreER/+; Baxlox/lox mice be a better control in this experiment?

We initially thought of using Lhx6-CreER/+;Baxlox/lox as a control since our phenotype could be due to loss of Bax itself, but not due changes in cell survival. However, we observed the same rescue phenotype in initial experiments using Lhx6-CreER/Bak-null (#006329), which strengthened our initial hypothesis. We now discuss potential limitations that may result from the fact that RNA-Seq data from Lhx6CreER/+;Baxlox/lox mice is not included in this study.

Reviewer #3:

Kim et al. aimed to characterize the similarities and differences between the development and molecular identity of telencephalic versus hypothalamic (HT) Lhx6+ GABAergic neurons. By analyzing a diverse repertoire of transgenic mice at different developmental stages and through the use of fate mapping, bulk and single cell sequencing approaches, ISH and immunostaining, the authors descriptively compare transcriptional networks and upstream regulators of LHX6. They found essential differences between LHX6-dependent networks and those in telencephalic neurons and suggest a role of LHX6 in survival instead of migration regulation HT neurons. Moreover, spatially distinct LHX6+ HT cell clusters were identified and transcriptionally profiled.

1) Only 1-2% of the GABAergic neurons express LHX6, and the cells expressing LHX6 in the HT were identified to be very diverse. Apart from a putative role for LHX6 in promoting the survival of HT neurons, which in my opinion is not analyzed convincingly, nothing functional was revealed. For this, I do not judge the potential significance and influence of the findings as broad or fundamental.

We respectfully but strongly disagree with this conclusion, most of which have already been described at length in our response to Reviewer #1. In brief, hypothalamic Lhx6+ neurons are key regulators of sleep initiation and maintenance, and nothing is known about their development. In much the same way that studies of the development of Lhx6+ cortical interneurons potentially help inform our understanding of neurodevelopmental disorders such as autism, so too may an understanding of the development of hypothalamic Lhx6+ neurons improve our understanding of sleep disorders and their treatment. In this study, we characterize the fate of hypothalamic Lhx6+ neurons, identify transcriptional regulatory networks that control their patterning and survival, and characterize their molecular heterogeneity in the postnatal period. We identify the homeodomain factor Nkx2.2 as a key regulator of both regional patterning of hypothalamic Lhx6 neurons, but also as a marker of a substantial subset of Lhx6+ ZI neurons that are activated by sleep pressure. This represents the groundwork needed for a basic understanding of the development of this physiologically important cell type, and forms the basis of more detailed future studies.

Unless the Reviewer simply believes that studies of hypothalamic development are inherently uninteresting and of little significance, these comments simply do not seem to reflect a careful reading of the manuscript, and come across as vague and unconstructive. In future reviews, we urge the Reviewer to be more specific, and to offer concrete and constructive comments, to support sweeping statements of this sort.

2) The manuscript could be better focused, and more coherent. The authors jump between different aspects of the story. First, the authors address a potential role of LHX6 in survival regulation in HT interneurons, and try to identify potential LHX6 target genes mediating this effect. The latter was neither analyzed convincingly nor validated. Then the authors switch to the comparative analysis of transcriptional networks in cortical versus hypothalamic LHX6+ interneurons, and the identification of different clusters of LHX6+ HT cells. Next, potential upstream regulators of LHX6 in HT neurons were addressed by fate mapping studies. Then, the authors again switch focus, and analyzed distinct anatomical regions covered by Lhx6+ neurons by single cell RNA seq and investigated an instructive role of Nkx2-1, Nkx2-2 and Dlx1/2 in the establishment of these hypothalamic regions.

Subheadings in the result section might be very useful. However, the focus of this study requires clarification and also respective consideration in the introduction.

As stated in our response to Reviewer #1, we have sought to conduct a broad characterization of the development and diversity of hypothalamic Lhx6+ neurons, a subset of which are important regulators of sleep. While we cover multiple aspects of this question, we strongly disagree that the manuscript “lacks focus”. However, we do agree that organization and clarity could be improved. To this end, we have incorporated subheadings into the Results section, and clearly outlined the experiments conducted, and the reasons why each were conducted.

3) The authors use a variety of different reporter and loss of function mouse models and jump between developmental stages for analysis. Apart from being confusing, the experimental/analytical pipeline is not sufficiently rigorous with respect to age and genetic background. E.g. to analyze target genes of LHX6 through which the effect on cell survival could be mediated, the authors compared expression profiles from P10 Lhx6CreER/+;Ai9 neurons with hypothalamic and cortical Lhx6-GFP positive and negative cells from P8 mice. Hypothalamic enriched genes were then compared to single-cell RNA-Sequencing (scRNA-Seq) datasets of E15.5 and P8 hypothalamic Lhx6-expressing neurons. Transcriptional profiles tremendously change with progressing development, and different mouse lines were used, which were not all time-matched. This might have caused Lhx6-independent variation, which likely masks relevant genes. This could be an explanation why so few LHX6 target genes were identified through which LHX6 putatively acts on neuronal survival.

This is another instance where the Reviewer seems to have failed to appreciate the rationale for the work presented here. We have modified the text to make this clearer. In summary, while it is certainly true that gene expression patterns are dynamic during development, cells of common origin and/or function also typically show core patterns of gene expression that are expressed across multiple stages of development. Our findings suggest that constitutive loss of function seen in Lhx6CreER/Lhx6CreER mice leads to a complete loss of hypothalamic Lhx6+ cells (Fig. 2), while the postnatal loss of function leads to a partial loss of Lhx6+ cells (Fig. 2). This suggests that Lhx6 may control the expression of similar target genes in both embryonic and postnatal hypothalamus to promote neuronal survival. In addition, since Lhx6 clearly is not required for survival of telencephalic neurons, we predict that Lhx6 will regulate the expression of specific sets of genes in both embryonic and postnatal hypothalamus, but not telencephalon, which promotes neuronal survival.

In Figure 4, we therefore identify candidates for these prosurvival genes both by comparing gene expression profiles between embryonic (E15) and postnatal (P8) hypothalamic and cortical Lhx6+ cells and also by directly comparing the gene expression profile of P10 control Lhx6-CreER;Ai9 and Lhx6-deficient but viable Lhx6CreER/Lhx6lox;Baxlox/lox;Ai9 mice. These were analyzed at P10 rather than P8 because of the need to ensure efficient disruption of the conditional alleles of Lhx6 and Bax, and induction of sufficient levels of tdTom to allow for efficient cell isolation, following daily 4-OHT administration between P1 and P5. While this might lead to the failure to identify whatever the small number of Lhx6-regulated genes that are differentially expressed between P8 and P10, we believe that this will identify the great majority of Lhx6-dependent genes that promote neuronal survival. Any readers who wish to delve further into this dataset, and identify additional genes we may have missed in this initial screen, can do so using the data in Table S1.

We are frankly puzzled by the Reviewer’s statement that we “identified so few Lhx6 target genes”, when we clearly state in Figure S2 that over 2,000 differentially expressed genes were observed between control and Lhx6/Bax-deficient hypothalamic neurons. A major reason why data was incorporated from the E15 and P8 datasets was to better select strong candidate regulators of neuronal survival from this very long list of genes.

4) The proposed survival regulatory function of LHX6 in HT interneurons represents the main functional finding of this study, which however was not analyzed in great detail. Likewise, the analysis of LHX6 target genes that mediate the survival regulating function was not very successful, identifying only the ERBB4 receptor and other genes related to the neurotrophic neuregulin pathway. Of note, the authors proposed a clear difference of LHX6-associated transcriptional networks and LHX6 function in telencephalic versus HT neurons (migration versus survival). However, THE identified target gene of LHX6 suggested to regulate survival in HT neurons was Erbb4. Erbb4 is likewise expressed in telencephalic neurons, here being involved in migration regulation. Studies that confirm Erbb4 function in survival regulation in HT neurons are lacking. By applying a more coherent analysis, comparing transcriptional profiles of Lhx6 KO and WT cells of the same age, better candidates might be identified. For this, the time window of the LHX6-dependent survival regulation needs to be identified.

This is exactly the point we were trying to make here. Lhx6 is strongly expressed in a large subset of progenitors and precursors of GABAergic neurons in the telencephalon, and in a much smaller subset of GABAergic neuronal precursors in has different functions between telencephalic and hypothalamic populations, yet is strongly expressed in both populations.

Quoting Reviewer #1 “Many developmental transcription factors are utilized both across diverse brain regions and across tissues outside of the brain”. Errb4 has been shown to regulate tangential migration in cortical interneurons but has been shown to promote neuronal survival in other cell types. Since hypothalamic Lhx6+ neurons do not undergo long-range tangential migration, we therefore conclude that the function of Errb4 in hypothalamic Lhx6+ neurons is likely related to promoting survival, rather than controlling migration. It is certainly possible, however, that Erbb4 could also contribute to the regulation of short-range tangential migration of Lhx6-expressing neuronal precursors, such as the likely migration of Nkx2.2-expressing cells from the hinge to the ZI. We have revised the text to make this point clearer. We certainly believe that further functional studies of these genes are worthwhile and compelling, but are also beyond the scope of this study.

5) With respect to the survival analysis, the analysis of Lhx6CreER/lox;Baxlox/lox;Ai9 mice although elegant, should be supplemented with other data, eg caspase and/or TUNEL labeling to support this main conclusion.

Both TUNEL and Caspase-3 staining is detectable for only a relatively brief period during apoptosis, and neither are highly sensitive tools for detecting neuronal death. We were unable to observe changes in staining with either marker between P5 and P10 following the postnatal loss of function of Lhx6 (Fig. 2). This is now mentioned in the text. The use of Bax mutants in this analysis, in which apoptosis altogether, was done with the aim of maximizing our ability to detect Lhx6-dependent regulation of neuronal survival.

Reviewer #3:

Kim et al. aimed to characterize the similarities and differences between the development and molecular identity of telencephalic versus hypothalamic (HT) Lhx6+ GABAergic neurons. By analyzing a diverse repertoire of transgenic mice at different developmental stages and through the use of fate mapping, bulk and single cell sequencing approaches, ISH and immunostaining, the authors descriptively compare transcriptional networks and upstream regulators of LHX6. They found essential differences between LHX6-dependent networks and those in telencephalic neurons and suggest a role of LHX6 in survival instead of migration regulation HT neurons. Moreover, spatially distinct LHX6+ HT cell clusters were identified and transcriptionally profiled.

1) Only 1-2% of the GABAergic neurons express LHX6, and the cells expressing LHX6 in the HT were identified to be very diverse. Apart from a putative role for LHX6 in promoting the survival of HT neurons, which in my opinion is not analyzed convincingly, nothing functional was revealed. For this, I do not judge the potential significance and influence of the findings as broad or fundamental.

2) The manuscript could be better focused, and more coherent. The authors jump between different aspects of the story. First, the authors address a potential role of LHX6 in survival regulation in HT interneurons, and try to identify potential LHX6 target genes mediating this effect. The latter was neither analyzed convincingly nor validated. Then the authors switch to the comparative analysis of transcriptional networks in cortical versus hypothalamic LHX6+ interneurons, and the identification of different clusters of LHX6+ HT cells. Next, potential upstream regulators of LHX6 in HT neurons were addressed by fate mapping studies. Then, the authors again switch focus, and analyzed distinct anatomical regions covered by Lhx6+ neurons by single cell RNA seq and investigated an instructive role of Nkx2-1, Nkx2-2 and Dlx1/2 in the establishment of these hypothalamic regions.

Subheadings in the result section might be very useful. However, the focus of this study requires clarification and also respective consideration in the introduction.

3) The authors use a variety of different reporter and loss of function mouse models and jump between developmental stages for analysis. Apart from being confusing, the experimental/analytical pipeline is not sufficiently rigorous with respect to age and genetic background. E.g. to analyze target genes of LHX6 through which the effect on cell survival could be mediated, the authors compared expression profiles from P10 Lhx6CreER/+;Ai9 neurons with hypothalamic and cortical Lhx6-GFP positive and negative cells from P8 mice. Hypothalamic enriched genes were then compared to single-cell RNA-Sequencing (scRNA-Seq) datasets of E15.5 and P8 hypothalamic Lhx6-expressing neurons. Transcriptional profiles tremendously change with progressing development, and different mouse lines were used, which were not all time-matched. This might have caused Lhx6-independent variation, which likely masks relevant genes. This could be an explanation why so few LHX6 target genes were identified through which LHX6 putatively acts on neuronal survival.

4) The proposed survival regulatory function of LHX6 in HT interneurons represents the main functional finding of this study, which however was not analyzed in great detail. Likewise, the analysis of LHX6 target genes that mediate the survival regulating function was not very successful, identifying only the ERBB4 receptor and other genes related to the neurotrophic neuregulin pathway. Of note, the authors proposed a clear difference of LHX6-associated transcriptional networks and LHX6 function in telencephalic versus HT neurons (migration versus survival). However, THE identified target gene of LHX6 suggested to regulate survival in HT neurons was Erbb4. Erbb4 is likewise expressed in telencephalic neurons, here being involved in migration regulation. Studies that confirm Erbb4 function in survival regulation in HT neurons are lacking. By applying a more coherent analysis, comparing transcriptional profiles of Lhx6 KO and WT cells of the same age, better candidates might be identified. For this, the time window of the LHX6-dependent survival regulation needs to be identified.

5) With respect to the survival analysis, the analysis of Lhx6CreER/lox;Baxlox/lox;Ai9 mice although elegant, should be supplemented with other data, eg caspase and/or TUNEL labeling to support this main conclusion.

Reviewer #2:

Kim and colleagues used a combination of state-of-art sequencing and mouse genetic tools to study the mechanisms that control the development of a subset of GABAergic neurons in the developing hypothalamus.

While neurodevelopment of GABAergic neurons has been extensively studied in the developing telencephalon, little is known about their counterparts in the developing hypothalamus. The authors focused their work on a specific subset of GABAergic neurons that express the LIM homeodomain factor Lhx6. Lhx6 is a master regulator of GABAergic neuron differentiation, specification, and migration in cortical interneurons. In contrast, Lhx6-expressing neurons make up only 2-3% of GABAergic neurons in the hypothalamus. The authors' previous work demonstrated that these neurons play a critical role in sleep homeostasis. Therefore, understanding how these neurons are formed and maintained is of great importance.

The authors show that hypothalamic Lhx6 is necessary for neuronal differentiation and survival. Furthermore, by profiling and comparing multiple RNA-seq, scRNA-seq, and ATAC-seq datasets, they were able to identify three transcription factors Nkx2.1, Nkx2.2, and Dlx1/2 that each delineates non-overlapping subdomains of Lhx6 neurons and are necessary for Lhx6 expression in the hypothalamus. Finally, the authors demonstrate that mature Lhx6 neurons manifest extensive molecular heterogeneity that is distinct from their counterparts in the telencephalon.

The work presented is of high quality and is a technological tour de force. The scope and depth of the study are unparalleled among similar studies of hypothalamic neurodevelopment. That said I only have a couple of minor suggestions.

1) In Figure S2, the number of tomato+ cells appear to be reduced, but not eliminated. Do the authors think that Lhx6 is necessary for the survival of all Lhx6 neurons, or just a subset? The use of the floxed Bax allele is clever, but is there evidence directly supporting increased cell death? Can the authors completely rule out the possibility of the mismigration of cell bodies after the postnatal deletion of Lhx6?

2) In Figure 4, the authors acknowledged that the ectopic gene expression in Lhx6CreER/lox; Baxlox/lox mice could be due to the loss of function of Bax. If so, would Lhx6CreER/+; Baxlox/lox mice be a better control in this experiment?

Reviewer #1:

This paper investigates the role of Lhx6 and other transcription factors in the development of GABAergic neurons in the hypothalamus. The authors report that a small fraction of hypothalamic GABAergic neurons express Lhx6 and further depend on this expression for their survival. Dlx1/2, Nkx1-1 and Nkx2-2 define 5 subpopulations and at least three of these populations depend on these TFs to maintain Lhx6 expression. A strength of the paper is the multimodal analysis and the fact that descriptive assays like RNAseq and ATACseq are followed up with specific knockouts of candidate transcription factors. However, the relationships between the developmental populations identified and adult subtypes of hypothalamic neurons remain unclear. Although the results will surely interest those already interested in hypothalamic development, it is not clear that broader developmental or functional principles have been identified. The authors make much of the fact that the identified populations do not resemble forebrain interneurons defined by Lhx6 expression, but it is not clear why this should have been expected. Many developmental transcription factors are utilized both across diverse brain regions and across tissues outside of the brain. Perhaps the emphasis of this point could be tempered.

The presentation of the manuscript could be improved by clarifying the relationships between embryonic and more mature structure within the hypothalamus. For example, It is extremely hard to follow the evidence split across figures 5, S6 and S7 for parsing the cell groups by TF expression.

The ATAC seems to be used only to bolster the impression that the populations identified by gene expression are different. The description of footprinting seems to imply an effort to analyze binding sites for specific factors (e.g. to identify targets of the TFs studied), but the statistical approach employed and even the conclusions reached are not fully spelled out. As such, this part of the study is underdeveloped or not well enough described.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Note: This rebuttal was posted by the corresponding author to Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

We thank the three reviewers for providing insightful critiques on our manuscript.

Changes to document and comments made are marked e.g. “Reply 1.1” (referring the Reviewer #1 item #1, etc.) as described below.

Reviewer #1

I found this study to be very convincing. Prior studies are referenced appropriately, the text is well written and clear, the figures are clear also. In my opinion the paper does not need further experiment.

[1.1] The conclusions are well supported by the data. However, the concatenation model seems very speculative at this point. Also, it does not take into account the dynamics of these molecules.

Reply 1.1: The concatenation model combines the structural data from our manuscript with prior biochemical insights into tetraspanin homodimerization and with scanning-EM data on immunogold-labeled CD81 and CD9 on cells. It is not completely clear to us what reviewer #1 refers to with “the dynamics of these molecules”. The cryo-EM data revealed that CD9 - EWI-F is a dynamic complex with straight and bent conformations, which could account for both circular and linear arrangements of tetraspanin-microdomains in cell membranes through the higher-order oligomerization of stable CD9 - EWI-F tetramers. Moreover, transient CD9 - CD9 interactions likely yield a variable number of complexes present in these concatenated and flexible strings of complexes. Such a concatenation model indeed requires further validation. However, it is consistent with experimental data and, importantly, provides a long-awaited molecular basis for TEM assembly. Although it was not within the scope of the current study, it will be of great interest to further investigate the concatenation model through detailed cell-biology based approaches.

**Minor comment:**

[1.2] There seems to be a mix up between the two structures in the following sentence p4: "In CD9EC2 - 4C8, the D loop adopts a partially helical conformation and central residue F176 is sandwiched by 4E8 residues W59 of CDR2 and W102 and R105 of CDR3 (Fig. 1D). In the 4C8-bound CD9EC2 structure the tip of the D loop points more outward and the Cα atom of F176"

Reply 1.2: The first sentence indeed mixed up the two structures and wrongfully mentioned CD9EC2 - 4C8 instead of CD9EC2 - 4E8. This has now been updated: “In CD9EC2 - 4E8, the D loop adopts …”

Reviewer #2

The paper is well written and the conclusions made are supported by the data presented.

[2.1] The ternary structure is in agreement with that of CD9 in complex with the related EWI-2 published earlier this year by Umeda et al (ref #25). The present work thus adds little structural insights but may be useful in showing that the interaction pattern seen extends to another EWI protein family member.

Reply 2.1: We agree with reviewer #2 that that the CD9 - EWI-F structure presented in our work is similar to the CD9 - EWI-2 structure published recently by Umeda et al. (ref #25). However, as also pointed out by reviewer #1, we believe that the CD9 - EWI-F structure adds new important information to understand the molecular mechanism underlying the assembly of tetraspanin-enriched microdomains. Notably, the different conformations of the CD9 - EWI-F complex observed in the cryo-EM data provide structural biology evidence for the dynamic nature of the interaction between a tetraspanin and a partner protein, which is consistent with a wealth of prior biochemical data. Guided by the distinct shape of the CD9EC2 - 4C8 densities, we were able to distinguish a range of straight to bent conformations of the complex. CD9 regions that represent known tetraspanin homo-dimerization sites, orient away from EWI-F and are available for interactions. Thus, combining our structural data with previous biochemical interaction data allowed for the generation of a long-awaited model for the assembly of tetraspanin-microdomains at the molecular level. We believe that these implications for TEM assembly will stimulate new, innovative research into the molecular principles that govern the function of tetraspanins.

[2.2] As such it may be acceptable for publication. In this case, the authors should improve the quality of Figs. 3D and 4D.

Reply 2.2: Figures 3D and 4D depict raw cryo-electron microscopy images (micrographs). The protein complexes imaged in this study only contain light atoms (H, N, C, O, S). Therefore, the collected micrographs only reveal low-contrast images of protein particles, and, for a typical cryo-EM experiment, it is required to average particles from thousands of micrographs to obtain a 3-dimensional reconstruction. We would like to keep the raw micrographs in figures 3 and 4, as it will aid cryo-EM scientists in judging the quality of the data.

Reviewer #3

The work is technically well performed and clearly presented including methodological details. I just have a few minor comments:

[3.1] Page 4 and Figure S1: it is hard to see how a reliable affinity for 4E8 can be obtained from the cell binding data in S1A, as there is no indication of saturation. It would be good to at acknowledge that this is at best a rough estimate. Fortunately the data for this nanobody in purified situation seems solid.

Reply 3.1: The obtained affinities are indeed an ±estimation based on a non-linear regression curve fitting on the measured data, performed in triplicate. The text has been updated and now reads as “4C8 and 4E8 bind to purified, full-length CD9 as well as to endogenous CD9 expressed on HeLa cells with apparent binding affinities in the nanomolar range (Fig. S1A, B, C)”. Next to that, a table stating the calculated KDs has been included as Fig. S1C.

[3.2] Page 6: Does the absence of micellar density for the EWI-F complex indicate flexibility of the extracellular domain relative to the TM? Does this happen because the classification focuses on the highly elongated Ig region?

Reply 3.2: These are indeed plausible assumptions. We observed highly heterogeneous, elongated particles in the micrograph shown in Fig. 3D, indicating inter-domain flexibility. If the alignment software focusses on certain Ig-like domains, other regions of the protein complex will be averaged out. An additional complexity with these elongated particles was to select an appropriate box size for particle picking and particle extraction, because the particles differ greatly in size based on their orientation (fully elongated side-views vs. much smaller top-views). When taken together, the complex of CD9 with full-length EWI-F was unsuitable for high-resolution structure determination; the subsequent strategy using EWI-FΔIg1-5 resulted in globular particles with less flexibility (Fig. 4D), which allowed for a more detailed structural characterization of the complex.

[3.3] Page 8: "Recently, a cryo-EM density map has been reported..." - please reference here.

Reply 3.3: We added the appropriate reference to the sentence: “Recently, a cryo-EM density map has been reported of CD9 in complex with an EWI-F homolog, EWI-2 (25).”

[3.4] Relatively little is known about how tetraspanins help to organize partner receptors into defined membrane domains, evidence for which has emerged from super-resolution light microscopy. Based on their structural analysis of the CD9-EWI-F complex, including the heterogeneity apparent in the cryo-EM structure, they propose a feasible concatenation model for higher order oligomerization of these complexes in the membrane. Obviously the model will need to be tested rigorously by mutational analysis, particularly the EWI Ig6 interface, but as it stands the paper is a significant contribution to the field of tetraspanins.

Reply 3.4: From the 8.6 Å cryo-EM data, the amino-acid residues that form the EWI-F Ig6 dimer interface can indeed not be distinguished. However, our data on CD9 in complex with full-length EWI-F (Fig. 3E) and previous cross-linking data (André et al. In situ chemical cross-linking on living cells reveals CD9P-1 cis-oligomer at cell surface - PMID: 19703604) support that EWI-F forms dimeric assemblies. Regarding the concatenation model, we therefore think that it will be of great interest to establish the putative CD9 - CD9 interactions (identified through biochemical approaches), that would link CD9 - EWI-F tetramers into higher assemblies, in the context of native membranes. However, investigating these transient interactions would require various non-trivial experiments and was therefore not within the scope of the current study.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #3

Evidence, reproducibility and clarity

This paper describes the structure of the tetraspanin CD9 and its interaction with the single pass protein EWI-F. The variability in the D loop of EC2 and the domain swapping is a useful addition to the limited structural database of these proteins and correlates with the relatively poor sequence conservation of this region. The key message is that dimerization of the single pass protein extracellular region, and interaction of its transmembrane helix with the tetraspanin, produces a heterodimeric structure that may further oligomerize. The authors propose a feasible concatenation model for higher order oligomerization of these complexes in the membrane.

The work is technically well performed and clearly presented including methodological details. I just have a few minor comments:

Page 4 and Figure S1: it is hard to see how a reliable affinity for 4E8 can be obtained from the cell binding data in S1A, as there is no indication of saturation. It would be good to at acknowledge that this is at best a rough estimate. Fortunately the data for this nanobody in purified situation seems solid.

Page 6: Does the absence of micellar density for the EWI-F complex indicate flexibility of the extracellular domain relative to the TM? Does this happen because the classification focuses on the highly elongated Ig region?

Page 8: "Recently, a cryo-EM density map has been reported..." - please reference here.

Significance

Relatively little is known about how tetraspanins help to organize partner receptors into defined membrane domains, evidence for which has emerged from super-resolution light microscopy. Based on their structural analysis of the CD9-EWI-F complex, including the heterogeneity apparent in the cryo-EM structure, they propose a feasible concatenation model for higher order oligomerization of these complexes in the membrane. Obviously the model will need to be tested rigorously by mutational analysis, particularly the EWI Ig6 interface, but as it stands the paper is a significant contribution to the field of tetraspanins.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

In this paper, Dr. Oosterheert and colleagues report the crystal structures of CD9EC2 bound to nanobodies 4C8 and 4E8. The CD9EC2/4C8 structure was useful in determining a low resolution cryo-EM structure of EWI-F in complex with CD9/4C8. The observed sample heterogeneity of this ternary complex was reduced by deleting the n-terminal five Ig domains of EWI-F, yielding a modest maximum global resolution of ~ 8.6 Å. The structural approaches used are standard. The crystallographic and structure refinement statistics are sound as are the cryo-EM image processing. The overall cryo-EM structure of the ternary complex shows a central EWI-F protein dimer flanked by one CD9 molecule on each side. The paper is well written and the conclusions made are supported by the data presented.

Significance

The ternary structure is in agreement with that of CD9 in complex with the related EWI-2 published earlier this year by Umeda et al (ref #25). The present work thus adds little structural insights but may be useful in showing that the interaction pattern seen extends to another EWI protein family member. As such it may be acceptable for publication. In this case, the authors should improve the quality of Figs. 3D and 4D.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

In this article, the authors provide new insights into the structure of the tetraspanin CD9. On the one hand, they provide crystal structures of the large extracellular domain of CD9, alone or bound to two nanobodies. The 3 structures are similar and similar to that of CD81, a related tetraspanin, except for a portion of the molecule, the so-called D-domain, showing flexibility of this domain. On the other hand, they obtained the cryo-EM structure of CD9 in association with a known-partner (EWI-F) with a resolution of 8.6A. More precisely, the complex of CD9 and the full-length EWI-F showed heterogeneity which they interpret as a consequence of the flexibility between the six Ig-like domains of EWI-F, precluding high-resolution structure determination. However, they showed that CD9 still interacted with a molecule lacking the 5 most membrane-distal Ig domains of EWI-F, and obtained the structure using this construct and an anti-CD9 nanobody. This structure reveals a hetero-tetrameric arrangement of CD9-EWIF, with a central EWI-F dimer flanked by a CD9 molecule on each side. CD9 and EWI-F interact through their transmembrane domains and the two truncated EWI-F molecules through the remaining Ig domains. Importantly, CD9 and EWI-F do not make contacts in the extracellular region, and CD9 shows a semi-open conformation. The structure also shows different configurations of the complex.

I found this study to be very convincing. Prior studies are referenced appropriately, the text is well written and clear, the figures are clear also.

In my opinion the paper does not need further experiment.

The conclusions are well supported by the data. However, the concatenation model seems very speculative at this point. Also, it does not take into account the dynamics of these molecules.

Minor comment:

There seems to be a mix up between the two structures in the following sentence p4: "In CD9EC2 - 4C8, the D loop adopts a partially helical conformation and central residue F176 is sandwiched by 4E8 residues W59 of CDR2 and W102 and R105 of CDR3 (Fig. 1D). In the 4C8-bound CD9EC2 structure the tip of the D loop points more outward and the Cα atom of F176"

Significance

Tetraspanins have been shown over the years to play an essential role in various biological functions. Among them, CD9 which is strongly expressed on the oocyte plasma membrane is essential for sperm-egg fusion. However, the mechanisms by which CD9 regulates this fusion process as well as other cell-cell fusion events remain unknown. The elucidation of its structure and of how it interacts with well characterized partner proteins is clearly a major advance in our understanding of the function of this molecule.

The absence of a structure for tetraspanins has been for a long time a knowledge gap. Following a breakthrough in 2001 with the publication of the crystal structure of the large extracellular domain of CD81 (Kitadokoro et al., EMBO J 2001), it was only recently that the structure of a full length tetraspanin, again that of CD81, was published (Zimmermann et al., Cell 2016). Earlier this year was published the crystal structure of a truncated version of CD9 as well as the cryo-EM structure of CD9 in association with another molecular partner EWI-2 (Umeda et al.,Nature com 2020).

The present structure adds new important information such as the existence of different conformation in the large extracellular domain of CD9 or the structure of CD9 with another molecular partner. It also highlights the different configurations of the complex. It will be of interest to researchers interested in tetraspanins, in membrane organization as well as researchers interested in the biological processes regulated by CD9, notably sperm-egg fusion.

My field of expertise concerns tetraspanins. I cannot comment on the technical aspects of the structures.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 2 of the manuscript.

This manuscript is in revision at eLife.

Summary:

This paper by Thacker et al. describes the use of lung-on-a-chip microfluidic devices to study early interactions during M. tuberculosis infection under conditions meant to mimic the alveolar environment in vivo. The authors use time-lapse microscopy to study host cell-Mtb interactions in macrophages and alveolar epithelial cells and the impact of surfactant on Mtb infection. This study suggests that organ-on-a-chip systems might be able to reproduce elements of host-microbe physiology during infection, which is difficult to reproduce ex vivo using single cells, air-liquid interface, organoids or organ explants.

This is an exciting approach which has the potential to expand the ability to study host-pathogen interactions. However, the reviewers all agree that the manuscript requires a major revision and additional data. Specifically, the manuscript requires improvement in the cell identification/classification, co-localization of Mtb with epithelial cells and macrophages, and distinction between intracellular and extracellular growth in order for the authors to provide convincing data to support their interpretations and conclusions.

While the reviewers recognize that it is challenging to use live cell imaging in this system, much of the data of the paper, such as comparisons between infection of AECs and macrophages, rests on the ability to determine the precise localization of bacteria. However, neither AECs nor macrophages are specifically identified with high enough resolution to give confidence that the Mtb are associated with those cells specifically, and more importantly, that the bacteria are growing intracellularly rather than extracellularly. Many of the images are of such low resolution that only tiny dots of bacteria are observed.

In addition, the findings of attenuated growth of Mtb after exposure to surfactant in macrophages and alveolar epithelial cells, changes in the Mtb cell wall after exposure to surfactant, and the finding that exposure to surfactant does not alter the extracellular viability of M. tuberculosis have been reported by others using other in vitro models and should be discussed in manuscript.

Reviewer #3:

The properties and mechanism of DNA transformation by Streptococcus pneumoniae have been intensively studied for nearly a century. This elegant and insightful paper develops a powerful new set of quantitative assays based on recombining out stop codons of fluorescent protein fusions to reprise several issues that have largely been addressed by conventional antibiotic resistance selection. This approach leads to new answers for a number of fundamental questions about pneumococcal transformation, thereby re-setting the paradigm in this area. This is an extremely well-written, complete study that answers interesting and important questions about bottlenecks and recombination during transformation of this genetically plastic pathogen.

This is a rigorous study that represents a substantial amount of work and creative thinking. The results will be of interest to a large audience concerned with genome evolution by transformation in different bacteria, points of limitation, or not, in the different steps in transformation, and mechanisms of recombination. The conclusions of this paper are well supported by extensive, often corroborative data, and provide new insights that go way beyond traditional genetic approaches. Rather complicated assay schemes are presented in highly effective diagrams and descriptions. Some of the new findings include that: all pneumococcal cells become competent and express the competence machinery in response to added competence stimulatory peptide or during natural competence; confirmation of brief non-genetic inheritance of phenotypes during transformation by single-cell tracking of recombination through lineage trees; a ≈50% limitation of transformation through RecA-dependent recombination that is unaffected by mismatch repair or restriction/modification; cell-cycle independence of recombination, regardless of reading strand or distance to the origin of replication; quantitation of direct multiple recombination (up to three was tested); and reduction of transformation recombination by non-homologous DNA.

Many of these conclusions overturn and/or refine previous results that were obtained by less precise genetic methods. Together, this paper shows that any site or orientation with regard to DNA replication can be transformed in pneumococcal cells, including multiple chromosomal insertions; however, there is an intrinsic limitation to the efficiency of recombination, possibly related to the level of off-marker recombination. This limitation may have implications to pneumococcal evolution.

Reviewer #2:

In this work Kurushima et al. use recently developed fluorescent labelling techniques to study natural transformation in the human pathogen Streptococcus pneumoniae. Previously, genetic marker analyses have been used to study the different aspects of this process, but with these new techniques the process can now be studied at the single cell level. The authors used the single cell analysis to identify new transformation bottlenecks and tried to determine why some cells are genetically transformed and others are not. Related experiments have been performed in the past using classic genetics and Kurushima et al. were able to confirm these studies. In that sense, in my opinion, the novelty is limited and no important new molecular insights are provided. They found that the number of cells that are ultimately transformed is plateauing at approximately 50%, despite the fact that most cells bind DNA. This is partially the result of the heteroduplex formed after recombination followed by separation by strand replication, combined with the fact that the DNA binding sites on cells are limited so that there is a competition between DNA markers at saturating DNA concentrations. The authors argue that this mechanism entails a "fail-safe strategy for the population as half of the population generally keeps an intact copy of the original genome". I find this conclusion far-fetched for two reasons.

Firstly, the DNA recombination event followed by DNA replication will automatically assure that only half the population will inherit the mutation, and to speak of a strategy implies that the organism has specifically evolved this system, but we are dealing here with a well-known and general recombination system found in many organisms that will generally result in a 50/50 distribution. Maybe more importantly, under natural conditions it is highly unlikely that cells encounter saturating levels of tDNA. In their experiments the authors use 3.2 nM DNA for transformation. If my calculation is correct, this would amount to 19xE11 DNA molecules per ml, which seems a bit high when assuming tDNA comes from lysed bacteria. In nature, this number will be much (much) smaller therefore there is no need for the bacterium to come up with a dedicated strategy to assure that not all cells in a population are being transformed.

Finally, the results are very well presented and the paper makes easy reading.

Reviewer #1:

Overall I thought this to be an extremely compelling story, both in terms of general scientific interest and the overall high degree of experimental rigor. Overall, the data provides strong experimental evidence to support the authors conclusions.

Overall, I found it very interesting the maximal efficiency is capped at 50%, as this makes for a very intriguing evolutionary hedge betting strategy for a naturally competent bacterial pathogen that frequently undergoes both intra and inter-species recombination events. In addition, this study provides a very elegant experimental framework for understanding the finer points of pneumococcal recombination through both clever genetic approaches and rigorous experimental design. The data was presented in a clear, concise manner and the overall manuscript followed a clear and logical progression.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 2 of the manuscript.

Summary:

All three reviewers felt that the manuscript was experimentally sound and praised the authors for their use of single cell analysis to tackle the question of why some cells are transformed and others are not in a population of genetically competent Pneumococci. The thoughtful presentation of complicated and extensive data was appreciated by all. Two reviewers were enthusiastic about the study's conclusions regarding bet hedging and the potential for an intrinsic limit on recombination efficiency. The latter reduces the potential for off-marker recombination which, as Reviewer #3 notes, might have implications to pneumococcal evolution. At the same time, Reviewer #2 had some reservations about the significance of the data in light of previous studies of Pneumococcus and other naturally competent organisms. Most importantly, this reviewer questions whether the finding that only a portion of bacteria incorporate exogenous DNA is a particularly novel one and, regardless, whether the saturating DNA concentrations used in the study are representative of a "natural" environment.

Reviewer #3:

The manuscript by Abdulhay, McNally and colleagues presents an effort to combine DNA modification detection and Pacbio sequencing to contribute to the growing body of methods designed to gain epigenome information at the chromatin fiber level, i.e. beyond existing short read NGS-chemistry constraints. They do so by leveraging micrococcal nuclease to cleave and help solubilize DNA, which they then treat with adenine methyltransferases to footprint nucleosomes; single-molecule adenine methylated oligonucleosome sequencing assay - SAMOSA. Fiber-level epigenetic information will be of great use to the field and is expected to answer many open questions that remain unanswered.

However many of the claims made about the potential of the method are insufficiently supported by the data provided. It appears that additional data is required to support the conclusions made from SAMOSA with respect to existing chromatin information, such as signal differences as a function of transcription factor binding (see below).

1) The authors should make an attempt to investigate where sequence bias influences a methylation call in their datasets. Clearly the pattern on the in vitro chromatinized template suggests that on average their methylated calls are correct. However, there appear to be clear positions in their chromatinized template datasets where this is not the case, i.e. lines in sup fig 5a representing methylation calls in unmethylated template DNA and unmethylated calls on fully methylated template DNA. Upon close examination, this also seems the case in the chromatinized template, with certain positions inflexibly methylated/unmethylated and at odds with the surrounding linker/nucleosome patterning (Fig1D). The authors should use Kmer analysis of methylated A's genome-wide to detect sequence bias in either the methyltransferase or sequencing platform.

2) It seems reasonable that the clustered data by NRL estimate (fig 3) should correlate with existing measurements (i.e. MNase-seq). The authors should identify regions of the genome with strong enrichment for the seven clusters and compare this to nucleosome repeat length as can be estimated using conventional MNase measurements, i.e. the average distance between 5' mapping read positions across the genome (Valouev et al., 2011, Teif et al., 2012). Some agreement (for at least a few of these clusters with very regular nucleosomes) would strengthen the conclusions made by this approach, especially where there are irregular positioning patterns. Additionally, for these clusters the authors should display raw read alignment/methylation calls for SAMOSA at a few representative loci, where a sense of the raw data can be gleaned.

3) The comparisons of SAMOSA at different TF bound regions is likely influenced by the fraction of actually TF-bound molecules present in the original cellular sample. For example, CTCF is known to occupy it's strong motifs in the majority of cells, while few other factors have such regular binding/residency (Kelly et al., 2012 NomeSeq data at CTCF sites). It seems reasonable that some cluster fractions should scale with the enrichment for the factor (for at least CTCF and REST, the strong binding/nucleosome positioners), especially those associated with chromatin accessibility at the motif (i.e. A-accessible, HA-hyper-accessible). The authors should try to illustrate this, as well as representative read alignments/methylation calls at a few loci where these signals are prevalent.

4) The meta-plotted data seems noisy for most TFs profiled (Fig 4 A-L) and the authors should show that their replicates agree with each other in terms of the relative size of clusters and at the metaplot level. Similarly, the data shown in Figure 5 should be broken into replicates. It is difficult to know to what extent the differences quoted are quantifiable/reproducible. For example, in panel A the reported deviation seems quite large around the median to make strong claims: e.g. "In specific cases, we observed small effect shifts in the estimated median NRLs for specific domains-for example, a shift of ~5 bp (180 bp vs. 185 bp) in H3K9me3 chromatin with respect to random molecules..." This should also apply to the analysis done in Figure 5B and C, where it is difficult to get a sense of reproducibility from cluster size and the heatmap of Odds ratio and q-values.

Reviewer #2:

The authors describe SAMOSA, a novel method for mapping accessibility on single chromatin fibers, using a non-specific adenine methyltransferase and taking advantage of the long-read high-accuracy capability of the PacBio platform. The method allows for chromatin arrays to be precisely mapped for nucleosomal and non-nucleosomal footprints on single chromatin fibers. When combined with light MNase treatment, the method provides two orthogonal readouts of the chromatin landscape for single molecules, with advantages over other single-molecule long-read methods. Proof-of-concept application of this new method to human K562 cells reveals global heterogeneity, with surprisingly little distinction in nucleosome array patterns between regions distinguished by various active or repressive histone modification patterns. The heterogeneity observed using the unbiased approach represented by SAMOSA highlights the fact that the most common chromatin profiling methods favored by both large projects such as ENCODE and individual researchers are dominated by features such as histone modifications and hyper accessible sites. The method itself and insights into global nucleosomal heterogeneity are of substantial interest to the fields of chromatin and gene regulation. The data are of high quality and the methods are well-described. I have only one suggestion and a couple of minor issues.

In Figure 5, controls are randomly chosen nucleosomes, but it would be interesting to see what unmarked nucleosomes show. For example, unmarked alpha-satellite should be dominated by highly regular arrays with a 171-bp repeat length present in higher-order repeats corresponding to active centromeres, which consist of nucleosomal complexes that lack Histone H3 (CENP-A instead). The authors speculate that satellite irregularity might result from dynamic restructuring by HP1, and this predicts that other (H3-containing) unmarked satellites that lack H3K9me3 and presumably lack HP1 will be in regular arrays.

Reviewer #1:

The authors validate the method on a reconstituted array of 9 nucleosomes, and convincingly show that m6dA is found in linker DNA, and not (or greatly reduced) at positions bound to nucleosomes.

They then apply the approach to chromatin fibers released from K562 cells. Long read patterns were clustered to identify 7 clusters. The idea is that because the fragments are released by mild MNase digestion, there will be a positioned nucleosome at one end. The 7 clusters differ in nucleosomal spacing. I am not familiar with Leiden clustering, it would be good if the authors can confirm these clusters with alternative clustering methods. These clusters appear differentially represented in domains that differ in histone modifications.

Aggregation of data around TF binding sites further reveals a range of different states that show variable nucleosome positioning. This section is interesting but seems rather shallow in analysis. The authors have the ability to look at specific sites and determine the variation in nucleosome positioning in the cell population. However, they look only at aggregated data.

Overall the approach works well and promises to address important questions, but the current work does not yet take full advantage of the single molecule nature of the assay and as such falls a bit short compared to very related methods that have recently been published (the works cited in the ms, and recently published work from the Stamatoyannopoulos lab). Also, the use of mild MNase is presented as an advantage, but is it really necessary? Adding EcoGII to isolated nuclei may work as well as shown in the recent Stamatoyannopoulos paper in Science.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Summary:

This manuscript describes a method, named SAMOSA, to identify nucleosome positions along chromatin segments that can be over 10 Kb in size. The approach employs EcoGII-modulated m6dA deposition on accessible non-nucleosomal DNA (inkers, nucleosome free regions) released from nuclear after mild MNase cleavage. The DNA modification is then read-out using PacBio sequencing. Mapping nucleosome positions along longer DNA stretches can provide information on variation in nucleosomal arrays, and how that relates to chromatin state and factor binding etc. The assay is validated using a reconstitute chromatin template and then applied to K562 cells, revealing significant variation in nucleosome positioning and nucleosome repeat lengths at transcription factor binding sites, and throughout domains with various histone modifications.

Reviewer #3:

In this study, the authors present data aimed at supporting their conclusion that microbiota-derived SCFA resulting in increased AD pathology, including microglial activation, ApoE upregulation, and A-beta deposition.

First and foremost, the biggest issue with this study is the lack of male versus female comparisons and the very small sample sizes of the mice. Especially given the past literature of microbiome effects on AD pathology, e.g. with antibiotic cocktails, it is essential to look at sufficient numbers of both female and male mice, individually, and not just group them. Moreover, the average number of mice used in each experiment (N=5) are relatively small for making any firm conclusions.

Specific concerns:

Figure 1D: Based on the observation of more smaller plaques in SPF mice vs GF mice, the authors conclude, "This result highlights the impact of bacterial colonization on early amyloid plaque deposition rather than plaque growth," The problem here is that these mice are 5 months old. It is well-known that SPF APPPS1 mice start depositing at only 6 weeks old. So, they would need much earlier (and later) time points to support this conclusion. In addition, N=5 animals/group is very small and not appropriate for making conclusions.

The authors also need to show total plaque burden distribution in each group and level of variability?

Figure 2: Again, N=5/group is very small for high impact paper. They also need to show plaque burden distribution, especially since there is much more variability in 3 month old animals.

Figure 2D: The authors claim SCFA brings up plaque load to a "significant increase", i.e., 2X GF levels. But what are these values compared to SPF animals? They would need to have data on the 3 month SPF group for comparison sake to make the claim that SCFAs are driving pathology. Otherwise, this is just not convincing.

Figure 3: Westerns should also include 3 month SPF animals. The small differences in CTFalpha and CTFbeta are not convincing. Even if there were a change, how does it account for elevated Abeta?

Figure 4: SCFA trigger microglial activation: the data in this figure fail to support this conclusion:

Fig 4B: Why did the authors perform in situ for CX3CR1 instead of Iba 1 ICC for microglia? The quantification is unconvincing. There should be other CX3CR1 microglia that are not plaque associated, but we don't see these in the field. This brings into question the sensitivity of the in situ analyses? They need to also do Iba1ICC.

Fig 4 C/D: Regarding the statement, "we directly investigated the influence of bacterial colonization on microglial reactivity in the WT background. To this end, we injected brain homogenates from 8 months old APPPS1 mice containing abundant Ab into the hippocampus of GF or SPF WT mice (Fig. 4C) and subsequently analyzed microglial abundance and activation by smFISH. We observed a significant increase in overall microglial cell counts at the peri-injection site of SPF compared to GF WT mice (Fig. 4D)."

This experiment does not support the conclusion since one would expect microglial reactivity to increase in this experimental paradigm. The authors claim more activation in SPF mice, thus "gut microbiome triggers microglial activation and reactivity towards an exogenous insult containing Ab". But, this is unfortunately not supported by the experiments, as performed.

Figure 4F: The ex vivo amyloid clearance assay is not useful or convincing since cultured microglia lose their transcriptional phenotype after 6 hrs in culture (Gosselin et al, Science 2017).

Reviewer #2:

This is an interesting and well-written paper on the relationship between gut microbiota metabolites and AB production. Although previous studies have documented a link between the gut microbiome and Ab pathology, the underlying mechanisms and molecular mediators remain elusive. Here the authors use a germ-free Alzheimer's Disease mouse model to examine the role of short chain fatty acids on amyloidogenesis and neuroinflammation.

The studies thus add another welcome piece to the puzzle of how the microbiota affects the brain.

My comments are relatively minor:

How do the behaviour of GF animals compare with non-GF animals given that cognitive deficits have been reported in them (Gareau et al., 2011)?

I am somewhat surprised that more metabolite differences were not observed between GF & SPF mice as all microbial metabolites should be only in the latter.

Fig 2B should include all metabolites tested individually

Were the concentrations of the metabolites increased in the plasma following administration in drinking water? The physiological relevance of the doses used in the rescue experiments could be better supported with experimental data

If acetate is most important then it is not clear why they used a pooled cocktail in rescue experiments.

The analysis of transcriptome of brain samples from control- and SCFA-supplemented GF APPPS1 mice is a nice addition but the molecular targets for SCFAs on microglia remains unresolved.

The comments about modulating dietary fibre to reduce central SCFA concentrations are provocative and although beyond the scope of the current study are clearly studies that would be very welcome for the field to test.

The potential effects of SCFAs on HDACs is completely left as a cliff-hanger...

Reviewer #1:

The authors do a good job of citing the prior literature; however, Harach et al., 2017 did diminish my enthusiasm as it covers much of the same ground as this study, limiting the novelty of the current findings.

Essential Revisions:

1) Experimental perturbation of the proposed pathway. The manuscript leads to a nice model; however, the data is descriptive in nature with any experiments using either genetic or pharmacological approaches to test the proposed mechanisms. The impact of this study would be increased substantially if at least one link between SCFAs and AB, microglia, or ApoE were experimental validated. While most of the text avoids making causal claims based on correlative evidence, the one sentence summary states that SCFAs impact disease "via activation of microglial cells and upregulation of ApoE."

2) Identify which SCFA matters. The experiments all rely on a mixture of 3 SCFAs making it impossible to determine which compound is responsible. There is also high salt in this mixture which confounds the interpretation further. At a minimum, each individual compound needs to be tested using an equimolar amount of salt as a negative control. The authors should also note issues with oral delivery of SCFAs, which does not necessarily mimic production in the colon. Ideally, tributyrin, or a similar ester for acetate or propionate should be used. Another key missing control is the administration of SCFAs to SPF mice. It is also important to be clear that while SCFAs are sufficient to impact AB, there is no evidence in the paper to suggest that they are necessary, the full scope of "key microbial metabolites" remain to be determined. If the authors want to claim necessity, they would need to deplete specific SCFAs in the presence of a complex gut microbiome.

3) Be more cautious in discussing the role of the microbiome in Alzheimer's disease. The background discussion includes studies that show correlations in humans and phenotypic differences in germ-free mouse models, which in my opinion are insufficient to claim a causal role in human disease. The authors should discuss the level of evidence in humans for a causal role of the microbiome and its relative impact relative to other risk factors, including any prospective or intervention studies that have been conducted. They should also take care not to extrapolate differences in intermediate phenotypes in mice (plaque levels, microglial activation, and ApoE expression) to human disease. For example, the one sentence summary says, "contributing to AD disease progression". The authors should also discuss whether or not cognitive performance was evaluated in response to SCFAs.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Summary:

Colombo et al. present an intriguing set of findings from the amyloidosis mouse model (APPS1). Rederivation of this model under germ-free conditions led to both decreased plaque load and impaired cognitive performance. Administration of a cocktail of SCFAs and salt (sodium propionate, butyrate, and acetate) significantly increased plaque levels, microglial activation, and ApoE expression. Together, these findings suggest a potential pathway through which the microbiome could impact cognitive performance. The paper is well-written, with a clear description of the current results and a logical flow to the text and figures. These data are a good starting point for further mechanistic dissection and add another welcome piece to the puzzle of how the microbiota affect the brain.

Note: This rebuttal was posted by the corresponding author to Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

Reviewer #1

1. The first hypothesis of the manuscript is that, rather than a change in a single immune pathway being responsible for the lack of response to the virus, the response will be systemic involving multiple inter-related pathways. The data show that this was the case after presenting convincing transcriptome analysis.

We thank the reviewer agreeing that we have convincingly shown that the response to the virus is systemic involving the induction of interrelated pathways

The second hypothesis is that the differences in responses between bats and humans are due to evolutionarily divergent genes. The authors provide evidence for this in the transcriptome differences in the C-reactive protein, aspects of the complement system, iron regulation and M1/M2 macrophage polarization. The second hypothesis is broad, but there are clearly differences in the genes involved in humans and bats. Without mechanistic information on the function of the proteins/cells investigated, it is hard to determine that the changes the authors are observing are the cause of the different responses, rather than an effect of some upstream response, and so difficult to pin-point specific divergent genes.

We agree that mechanistic studies will be required to test causal links between the genes we identified and specific anti-viral responses, an effort that is likely to require multiple laboratories and some time. The aim of this study was to enable this effort by identifying a list of candidate genes affected by EBOV and MARV infection in bats, not merely in cultured bat cells.

The authors wish to compare the response to the virus in bats to the better characterized human tissue responses, but because this relies on previously published work in humans, it is sometimes unclear whether "more bat-like" responses are definitely associated with positive outcomes in humans. As the benefit of certain responses in human infections can depend on the timing of the response, it might be helpful to include summarized human data in manuscript to aid comparison with the bat responses.

We agree and have added the following data and discussion (inserted into Discussion, page 9, and added two new tables, Tables 2 and 3).

Comparing our observations to human responses to filoviruses is limited by the scarcity of studies in humans. Nevertheless, this comparison suggests potential directions to explore. In one study, individuals who succumbed to the disease showed stronger upregulation of interferon signaling and acute phase responses compared to survivors during the acute phase of infection[1], consistent with the anti-inflammatory response gene expression signature identified in this study in bats. However, most of the genes used in the study by Liu et al. to classify survivors are either barely expressed in bats or do not respond to filoviral infection (Table 2), the differences that provide potential clues to find why bats can tolerate the infection.

A study of patients infected with Sudan Ebola virus (SUDV) analyzed protein levels for a panel of genes using a Luminex multiplex assay (using antibodies)[2]. The panel was based on results from other studies and pathways involved in the response to infections. The patients were classified into 3 possible dichotomies (fatal/non-fatal, hemorrhaging/non-hemorrhaging, or high/low viremia) correlated with genes that characterized these states. Most of these genes either are barely expressed, if at all, or are unaffected by infection in bats, except for ferritin (FTL, FTH1) whose expression is lowered by MARV infection, consistent with the observation that ferritin is higher is fatal human cases (Table 3).

For instance, the T-cell response section concludes "Bats mount a T cell response against the infection" but there is no discussion of the impaired but complex lymphocyte response in humans, so comparison is not possible.

We have expanded the discussion on T cells (Results, page 7) as follows.

Previous studies on the adaptive immune response to Ebola and Marburg viruses in humans, non-human primates, and non-primate mammals, shows that long-term immunity is conferred by both T cell and antibody responses. Mostly CD8+ T cells were elicited and helpful against Ebola in mice[3],[4], while SUDV infection in humans[5]) and MARV infection in cynomolgus monkeys[6] and humans[7] ) elicited mostly CD4+ T cells . In most human EBOV infections, CD8+ T cells against the EBOV NP protein dominated the responses, while a minority of individuals harbored memory CD8+ T cells against the EBOV-GP [8].

Consistent with this, in MARV-infected bats, CD4 expression (specific to CD4+ T cells) was higher, while in EBOV-infected bats, CD8 expression (specific to CD8+ T cells) was higher, the overall levels are low, because the tissue samples are heterogenous and expression of these markers is not high in the T cells to begin with. T cell markers (such as CCL3, ANAX1, TIMD4 and MAGT1) are also upregulated in liver, suggesting a T cell response is mounted.

Mock infected IHC should be included in Figure 1F to demonstrate the antibodies are not background.

We have added IHC data of two mock-infected animals (Fig. S1 panels A and B).

See comment in hypotheses- a summarized table of findings from previous studies of early responses to the virus would be helpful for comparisons to the bat response and for determining the second hypothesis.

We have expanded our comparisons to previous studies by adding the following text to Introduction (page 3)

A potential source of the difficulty to understand how bats tolerate or eliminate the viruses that are deadly to humans is the lack of studies that analyze the response to infection in bats rather than in cultured bat cells. The results obtained using cell lines have been contradictory. Some studies claim both EBOV and MARV replicate to similar levels in ERB and human derived cell lines[9], with a robust innate immune response mounted by ERB and to a lesser degree, human cells, while others claim MARV inhibited the antiviral program in ERB cells, like in primate cells, and did not induce almost any IFN gene [10], or little anti-viral gene induction[11]. An experiment with the pig (PK15A) and bat (EhKiT) cells suggested they responded to EBOV through the upregulation of immune, inflammatory, and coagulation pathway, in contrast to a limited response in the human (HEK293T) cells[12]. To comprehensively understand the pathways involved in the bat filoviral response, we infected bats, rather than their isolated cells, and analyzed tissue-specific RNA expression through mRNA-seq in the organs of the infected animals.

Reviewer #2

1. The authors provide this contribution to the extremely interesting topic of the immunobiology that facilitates filovirus infections of bats without overt pathology. They focused entirely on gene transcription signatures from different tissue sites following experimental infection, and sometimes compare those signatures with those generated in humans following natural exposures to filoviruses. The strengths of the paper is the shear breadth of data generated that is available openly to the scientific community and the development of novel mRNA datasets from bats, in the absence and presence of infection. One of the major limitations of this systems-based approach is that there is no mechanistic data that links gene function to the immune response to filovirus infection. Rather, associations are made and functional links are inferred. This limitation makes the title of the manuscript "...is controlled by a systemic response" an overstatement.

We thank the reviewer and agree that mechanistic studies were out of scope of this study and have reflected this fact in the title by replacing “is controlled” with “induces”:

Ebola and Marburg filovirus infection in bats induces a systemic response

The authors indicate that one of their main objectives is to understand differences in the responses to infection between bats and humans. But this submission says little about the transcriptome-level responses to filovirus infection in humans. It does, on at least one occasion, state that some of the bat genes with altered expression levels were also altered in a study of human filovirus infections (reference #67). I think it would be helpful if the authors devoted a figure or table to the direct comparison between their analysis of MARV- and EBOV-infected bats and the findings of filovirus-infected humans, highlighting genes that are differentially up- or downregulated between the two species.

This discussion, which was also requested by Reviewer 1, is now included in the manuscript (Discussion page 9 and Tables 2 and 3).

Figure 2 is not described nor presented usefully. Instead of providing a figure title ""Upset plot..." the authors should clearly describe the type of transcriptomic data being presented. Moreover, it way the data is plotted does not reveal any direct information about the genes that are up- or downregulated in each condition, thus reducing its utility to the reader. I suggest that this Figure be placed in the Supplemental information. In fact, Figures 3 could also be moved to the Supplemental information

Figure 2 makes that point that the response is a broad one while Figure 3 presents evidence from expression data that there is tissue-specific responses to the viruses. Both together provide convincing evidence of a systemic, wide-ranging response to both MARV and EBOV infections. We have edited the caption to Figure 2 by changing it to the following:

Figure 2: Broad response of bat liver genes to filoviral infection. Many genes in the liver respond to filoviral infections, with MARV having a bigger impact compared to EBOV (840 genes that are responsive to MARV alone, compared to the 43 specific to EBOV alone). The EBOV-specific (EBOV/MARV) and MARV-specific (MARV/EBOV)genes are likely host responses specific to the viral VP40, VP35 and VP24 genes. In the plot, mock refers to mock-infected bats, EBOV to EBOV-infected bats, and MARV to MARV-infected bat livers. Each row in the lower panel represents a set, there are six sets of genes based on various comparisons, e.g., EBOV/mock is the set of genes at least 2-fold up regulated in EBOV infection, compared to the mock samples. The gray bars at the lower left representing membership in the sets. The vertical blue lines with bulbs represent set intersections, e.g., the last bar is the set of genes common to EBOV/MARV, EBOV/mock and MARV/mock, so the genes in this set are up 2-fold in EBOV compared to the mock and MARV samples, and at least 2-fold up in MARV compared to mock. The main bar plot (top) is number of genes unique to that intersection, so the total belonging to a set, say mock/EBOV, is a sum of the numbers in all sets that have mock/EBOV as a member (41+203+6+31=281).

The authors do not specify in the main text, figure captions, or methods sections how they objectively assigned bat homologs as being "similar to " or "divergent from" their human counterparts. What is the cut-off in terms of sequence similarity?

We apologize for this omission. In addition to a description in Methods, we have added the following statement to the Results section (Page 4).

To identify divergent genes, we relied on BLASTn[13]. Genes detected as homologues (16004, 87% out of 18443 genes in our databse) using BLASTn default settings were labelled “similar”. The remaining 2439 genes (13%) were considered “divergent”. Of these genes, 1,548 transcripts (8% of the total), could be identified as homologous by reducing the word-size in BLASTn from 11, the default, to 9. This approach is equivalent to matching at the protein level, but we find that using nucleotide level matches provides a cleaner separation of the two classes than using translated proteins (Fig. 4, Methods).

In the Discussion, it is surprising that the authors state that "the majority of interferon response genes are not divergent from human homologs" since genes involved in innate immunity are some of the most rapidly evolving genes known to exist. Again, clarification over what dictates "divergence" over "similarity" is warranted. Many previous studies have shown how a single residue change in an innate immune effector can drastically alter its specificity and/or potency.

We have clarified this point by adding the following statement in the Discussion (pages 8,9)

There are hundreds of genes involved in the interferon response, some key components can mutate to change specificity of their interactions, but most, especially those in the core ISG category[14], evolve slowly and have conserved function and sequence[15]. Our analysis of gene divergence shows that the majority of interferon response genes are not divergent from their human homologs, consistent with prior observations that the innate responses are quite similar between human and bat cell lines[9]. This implies that other systems are involved in generating the difference in response between bats and humans.

The authors state in the introduction, and point to citation #21, that ERBs are "refractory to infection." In Figure 1, the authors indicate that experimental of ERBs with EBOV led to detectable infection in some animals, particularly in the liver. At this point in the manuscript, the authors should state if and how this result differs from what is published in #21, and they should comment on whether this is scientifically significant, or not. This is eventually discussed briefly in the Discussion but adding a sentence to Results section would be helpful for readers.

To emphasize that our results contradict prior reports of ERB being refractory to EBOV infection, we have modified the statement in the Results (page 3) as follows.

Two of the three EBOV-inoculated animals presented with histopathological lesions in the liver, consisting of pigmented and unpigmented infiltrates of aggregated mononuclear cells compressing adjacent tissue structures, and eosinophilic nuclear and cytoplasmic inclusions, changes consistent with previous reports[16], [17]. In EBOV-infected animals, focal immunostaining with both pan-filovirus and EBOV-VP40 antibodies was observed in the liver of one animal, but very few foci were found, suggesting limited viral replication.

The research question at hand, concerning how bats serve as reservoirs for multiple viruses which are pathogenic to humans without succumbing to disease, is one of the hottest topics in immunology and virology. However, the authors do not provide a clear enough explanation of how their approach to study the transcriptome response following filovirus infection goes beyond what has been published in previous studies. This manuscript would greatly benefit from a discussion of its novelty in the Introduction and Discussion sections.

We have reviewed prior human and bat studies (Introduction -page 3 and Discussion- page 9 shown above) to highlight the novelty of our findings. We have also added the following sentence at the end of the Introduction highlighting the novelty of the study.

This is the first in vivo study that focuses on the coordinated transcriptional response to filoviruses at the level of individual organs in bats.

References

[1] X. Liu et al., “Transcriptomic signatures differentiate survival from fatal outcomes in humans infected with Ebola virus,” Genome Biology, vol. 18, no. 1, p. 4, Jan. 2017, doi: 10.1186/s13059-016-1137-3.

[2] A. K. McElroy et al., “Ebola hemorrhagic Fever: novel biomarker correlates of clinical outcome,” J. Infect. Dis., vol. 210, no. 4, pp. 558–566, Aug. 2014, doi: 10.1093/infdis/jiu088.

[3] S. B. Bradfute, K. L. Warfield, and S. Bavari, “Functional CD8+ T cell responses in lethal Ebola virus infection,” J. Immunol., vol. 180, no. 6, pp. 4058–4066, Mar. 2008, doi: 10.4049/jimmunol.180.6.4058.

[4] M. N. Rahim et al., “Complete protection of the BALB/c and C57BL/6J mice against Ebola and Marburg virus lethal challenges by pan-filovirus T-cell epigraph vaccine,” PLOS Pathogens, vol. 15, no. 2, p. e1007564, Feb. 2019, doi: 10.1371/journal.ppat.1007564.

[5] A. Sobarzo et al., “Multiple viral proteins and immune response pathways act to generate robust long-term immunity in Sudan virus survivors,” EBioMedicine, vol. 46, pp. 215–226, Aug. 2019, doi: 10.1016/j.ebiom.2019.07.021.

[6] L. Fernando et al., “Immune Response to Marburg Virus Angola Infection in Nonhuman Primates,” J Infect Dis, vol. 212, no. suppl_2, pp. S234–S241, Oct. 2015, doi: 10.1093/infdis/jiv095.

[7] S. W. Stonier et al., “Marburg virus survivor immune responses are Th1 skewed with limited neutralizing antibody responses,” J. Exp. Med., vol. 214, no. 9, pp. 2563–2572, Sep. 2017, doi: 10.1084/jem.20170161.

[8] S. Sakabe et al., “Analysis of CD8+ T cell response during the 2013–2016 Ebola epidemic in West Africa,” PNAS, vol. 115, no. 32, pp. E7578–E7586, Aug. 2018, doi: 10.1073/pnas.1806200115.

[9] I. V. Kuzmin et al., “Innate Immune Responses of Bat and Human Cells to Filoviruses: Commonalities and Distinctions,” J. Virol., vol. 91, no. 8, Apr. 2017, doi: 10.1128/JVI.02471-16.

[10] C. E. Arnold et al., “Transcriptomics Reveal Antiviral Gene Induction in the Egyptian Rousette Bat Is Antagonized In Vitro by Marburg Virus Infection,” Viruses, vol. 10, no. 11, 02 2018, doi: 10.3390/v10110607.

[11] M. Hölzer et al., “Differential transcriptional responses to Ebola and Marburg virus infection in bat and human cells,” Scientific Reports, vol. 6, p. 34589, Oct. 2016, doi: 10.1038/srep34589.

[12] J. W. Wynne et al., “Comparative Transcriptomics Highlights the Role of the Activator Protein 1 Transcription Factor in the Host Response to Ebolavirus,” Journal of Virology, vol. 91, no. 23, Dec. 2017, doi: 10.1128/JVI.01174-17.

[13] S. F. Altschul, W. Gish, W. Miller, E. W. Myers, and D. J. Lipman, “Basic local alignment search tool,” J. Mol. Biol., vol. 215, no. 3, pp. 403–410, Oct. 1990, doi: 10.1016/S0022-2836(05)80360-2.

[14] A. E. Shaw et al., “Fundamental properties of the mammalian innate immune system revealed by multispecies comparison of type I interferon responses,” PLOS Biology, vol. 15, no. 12, p. e2004086, Dec. 2017, doi: 10.1371/journal.pbio.2004086.

[15] T. B. Sackton, B. P. Lazzaro, T. A. Schlenke, J. D. Evans, D. Hultmark, and A. G. Clark, “Dynamic evolution of the innate immune system in Drosophila,” Nat. Genet., vol. 39, no. 12, pp. 1461–1468, Dec. 2007, doi: 10.1038/ng.2007.60.

[16] M. E. B. Jones et al., “Experimental Inoculation of Egyptian Rousette Bats (Rousettus aegyptiacus) with Viruses of the Ebolavirus and Marburgvirus Genera,” Viruses, vol. 7, no. 7, pp. 3420–3442, Jun. 2015, doi: 10.3390/v7072779.

[17] J. T. Paweska, N. Storm, A. A. Grobbelaar, W. Markotter, A. Kemp, and P. Jansen van Vuren, “Experimental Inoculation of Egyptian Fruit Bats (Rousettus aegyptiacus) with Ebola Virus,” Viruses, vol. 8, no. 2, Jan. 2016, doi: 10.3390/v8020029.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

The authors provide this contribution to the extremely interesting topic of the immunobiology that facilitates filovirus infections of bats without overt pathology. They focused entirely on gene transcription signatures from different tissue sites following experimental infection, and sometimes compare those signatures with those generated in humans following natural exposures to filoviruses. The strengths of the paper is the shear breadth of data generated that is available openly to the scientific community and the development of novel mRNA datasets from bats, in the absence and presence of infection. One of the major limitations of this systems-based approach is that there is no mechanistic data that links gene function to the immune response to filovirus infection. Rather, associations are made and functional links are inferred. This limitation makes the title of the manuscript "...is controlled by a systemic response" an overstatement.

Major points:

The authors indicate that one of their main objectives is to understand differences in the responses to infection between bats and humans. But this submission says little about the transcriptome-level responses to filovirus infection in humans. It does, on at least one occasion, state that some of the bat genes with altered expression levels were also altered in a study of human filovirus infections (reference #67). I think it would be helpful if the authors devoted a figure or table to the direct comparison between their analysis of MARV- and EBOV-infected bats and the findings of filovirus-infected humans, highlighting genes that are differentially up- or downregulated between the two species.

Figure 2 is not described nor presented usefully. Instead of providing a figure title ""Upset plot..." the authors should clearly describe the type of transcriptomic data being presented. Moreover, it way the data is plotted does not reveal any direct information about the genes that are up- or downregulated in each condition, thus reducing its utility to the reader. I suggest that this Figure be placed in the Supplemental information. In fact, Figures 3 could also be moved to the Supplemental information.

The authors do not specify in the main text, figure captions, or methods sections how they objectively assigned bat homologs as being "similar to " or "divergent from" their human counterparts. What is the cut-off in terms of sequence similarity?

In the Discussion, it is surprising that the authors state that "the majority of interferon response genes are not divergent from human homologs" since genes involved in innate immunity are some of the most rapidly evolving genes known to exist. Again, clarification over what dictates "divergence" over "similarity" is warranted. Many previous studies have shown how a single residue change in an innate immune effector can drastically alter its specificity and/or potency.

Minor points:

The authors state in the introduction, and point to citation #21, that ERBs are "refractory to infection." In Figure 1, the authors indicate that experimental of ERBs with EBOV led to detectable infection in some animals, particularly in the liver. At this point in the manuscript, the authors should state if and how this result differs from what is published in #21, and they should comment on whether this is scientifically significant, or not. This is eventually discussed briefly in the Discussion but adding a sentence to Results section would be helpful for readers.

Significance

The research question at hand, concerning how bats serve as reservoirs for multiple viruses which are pathogenic to humans without succumbing to disease, is one of the hottest topics in immunology and virology. However, the authors do not provide a clear enough explanation of how their approach to study the transcriptome response following filovirus infection goes beyond what has been published in previous studies. This manuscript would greatly benefit from a discussion of its novelty in the Introduction and Discussion sections.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

Summary:

The manuscript by Jayaprakash et al investigates the response to the filoviruses Marburg and Ebola virus in Rousettus aegyptiacus bats, the natural reservoir of Marburg virus. The response to infection is investigated by comparing transcriptomes of different bat tissues in infected and uninfected bats. The manuscript groups the observed transcriptome changes into pathways that are impacted, and discusses how those pathways may cause subclinical infection in bats, compared to severe disease in humans. The data included also sheds light on bat immunology and reservoir characteristics more generally, which is particularly timely during the SARS-CoV-2 pandemic.

Major comments:

Are the key conclusions convincing?

The first hypothesis of the manuscript is that, rather than a change in a single immune pathway being responsible for the lack of response to the virus, the response will be systemic involving multiple inter-related pathways. The data show that this was the case after presenting convincing transcriptome analysis. The second hypothesis is that the differences in responses between bats and humans are due to evolutionarily divergent genes. The authors provide evidence for this in the transcriptome differences in the C-reactive protein, aspects of the complement system, iron regulation and M1/M2 macrophage polarization. The second hypothesis is broad, but there are clearly differences in the genes involved in humans and bats. Without mechanistic information on the function of the proteins/cells investigated, it is hard to determine that the changes the authors are observing are the cause of the different responses, rather than an effect of some upstream response, and so difficult to pin-point specific divergent genes. The authors wish to compare the response to the virus in bats to the better characterized human tissue responses, but because this relies on previously published work in humans, it is sometimes unclear whether "more bat-like" responses are definitely associated with positive outcomes in humans. As the benefit of certain responses in human infections can depend on the timing of the response, it might be helpful to include summarized human data in manuscript to aid comparison with the bat responses. For instance, the T-cell response section concludes "Bats mount a T cell response against the infection" but there is no discussion of the impaired but complex lymphocyte response in humans, so comparison is not possible.

Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

No, speculative discussion of potential drugs is already qualified as speculative, and adds to the understanding of the significance of the data.

Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation.

No

Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments.

N/A

Are the data and the methods presented in such a way that they can be reproduced?

Yes

Are the experiments adequately replicated and statistical analysis adequate?

Yes

Minor comments:

Specific experimental issues that are easily addressable.

Mock infected IHC should be included in Figure 1F to demonstrate the antibodies are not background.

Are prior studies referenced appropriately?

Mostly yes. The discussion of the T-cell responses in infection could be expanded to include more information on human responses

Are the text and figures clear and accurate?

Yes

Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

See comment in hypotheses- a summarized table of findings from previous studies of early responses to the virus would be helpful for comparisons to the bat response and for determining the second hypothesis.

Significance

Nature and Significance of the advance.

Bat immune responses to filoviruses are poorly characterized, and this paper contains much information that can aid future investigation of reservoir responses. This data also has broad application to other bat-borne pathogens.

Compare to existing published knowledge.

There is little about in vivo bat immune response to filoviral infections. Significantly, this report has a non-refractory response to Ebola virus infection in Rousettus aegyptiacus.

Audience

This paper would be of interest to filovirologists and those interested in zoonotics and bat immunology.

Your expertise.

I am a viral immunologist with >15 years' experience with filoviruses. Ms. Clarke is a senior graduate student whose thesis focuses on immune responses to filovirus glycoproteins.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 3 of the manuscript. The major points agreed by the reviewers are included below, as well as the separate reviews.

Summary:

The work presented is a major scientific achievement. This is the first functional reconstitution of any CO2 concentrating mechanism (CCM). The work has major implications for engineering of CCMs into crops for increasing yields: the authors have definitively identified a set of components that confer CCM activity in a heterologous host. As a bonus, the authors demonstrate a new way of generating a Rubisco-dependent E. coli.

Major points:

1) The EM images shown in Figure 5-figure supplement 1 should be presented as a main figure, not a supplement. The negative control is too dark and difficult to compare with the other micrographs. Moreover, it is concerning that the positive control (WT:pHnCB10) failed. It should be repeated as it would allow comparison of the putative carboxysomes to a native carboxysome and would greatly improve the quality and value of this figure.

2) For the benefit of a non-expert reader, the names of the 20 proteins and corresponding genes should listed in a Table, together with their function and the relevant references.

3) In Figure 3-figure supplement 1A, the authors should discuss why the gene csos1D is present in both pCB and pCCM.

4) In Figure 4B, the large variance in the OD600 after 4 days for CCMB1:pCB'+pCCM' cultures was explained as being due to genetic effects or non-genetic differences (line 1064). However, in Figure 3 - figure supplement 2B the measured growth kinetics did not show such big differences. Authors please explain.

5) Would be nice if the authors can demonstrate that Rubisco localizes to the putative carboxysomes by performing an experiment such as immunogold labeling. It would improve the claim that the observed polyhedral bodies are in fact carboxysomes. We leave the decision of such an experiment to the authors.

Reviewer #3:

In this manuscript, Urchs and colleagues use transductive conformal prediction (TCP) applied to rsfMRI functional connectivity data to predict autism in a subset of cases. The approach is novel for applying to autism research and also is pinpointed at a topic that is very much needed in autism - the problem of heterogeneity. The logic applied is that only a subset of autism cases will have powerful biomarker differences in terms of resting state functional connectivity and TCP is utilized to isolate that subset. Thus, while the approach is novel and maps onto similar kinds of logic in the realm of genetics of autism, the utility is somewhat limited, as TCP will not be able to tell us much about the majority of cases. This is the same problem with many highly penetrant genetic mechanisms that lead to high risk for autism. However, it is still an issue that the approach can only make statements about a very small percentage of the total autism cases in the population. Could the authors comment more on this issue/limitation? For instance, what does this biomarker in a small percentage of cases tell us? Are there powerful, specific, and homogeneous biological mechanisms behind such cases, whereas for the rest of the population the underlying mechanisms are highly diverse and not powerful enough to penetrate up into macroscale functional connectivity phenotypes? The result could help to generate new hypotheses focused on such a group. However, I think the authors should try to lead readers in discussing how to take such results further for new discoveries.

Besides this main issue noted above about the utility or meaning behind the novel findings, the following are comments about how to make the introduction more readable, and how to potentially better facilitate a reader's understanding of the analyses.

1) Introduction: I would suggest that some modifications need to be done to the introduction in order to make the ideas flow a bit better. The problem is that the authors are introducing a variety of complex and not necessarily easily linked information - e.g., risk from a variety of different types of genetic mechanisms, failure of neuroimaging classifier studies, and TCP. With a bit of effort and a couple re-readings it is clear that the logic the authors are using is that we have some understanding of how much risk there is from different types of genetic mechanisms, and we would like to understand how neuroimaging data might match up to that. Using TCP would hopefully allow you to do that, hence the goals of the study. This logic is not clearly spelled out as one reads the introduction however, because the different topics are either mixed together within a paragraph with little linking text to help the reader follow the logic, or the bits of information for each topic are segregated into their own paragraphs with little linking text and the beginning or ends of the paragraphs to help the ideas flow from one paragraph to the next. A good example of this is that the background paragraph to start with has these topics mixed together within the very first paragraph, and then the subsequent 3 paragraphs solely focus on each topic, without helping the reader understand why they are jumping from very different topics. By the time the reader gets to line 120 of the Objectives, then things are spelled out a little better, but the reader has to then go back and connect the ideas about how the authors are trying to compare how a TCP approach to identify a high risk imaging marker would match up against more well known risk markers at the genetic level. It may be the case that the manuscript here will get readers of various different backgrounds (e.g., autism researchers, those with expertise in genetics, neuroimaging, or machine learning). Few have expertise in all those areas, and for those individuals, it may be hard to understand how these different topics flow together and are linked in a specific logical way. The logic is there, but even for this reviewer, it required a couple readers to see how all this information lined up in a logic way to justify the study. Thus, I would suggest that the authors make changes to the writing so that the reader can clearly follow the logic without too much extra effort to connect what isn't written about how these topics are supposed to line up.

2) Methods: The methods and analysis are fairly complex. Can the authors make a figure that clearly lays out the analysis pipeline? It would help to have a visual that clearly outlines how the authors selected the subset of individuals from the larger ABIDE datasets, how the preprocessing was done, how the features were estimated, and how the TCP analysis was implemented with all the associated added aspects like the bootstrapping, etc. Furthermore, to facilitate understanding of the complexities of the analysis, can the authors create a GitHub repo that has all the reproducible analysis code that generates the results and figures produced in the paper, along with tidy data files that have the features used by the TCP model? Although in the data availability statement the authors write that a GitHub repo exists, having had a look through this, no tidy data files are available that the code can load up to have readers reproduce the analysis or figures. In addition, the code consists of only 4 brief R scripts. That code isn't easily readable with regards to how the analysis was done. The R code could be done in another way that is more in line with literate programming, such as an Rmd file, that has the analysis code, along with plain text to describe the different steps, and then the figures embedded within the html or pdf report that it creates when it is knitted in R Studio. There are also some Jupyter notebooks that show how the figures were generated. This was helpful to see and is what is needed for the R code too. In those Jupyter notebooks, it seems like there are certain tidy data files that those notebooks load, but they are absent in the repository and therefore, the readers cannot reproduce the analysis.

Reviewer #2:

This work represents an investigation into autism(s). For this purpose, multi-network inputs to transductive conformal prediction are used. This approach provides a measure for how much an individual resembles a pattern linked to autism(s) or healthy controls. The resulting predictions are translated to the population prevalence. The authors state correctly that their models are in the ballpark of what has previously been reported. However, they claim that their improvements with respect to predictions in the general population are a major improvement, achieved by a bias towards specificity of their model. While machine learning papers often do not report this translation it is also apparent that they easily could. Therefore, the novelty of this approach is not clear to me as it may be to the authors. This requires clarification in the context of the literature in addition to addressing the major concerns below.

1) The paper would benefit from a more in depth discussion of the literature. There have been more than 50 papers published using different pattern recognition approaches on ASD. It is important that the authors evaluate their work in the context of those findings. There are a bunch of reviews on pattern classification approaches in psychiatry in general and ASD in particular.

2) A slightly longer and more in-depth description of the methods section would help the reader, especially a description of the method used to calculate the relevant score.

3) Based on Figure 3 it is a bit unclear to me if the small number of individuals identified with higher HRS score indeed also show higher symptoms. This should be statistically tested.

4) The strongest confounding effects are usually induced by scanner differences, as both the discovery as well as the replication sample are multi-site samples. It would be important to investigate the effect of scanners on the proposed models. This is particularly problematic should there be disbalances between the groups across scanners.

5) Probabilistic predictive approaches have already been applied to ASD using for instance gaussian process regression (e.g. Ecker et al. 2010, Neuroimage). The paper would benefit by stating clearly how their method improves above the approach mentioned in this referred paper as well as other approaches in ASD. The adjustments of the prediction to the population prevalence is a minor achievement.

6) The authors discuss: "Although our model made only few predictions, those predictions carry a much higher risk of an ASD diagnosis for the identified individuals. The result is a prediction with a much higher specificity (99.5% compared to 72.3% and 63% for traditional approaches, Heinsfeld et al., 2018; Abraham et al., 2017) and much lower sensitivity (4.2%, compared to 61% and 74% respectively). It is thus important to point out that here we have not proposed a better prediction learning model, but rather addressed a different objective." However, sensitivity and specificity are always a trade-off and dependent on the decision threshold. You can bias this for either of the two. For probabilistic models this is easy to do by adjusting the decision threshold to the population prevalence of a disorder. It is also possible to determine a decision margin which will naturally lead to higher performance, similar to the approach presented here and has been done and proposed earlier.

Reviewer #1:

This is a well-written manuscript examining prediction of ASD diagnosis from resting-state fMRI data. The primary innovation is the application of Transductive Conformal Prediction (TCP), which quantifies the confidence with which one can accurately make a prediction. The authors show that they can identify a functional connectivity (FC) signature with high PPV for a subset of patients.

The approach is certainly interesting, but it also seems circular. As I understand it, predictions are limited only to individuals who can be classified with high accuracy. A priori, we might expect that these people would be patients with severe illness, and the results show that the subset of patients who are correctly identified do have more severe symptoms. It therefore seems unfair to compare the high PPV of this method with other approaches, when the current method, by construction, focuses only on those cases who are easier to classify (whereas others don't). Could the authors please clarify whether this interpretation is accurate?

Related to the above, the PPV of the test is high, but this is only one side of the coin. The sensitivity is very low and I imagine the NPV is also low. Given its low sensitivity, It does not seem correct to speak of the FC signature as a risk marker, since many people at risk (indeed with a diagnosis) do not show it. In practical terms, it seems like a positive result with this FC marker is conservative, relatively accurate indicator of someone's risk for a severe form of ASD, but a negative result carries almost no information at all. What is the practical utility of such a marker, given that severe autism should be evident from clinical observation? That is, how could the current results add value to clinical decision-making? If the FC signature could be detected in newborns, it would be of value, but this analysis is conducted in adults after diagnosis has been established.

The methods section indicates that the approach prioritises specificity, but the reasons for this decision are unclear.

How were site differences addressed in the analysis?

It would be useful to see how results vary as the 5% threshold is varied.

The evidence for cluster structure in Fig 1b seems quite weak.

The Figure 1 caption requires greater detail explaining what is actually shown in the plots.

Were any of the participants taking psychotropic medications? to what extent could this have impacted the findings?

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Summary:

The reviewers shared a number of concerns in common, as outlined in their detailed reviews. In addition, the following points were raised upon further discussion between the reviewers:

-A comprehensive analysis of the potentially confounding effect of site differences is required

-The potential circularity of the method - classifying only cases that can be confidently classified - and practical limitations of this approach should be discussed in greater detail. The algorithm is biased towards specificity. This could also be achieved using probabilistic machine learning approaches by, for instance, adjusting the decision threshold to the population prevalence or by defining a margin for cases for which you do not make a decision.

-The findings are considered in relation to population prevalence rates, but the algorithm is not applied to a population sample. It seems likely that the classifier would not detect cases with the same accuracy in a population sample. If this claim is made, it needs to be explicitly tested.

-The passage "The result is a prediction with a much higher specificity (99.5% compared to 72.3% and 63% for traditional approaches, Heinsfeld et al., 2018; Abraham et al., 2017) and much lower sensitivity (4.2%, compared to 61% and 74% respectively)." seems problematic. If you calculate the balanced accuracy for the current approach, of Specificity + Sensitivity/2, you end up slightly above chance accuracy. The other papers actually perform better.

Reviewer #3:

The article by Delabouglise and collaborators presents a longitudinal analysis of farms in Southeast Asia to understand farmer behaviours in response to disease outbreaks in poultry. The study is original in its design and the results are important for the prevention of avian flu epidemics in the region, as they suggest that smallholder farmers are more likely to sell their poultry to traders following outbreaks, which could contribute to the rapid disease spread. There are important differences in terms of response to outbreaks (harvest, vaccination, etc.) between large and small farms, which suggests that targeted sensitization campaigns and programs are necessary to modify these behaviours. The article is well written, although the discussion needs some work to lay out the limitations of the study and to expand the practical implications of the study in terms of policies or interventions to put in place.

I have a few comments to improve the manuscript:

Introduction:

-I am uncertain about whether the term cohort applies to their study, as the unit of follow-up are farms but they're not following the same individuals (chickens) over time. I would suggest changing the term to longitudinal study.

Methodology:

-How reliable is the classification of outbreaks with and without sudden deaths? Are farmers able to recognize fast the onset of symptoms and then a death within 24h after the onset of those symptoms? I imagine that misclassification can happen, so I would mention this as a potential limitation.

Results:

-Table 2: it would be much more easily interpretable if variables are described fully, with the function used for transformation in brackets. For example, instead of "square root of Nbc", I would include "Number of broiler chickens in the farm (sqrt)", and so on.

Discussion:

-I think the different limitations of the study should be explained and discussed. For instance, 1) the use of a proxy for weight instead of weight itself, 2) potential misclassification of outbreaks (see above), 3) some behaviours may depend on events happening in longer time frames, for example the previous year, but this is not accounted for in the models.

-Also, the harvest of chickens could be greatly influenced by economic needs of the household (a family event, an economic shock, disease, etc.), especially for smallholder farmers in the developing world who may use chicken as a form of cash savings. I am actually surprised that this was not included in the questionnaires, and I think it's an important limitation that should be discussed (and appropriate literature referenced).

-I feel that the discussion lacks insights into practical implications/solutions coming from this study (policies, interventions, etc.). Given the results, what can the government or NGOs or international organizations implement in order to reduce the risk of future outbreaks? This part should be expanded and be more specific.

Reviewer #2:

This manuscript addresses an important gap in knowledge of infectious disease emergence and spread within small-scale poultry production systems. The study design allows for analysis of longitudinal epidemiological and human behavioral data, not commonly found in animal health research; the statistical analysis is well thought out and robust. The authors find that farmers with small flocks respond to disease outbreaks with the rapid sale of sick birds to traders, and that despite government-supported programs, there is little uptake of vaccination in this population. Findings point to future areas of research that could inform policy development or better target activities to reduce disease transmission within similar poultry production systems.

Reviewer #1:

General assessment:

The manuscript is very well written, easy to follow despite the substantial statistics, and has a clear goal that the authors address with strength. The study is highly relevant in the context of emerging infectious diseases, and addresses one of the main understudied candidate drivers of emergence. The study design allows a thorough analysis of the observed patterns, providing highly useful insights into the potential ways in which avian influenza can spread.

Substantive concerns:

I have no substantive concerns. The longitudinal study seems to have been designed and conducted well, allowing the incorporation of potentially important variables in the statistical models. The authors made great and responsible use of MGAMs, and clearly have an excellent background in statistics. I have no reservations or concerns about any aspect of the statistics. In fact I would like to complement the authors on the way in which the methods were described and results were reported, which was done in a clear way despite the large and potentially confusing number of results.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Summary:

Your manuscript surveyed 53 poultry farms in Southern Vietnam and identified that small scale farmers with lower sized flocks were more likely to rapidly harvest and sell disease birds to mitigate loss of profit. This finding is of great potential importance for developing prevention efforts for introduction of avian influenza into human populations.

The reviewers were all highly complimentary of this paper. They all felt the manuscript was methodologically sound, clearly written, highly original and of substantial public health and policy relevance. Particular noted strengths were appropriate use and description of mixed-effects general additive models, appropriate study design and the inclusion of all raw data for public use.

Reviewer #3:

PREreview of "The gene cortex controls scale colour identity in Heliconius" Authored by Luca Livraghi et al. and posted on bioRxiv DOI: 10.1101/2020.05.26.116533

Review authors in alphabetical order of last name: Monica Granados, Vinodh IlangovanORCiD, Katrina Murphy, Aaron Pomerantz

This review is the result of a virtual, live-streamed preprint journal club organized and hosted by PREreview and eLife. The discussion was joined by 17 people in total, including researchers from several regions of the world.

Overview and take-home message:

In this preprint, Livraghi et al. present noteworthy advances in evolutionary biology by characterizing the role of cortex gene in multiple Heliconius butterfly species, which is responsible for the wing patterns: yellow bar or the Type I scale cell fates (white/yellow). The authors identified cortex gene’s major role in sympatric speciation, the modulation of convergent wing patterns, and the regulation of scale identity in multiple Heliconius species, which naturally have different niches to help explain different co-mimetic morphology. Livragi’s team provides strong evidence for the cortex gene as one of the earliest regulators and its ability to set the differentiation of scale cells in a molecular switch fashion from yellow to red/black at a particular development stage through distal localization. This important discovery on the role of cortex gene fills a gap in our existing knowledge about the gene’s ability to control scale cell identity and wing color patterns. Since this work is of significant interest in evolutionary biology, we outlined some concerns below that could be addressed in the next version.

Positive feedback:

1) We strongly recommend this preprint to others/for peer review. In addition, we recommend this article to trainees as educational material to learn evolutionary developmental biology through interactive tutorials.

2) The authors have provided a good amount of novel results and have utilized current tools to address their questions.

3) This research fills a gap in our understanding of wing patterning in Heliconius while doing so in a very comprehensive way across multiple species and using techniques that systematically detail the association between gene expression and phenotype.

4) It was interesting to learn that the cortex gene doesn’t follow the typical pattern gene paradigm. We do not have many examples of integrator genes like cortex, which give binary outputs from a network of genes and integrate elements to produce a singular output.

5) This is a textbook example and is important for evolutionary development and mimicry studies. It is hard to find and/or work with a developmentally important gene that is amenable for genetic modification and still be able to work with viable offspring and have it be relevant for evolution.

6) The current cortex protein data as seen in Figure 6 adds novel data to the manuscript.

7) Thanks to the authors for setting a great example of showing modeling information. The graphics are visually appealing and convey complex information well.

8) This preprint sets up a good next step of how cortex evolved in a more broad context. We know the cortex gene is potentially implicated in wing pattern evolution in other distantly related butterflies and moths (e.g. peppered moth Biston betularia) and in possible roles of evolution/speciation by pattern changes due to genomic inversions at cortex locus.

9) The authors did a good job of creating a well-composed manuscript. Yellow bar with one species had a contradiction but did reconcile with further research questions.

10) Definitely, [the results are likely to lead to future research] especially with understanding how a cell cycle regulator affects developmental cell fates in terms of these scale colors and structures.

11) Antibodies can open up future research. This research team figured out three elements and there are possibly more to explore. Future research might investigate how cortex possibly regulates endocycling and what this means for color identity determination.

Major concerns:

1) The use of the term “race” to define butterflies with specific phenotypes needs to be revised to clines or strains or variants. “Race” is a social construct and not a biological reality and we strongly suggest revising this term.

2) The authors state that cortex and dome/wash genes are controlled by inversion (see Line 375, page 19). Does the strain they engineered have/carry the inversion ?

-We are aware that inversion for species is complex - strains, genetic background - starting material for inversion.

-Inversion events occurred millions of years ago in the loci contributing to the wing pattern. Authors describe the first generation of CRIPSR knock-outs in Heliconius sp. and hence we suggest to include further information.

3) We strongly suggest the authors elaborate on their qRT-PCR analysis pipeline. Did the authors follow MIQE guidelines in their quantitative real time PCR assays?

4) More explanation could be provided for cortex protein experiments. Figure 6 could explicitly say what developmental stage/time after pupation (they report this in the Methods section) and the rationale behind presenting data for this stage in development.

-If a systematic developmental time series of cortex protein expression is observed using immunostaining, we suggest adding the data. Otherwise we request the authors to comment on the rationale behind selecting this particular stage of development.

5) We recommend the authors mention institutional or local animal care ethical approval and safety regulations in the field working on Heliconius sp. for setting best practice reporting standards.

6) We suggest to clarify the lack of a clear correlation between in situ stains and the mutational effects of cortex CRISPR knock-outs.

7) Please add statistical analyses in figure legends, e.g. Figure 2 lacks statistical analysis information. Which test was performed and why? A statistical analysis subsection under the Methods section could be useful.

8) Could a sized-down Figure S10 be added to Figure 6 in the manuscript to provide more information about the nuclear ploidy and cortex antibody signal? Even no association is informative and helps the reader think about the connection between color/endopolyploidy.

Minor concerns:

General

1) We request authors to revise the introduction section allowing an easy to comprehend information on gene regulatory complex affecting each patterning region.

2) We strongly recommend minor rephrasing of the on/off switch to guide non-experts in evo-devo biology.

Figures

1) Figure S10 has a couple of typos - ‘localisation’ and ‘punctae’ in the first sentence of the figure caption.

2) It will be helpful to guide the readers, if a high-level phylogenetic tree mapping the related Heliconius’ evolution is presented in Figure 1. We suggest a compass guide to be added in the map of Figure 1b.

3) The scale bar is missing in Figures 6a and 7a.

4) In Figure 4, some of the mosaic KOs are very apparent and others are not especially for researchers unfamiliar with butterfly CRISPR, e.g. H. charithonia. I might suggest highlighting or using arrows to indicate the mKO regions.

5) We request the authors to consider reflecting on the distribution of samples in qPCR data superimposed on box-whisker plots .

Sufficient Detail

1) More information about the genes would be helpful, such as accession numbers and annotated gene information rather than the complete genome data.

-Might not be able to repeat CRISPR from the details in the Methods section. If the gene information is not well annotated as a model system then it is difficult. What about Heliconius? It might be helpful to report the scores for low off-targets.

-Non-standard genetic model systems present a challenge particularly to create genomic resources.

2) Multiple people mentioned not able to repeat in situ hybridization methods from the available information on methods. The hybridization conditions for thicker whole mounts were not fully explained.

3) Please provide more information about the number of animals.

Data Accessibility

1) We appreciate the authors adding supplemental information as figures and we request to report data files associated with the manuscript.

2) R code was used for morphometric analysis - this is difficult to track from pay walled reference mentioned and thus a problem. We request to make this analysis information/pipeline available openly.

3) Please include supplemental information on the microscope settings and metadata of images used for analysis explicitly.

4) High-resolution images of the CRISPR mutants could be provided in a supplemental/data repository.

5) Providing gene sequences used in this study will be very helpful rather than the SRA repository, especially probes used for in situ and sequences targeted for CRISPR.

Acknowledgments:

We thank all participants for attending this preprint journal club. We especially thank those that engaged in the discussion. Their participation contributed to both a constructive and lively discussion.

Below are the names of participants who wanted to be recognized publicly for their contribution to the discussion:

-Monica Granados | PREreview | Leadership Team | Ottawa, ON

-Vinodh Ilangovan | Labdemic - Founder |Postdoc | @I_Vinodh

-Katrina Murphy | PREreview | Project Manager | Portland, OR

-Aaron Pomerantz | UC Berkeley/Marine Biological Laboratory | Ph.D. Candidate | Berkeley, CA/Woods Hole, MA

Reviewer #2:

This manuscript explores the role of the gene cortex in the specification of wing scales in the butterfly genus Heliconius. Species of Heliconius butterflies are notorious for their reciprocal mimicry of wing color patterns. Several genes are known to control variation of specific color pattern elements within and between species, cortex is one of them. The authors combine RNAseq analysis across wing development, in situ hybridizations, antibody stainings and analysis of crispr somatic mutations to dissect the role of cortex in the specification of scales. Their main claim is that cortex imparts scale identity (color, morphology), namely type II and type III identity.

Although this paper includes a substantial amount of work and a number of interesting observations, I am not sure what can really be concluded in the end, and several results would need follow-up experiments to reach a stable conclusion.

The strongest part, in my opinion, is the analysis of somatic mutant clones of cortex in the wings of different species. The authors show that the lack of cortex consistently results in the conversion of type II and type III scales into type I scales, and thereby demonstrate the necessity of this gene for type II & III identity. This is solid, interesting, but not a novel concept from a genetic or developmental biology point of view. There are countless examples in the 1990s literature of genes whose mutations results in such shifts in cell identity (e.g., poxn and cut in the peripheral nervous system of flies).

From this result, two questions emerge: how and when does cortex assign this identity during development? And how does cortex explain the variation in color pattern among Heliconius morphs and species? Although the paper discusses these two questions, I find the answers unclear and the results confusing.

The authors first examine the expression dynamics of cortex. They re-annotated the 47-gene genomic interval where cortex maps and analyzed the differential expression of all genes in the interval, across developmental stages, across species and morphs and also compared wing compartments. Their main conclusion is that cortex is the most likely candidate in this interval to explain color pattern variation. I am not sure why the authors did this. I thought this was already clearly established from a previous paper (Nadeau et al. 2016, Nature). Moreover, the explanations of the differential gene expression (DGE) analysis are often too shallow to really understand what the authors really did, including the method description. The figures are poorly annotated and it's difficult to understand if there are replicates in the RNA-seq analysis (see minor comments). One striking result from this part, is that the DGE suggests that cortex is differentially expressed in the the 5th instar larvae between 2 morphs of Heliconius erato and 2 morphs of Heliconius melpomene, but the differential expression goes into opposite directions between this 2 species. How could the same phenotypic variation between morphs of 2 species be caused by opposite DGE? They authors note that it is interesting but do not comment or analyze further.

They pursue their investigation with in situ hybridization on 5th larval instar wings and mitigate the notion of a spatial correlation between cortex transcripts spatial distribution and color patten elements proposed by Nadeau et al., 2016. Here again, the figure would benefit from better annotation. The authors indicate subtle differences in the local distribution of cortex transcripts between morphs but do not really conclude anything from their observation. They also give no indication of sample size or replicates, which I find unsettling given the noise associated with this experiment. I am not sure what this figure really adds to the published work, or to the present manuscript.

Finally, the authors examine the distribution of Cortex protein in late (2-day pupa) developing wings with a polyclonal antibody. They find, surprisingly, that the protein is distributed more or less uniformly in the wing epithelium and localizes to the cell nuclei. While this is very different from the patterned transcript distribution, it is consistent with the somatic mutant clone analysis that showed that any mutated cell at any position of the wing displayed a phenotype. But this opens many questions: what is the origin of the apparent difference in expression between protein and transcripts? Is cortex secreted and it diffuses across the wing? Or is the transcript expression spatially dynamic and the protein distribution revealed by the authors reflects the temporal integration of this expression? And if Cortex is present and functional across the wing, how does it produce discrete pattern elements?

The authors conclude their paper with a figure suggesting that cortex specifies typeII/III scale identity early during wing disc development and that the distinction between type II and type III is subsequently governed by the gene optix at a later stage. But what substantiates the idea that cortex imparts cell type identity early on? What does Cortex larval (5th instar) distribution look like? Is it as uniform as that of later stages? The data presented here do not offer the temporal or functional resolution to support this conclusion.

In conclusion, this paper shows that the mutation of the gene cortex results in scale type transformation, but fails to explain or suggest how this may happen during development. It also does not suggest how cortex may control the "fantastically diverse" pattern variation in Heliconius.

Reviewer #1:

This is an interesting but complex study that examines the role of a few genes in a previously mapped interval in being the "switch" gene that regulates the presence or absence of a yellow band in the wings of Heliconius butterflies. The study first examines whether there is a correlation between expression level of several (47) genes in the mapped interval in developing wings (or parts of wings) in two separate species of Heliconius each having a race with the yellow band and a race without the yellow band. This part of the study highlights three genes (among others) that show some pattern of differential regulation but shows that there is no simple correlation between the expression level of these three genes in either larval or pupal wings and the presence of the yellow band. The authors then examine the function of one of the genes in the interval, cortex, in scale color development by using CRISPR. They find that cortex crispant individuals display color changes across the whole wing, not just in the region of the yellow band. In particular the black scales (Type II) become white or yellow (Type I), and the red scales (Type III) also become white or yellow (although this last transformation is not documented at the SEM level). The authors examine, once again, the expression domain of the cortex gene, this time during pupal development with an antibody, and they find that the gene is expressed across the whole wing, supporting its functional effects also across the whole wing. They observe that cortex is expressed in multiple punctate domains in the nuclei of scale building cells, which are polyploid cells, and in a single punctate domain in the nucleus of non-scale building epidermal cells, which are not polyploid. They then test whether perhaps there are more of these punctate nuclei in the region of the yellow band, but they find no such correlation.

In the end the authors try to argue that either 1) cortex is the yellow-band switch gene they are after but that the switch is not in the form of a typical spatially expressed gene (in the shape of the yellow band) but perhaps in the form of some threshold or heterochronic mechanism (not clearly explained), or that 2) another gene in the mapped interval, not examined for function in this study, is instead the switch genes they are after, and which may (or may not) interact with cortex in the differentiation of the yellow band.

I believe the authors are trying hard to implicate cortex in some way, as the yellow band switch locus, but the data just does not support this. Instead the authors implicate cortex in scale color identity (the title of the manuscript). However, given that cortex (alone) cannot control a specific color either, because the effect of cortex on color is different in different parts of the wing, their model for how cortex acts is too simple and does not fit their data. A combinatorial genetic code for both scale color and morphology (see below), where cortex is simply one of the players (rather than a major switch/homeotic gene) is required to explain the data in this manuscript.

Furthermore there are several data missing from the manuscript that need to be added to support some of the conclusions drawn, and several other data that would be important to add for purposes of data replication across labs.

1) The authors claim that cortex converts Type II (black) scales into Type I (white/yellow) scales but their SEM data and scale morphological measurements presented in the supplement don't fully support this conclusion. These transformations vary from species to species (e.g. H. melpomene and H. erato show different degrees of transformation) and only some features of the scale are actually transformed (e.g., cross rib periodicity in both species, and scale width and length and ridge periodicity in H. melpomene). The remainder of the measurements show that cortex is not sufficient to convert scale Type II into scale Type I.

2) I suggest that the definition of the scale types presented should be made more explicit. What are scale types I, II and III really? In line 87 it is mentioned that these scale types are based on scale color and on scale morphology but what follows is just a description of the pigments found in each scale and not their morphology. Furthermore, the data presented in the manuscript suggests that color and morphology can be uncoupled with genetic perturbations of cortex, so is it even useful to stick to this scale type nomenclature going forward? Something to consider.

3) There is a need for a new figure showing how the scale morphological measurements were actually conducted. There is no scale bar in the SEM images of yellow and black scales and this should be added. The SEM images used to represent a typical yellow WT scale and a transformed yellow scale of H. melpomene (in Figure 7) show very different densities of cross-ribs (but I am not even sure what exactly is being considered a cross-rib), yet the graph indicates that there is no difference between these scale types. This is confusing and needs clarification. Make sure you look up scale morphology nomenclature in Ghiradella 1991 (Applied Optics) to make sure you designate ribs (crossribs) and microribs appropriately. There seem to be quite a lot of differences in microrib density across Wt scales and transformed yellow scales in H. melpomene.

4) The authors claim that cortex converts Type III (red) scales into Type I (white) but they only describe conversions of Type II (black) into Type I (yellow) scales at the SEM level and don't provide any SEM images or quantitative data for the red to yellow, red to white, and black to white scale transformation. Adding these data is important to support the conclusions of the study.

5) I suggest the authors remove the dome-t and dome/washout gene data from the manuscript as 1) nothing about these genes is mentioned in the abstract; 2) the expression of these genes doesn't correlate with presence of the yellow band; 3) the genes are not investigated at the functional level; 4) the whole gene duplication issues surrounding these genes make the whole manuscript more difficult to read and does not, in the end, contribute to the main story that yielded results - which is the function of cortex in scale development. The function of these genes might still be worthy of investigating using CRISPR at a later date, and perhaps it would be useful to include the expression pattern data in that subsequent paper. This is merely a suggestion that I believe will make this manuscript less heavy and easier to read by focusing the reader's attention on the main points of this story.

6) Pigmentation and scale morphology is most likely controlled at the pupal stages of wing development and by measuring RNA levels of candidate switch genes at just two time points during pupal development (36hrs and 60-70 hrs after pupation) you may not have sampled the correct time window for yellow band differentiation. Several genes are expressed only during the first 16-30 hrs of pupal development, in species that need 7 days for pupal development (see Monteiro et al. 2006 for genes such as Wg, pMad and Sal) so sampling wings (for RNA-seq and antibody stains) at 36hrs and 60-70 hours may not be an ideal sampling strategy going forward.

7) The authors mention that because cortex causes changes in both scale color and morphology this suggests "that cortex acts during early stages of scale cell fate specification rather than during the deployment of effector genes". This conclusion needs more discussion. Matsuoka and Monteiro (2018) showed that knockout of the gene yellow, an effector gene at the end of a gene regulatory network for melanin pigment production, also led to both changes in scale color and morphology. These authors proposed instead that absence of certain pigments on the wing, such as dopa melanin, caused chitin to polymerize differently and form an extra lamina that prevent the windows from forming in the scales (just as seen in cortex mutants). The authors should consider and evaluate this alternative explanation in their discussion.

8) Did the authors examine whether there were protein coding changes between the 47 genes in the mapped interval between the yellow and black races? Please mention whether this was done. Please also upload the sequences of the genes that were studied and provide accession numbers for these sequences.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Summary:

The topic of your work is timely and intriguing, but the reviewers raise several issues with the study. For example, the reviewers propose that the major conclusions of the manuscript are not supported by the data presented, and that a full set of SEM data across all scale type color transformations should be presented. Given the results presented, the relationship between cortex expression and the actual pigmentation remains unclear, and the sole phenotypic analysis is insufficient to make conclusions about the role of a gene in producing pigmentation pattern variation.

Reviewer #3:

In this manuscript Hashmi et al describe the emergence of an endoderm population in a gastruloid model. They observe that endoderm cells are positive for E-Cad, likely express E-Cad continuously from an epiblast state, initially form small islands, and finally coalesce into a larger endoderm region at the pole of the gastruloid. There are several issues with this manuscript in its current form.

1) No evidence is provided that there is a relationship between how endoderm forms in this gastruloid model and in vivo. In fact, endoderm is believed to derive from a restricted area in the anterior primitive streak. This is evident from the mouse imaging data of Mcdole et al Cell 2018 as well as from more recent genetic labeling experiments (Probst et al bioRxiv 2020). It is well known that cells of different germ layers may self-segregate and this may drive the behavior observed here downstream of heterogeneous differentiation in the gastruloids, but that is not necessarily the mechanism which occurs in vivo. The authors suggest that their experiments show something about endoderm formation in vivo without addressing this point which substantially diminishes from the interest of the manuscript.

2) The authors suggest that this view of endoderm differentiation, which doesn't require full EMT is novel, however, much of the observations here are already known. It is known that future endoderm cells do not down regulate E-Cadherin but instead must continue to express it. They also are known to migrate collectively rather than as single cells in a cadherin-dependent way (Montero et al Development 2005; reviewed in Nowotschin et al Development 2019). The authors should discuss this literature and make clear which aspects of the proposed mechanisms are novel.

3) The authors are assessing the status of EMT based on a single marker, E-Cad. If this is a major point of the manuscript other markers e.g. Snail, N-Cad should be examined.

4) It is well known that embryoid bodies form an outer layer of visceral endoderm, e.g. Concouvanis & Martin Cell 1995, Doughton et al PLOS ONE 2010. None of the markers here are exclusive to definitive endoderm (including Sox17 which is used throughout, see Artus et al Dev Biol 2011). The authors should address the possibility that their observations may be consistent with a similar mechanism and may not reflect definitive endoderm differentiation.

Reviewer #2:

In this manuscript, the authors proposed a new mechanism of endoderm formation in 3D gastruloid models based on cell migration and fragmentation. Specifically, they found that E-cad is first uniformly expressed inside mESC aggregates. After exposure to Wnt agonist Chiron (Chi), a gradual repression of E-cad and an increase of T-Bra were detected. Cells in the core are tightly packed and express E-cad. T-Bra expressing cells are sparsely wrapped around the core. A directed flow of E-cad expressing cell islands surrounded by T-Bra expressing cells help to accumulate E-cad expressing cells to the tip of the aggregate and form endoderm domain. I think the dynamical expression of E-cad and T-Bra and the directed cell flow reported in this manuscript are interesting. The results and videos have shown that the elongation and formation of endoderm region is a collective cell behavior rather than single cells undergo epithelial-to-mensenchymal transition. But I am not convinced that the process is done based on the three-step mechanism proposed by the authors. Moreover, I am not sure if this phenomenon really happened in mouse embryo development, giving the considerable differences between gastruloid model and embryo. Since there are methods culturing mouse embryo in vitro up to the early organogenesis stage, I would suggest the authors provide more evidence showing that the proposed mechanisms might also happen in vivo.

In addition, the manuscript provides too little information to understand the phenomenon. And they did not clearly introduce experimental and computational methods they used to acquire the results. I listed some of my comments below.

Major comments:

1) Did all 3D aggregates become elongated shape in the presence of Chi? If not, what do E-cad and T-Bra expressions and cell migration dynamics look like in those spherical aggregates? Without Chi, inside the spherical aggregates, do they also have cell migration since the aggregates keep growing larger?

2) When did the collective cell migration start? Right after exposing to Chi? Or after some percentage of cells become T-Bra positive cells? Did the gastruloid keep elongating with directed cell flow inside it when cultured for a long time?

3) Are the collective cell migration driven by the T-Bra cells? Is it a spontaneous property of E-cad cells when the E-cad cell density exceed some critical threshold (e.g. glassy dynamics)?

4) Does the elongation and migration dynamics depend on the concentration of Chi, size of the aggregates? I noticed the authors used different initial seeding densities.

5) For the elongated cell aggregates, one side of cells express E-cad. How about the other side of cells? Did they all become mesoderm-like (T-Bra+) cells?

6) Many results are only based on several (3 or 4) gastruloids. For example, figure 1 (d) (e), figure 2 (b), figure 3(c). And in Figure 4 (b), the authors only quantify 13 junctions, probably in the same gastruloid. Due to the heterogeneity among the gastruloids, I am not sure how repeatable the experiments are. Can those observations really reflect phenomenon happened inside the majority of gastruloids? I think the authors should provide some quantifications of the percentage of observing the reported results among a large number of gastruloids.

Unclear results or experimental descriptions:

1) Can the authors show a schematic of the experimental process, such as the time of adding Chi and fixation?

2) 'We find that 30/37 ... set to 0.125.' How did the authors define and calculate the elongation ratio and E-cadherin polarization ratio? How did the authors define the elongation threshold?

3) Figure 1 (a): what is the y axis? 1 (d): how did the author measure the E-cad and T-Bra expression? Fixing at different time points or live imaging? If it is live imaging, is the acquisition process influenced by adding and removing Chi? 1(e) how can the authors get continuous results for polarization?

4) Figure 2 (b) Are those dots represents the nuclear position? Can the authors provide the 3D view of the whole gastruloid? (c) What information the authors are trying to get from the connectivity graph?

5) Figure 3 (a) What are those white dots in the images, also in movie 6? Can the authors replace t1, t2, t3, t4 with the real time, such as 24h, 36h? (d) How did the authors calculate the intensity? How did the authors normalize the intensity? The schematic in (b) is hard to understand. What do the light and dark colors represent? How did the authors measure theta_1 and theta_2, especially in 3D situation? More quantitative information should be acquired from (a).

6) I am not able to identify islands of E-cad expressing cells in Figure 3 (a) and movie 6.

Reviewer #1:

General assessment:

The manuscript by Hashmi et al describes the emergence of endoderm-like cells in a stem cells based embryo model. The particularity of the protocol is that it stimulates transition through an epiblast-like state, then differentiation towards mesoderm after a pulse of Chiron, a Wnt agonist. In those conditions, islets of E-cadherin positive cells emerge, surrounded by Ecad+Brachyury+, then Brachyury positive cells. Those islets fuse together at the tip, possibly due to distinct surface tension and directed cell movements, and express endoderm markers such as Sox17 and FoxA2.

It is an original approach and concept, raising new questions and possibilities about the mechanisms of endoderm emergence in the mouse embryo. The manuscript is well written and clear.

Concerns:

1)The data would benefit from increased clarity in stating, for each experiment, the proportion of aggregates in which a given phenomenon was observed, as well as the number of cells counted in each aggregate, in particular in supplementary figures.

2) For the migration analysis, it could be interesting to distinguish each cell trajectory in order to distinguish behaviours of the subpopulations.

3) In terms of the surface tension analysis, performing a similar analysis at different timepoints might be helpful to understand how the islets come to fuse at the tip.

4) I am not sure about the specificity of the gata6 staining, not that it adds a lot to the story.

5) The authors might want to discuss how those aggregates evolve, and whether the endoderm-like cells have a potential for further differentiation.

Conclusion:

Overall it is an interesting and original observation, well substantiated. More details on the quantification methods would help convince about the solidity of the model: chance of obtaining those cells, amount of cells of each subpopulation including those described in supplementary figures, technical possibility of sorting them for transcriptome analysis etc.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Summary:

The reviewers agree that the manuscript reports an interesting and original observation in gastruloids. However there is currently no evidence to propose that such a mechanism would be present in embryos. Additionally, there is a consensus that the methods are not sufficiently explained, the reproducibility is not clearly quantified, and some claims would require a larger number of aggregates/cells to be solid.

Reviewer #3:

This is an interesting study addressing a very relevant and exciting topic. The study investigates the contribution of auditory subcortical nuclei and the cochleae using physiological recordings while listeners differentiated words in different noisy-speech conditions. It is a valuable approach to consider contiguous measures along the auditory pathway during a single behavioral measurement.

However, I have several substantial concerns with the design, conceptualization, data analysis and interpretation of the results. I have had challenges to understand the hypotheses and rationale behind this study. A number of experimental paradigms have been employed, including peripheral/brainstem physiological measure, as well as cortical auditory responses during active versus 'passive' listening. Different noise conditions were tested but it is not clear to me what rationale was behind these stimulus choices. The authors claim that "our data comparing active and passive listening conditions highlight a categorical distinction between speech manipulation, a difference between processing a single, but degraded, auditory stream (vocoded speech) and parsing a complex acoustic scene to hear out a stream from multiple competing and spectrally similarly sounds" (lines 401-403). This seems like too much of a mouthful. I cannot see that the data support this pretty broad interpretation.

Despite maintaining iso-difficulty between vocoded vs speech-in-noise (SIN) conditions, the authors neither address (a) the fundamental differences in understanding vocoded vs. SIN speech nor (b) any theoretical basis for how the noise manifests in vocoded speech. If the tasks are indeed so obviously 'categorically' different - then it should not be surprising they engage different processing (the 'denoising' may not be comparable). I would prefer much more clearly defined and targeted hypotheses and a justification of the specific stimulus and paradigm choices to test such hypotheses. It appears to me that numerous measures have been obtained (reflecting in fact very different processes along the auditory pathway) and then it has been attempted to make up some coherent conclusions from these data - but the assumptions are not clear, the data are very complex and many aspects of the discussion are speculative. To me, the most interesting element is the reversal of the MOCR behavior in the attended vs ignored conditions. However, ignoring a stimulus is not a passive task! It would have been interesting to also see cortical unattended results.

Overall, I'm struggling with this study that touches upon various concepts and paradigms (efferent feedback, active vs. passive listening, neural representation of listening effort, modeling of efferent signal processing, stream segregation, speech-in-noise coding, peripheral vs cortical representations...) where each of them in isolation already provides a number of challenges and has been discussed controversially. In my view, it would be more valuable to specify and clarify the research question and focus on those paradigms that can help verify or falsify the research hypotheses.

Reviewer #2:

This is a highly ambitious study, combining a great number of physiological measures and behavioral conditions. The stated aim is to investigate the role of the descending auditory system in (degraded) speech perception. Unfortunately, the study was not designed with a clear a priori hypothesis, but instead collected a large number of measures, which were fitted together post-hoc into a particular interpretation, based on a selective subset of the data. Even more problematically, the experimental design is based on a fundamentally flawed premise, which undermines the validity of the interpretation. A final practical problem is that the most important comparison is made between conditions that were measured in separate experiments, with different participants. Given the notoriously poor reproducibility of across studies of these measures in this research field (suggesting large inter-individual variations), this casts a serious doubt on the interpretability of the observed difference.

Specific comments:

1) A core premise of the experiment is that the non-invasive measures recorded in response to click sounds in one ear provide a direct measure of top-down modulation of responses to the speech sounds presented to the opposite ear. This is not acknowledged anywhere in the paper, and is simply not justifiable. The click and speech stimuli in the different ears will activate different frequency ranges and neural sources in the auditory pathway, as will the various noises added to the speech sounds. Furthermore, the click and speech sounds play completely different roles in the task, which makes identical top-down modulation illogical. The situation is further complicated by the fact that the clicks, speech and noise will each elicit MOCR activation in both ipsi- and contralateral ears via different crossed and uncrossed pathways, which implies different MOCR activation in the two ears.

2) The vocoded conditions were recorded from a different group of participants than the masked speech conditions. Comparing between these two, which forms the essential point in this paper, is therefore highly confounded by inter-individual differences, which we know are substantial for these measures. More generally, the high variability of results in this research field should caution any strong conclusions based on comparing just these two experiments. A more useful approach would have been to perform the exact same task in the two experiments, to examine the reproducibility.

3) The interpretation presented here is essentially incompatible with the anti-masking model for the MOCR that first started of this field of research, in which the noise response is suppressed more than the signal, which is contradictory to the findings and model presented here, which suggest no role for the MOCR in improving speech in noise perception.

4) The analysis of measures becomes increasingly selective and lacking in detail as the paper progresses: numerous 'outliers' are removed from the ABR recordings, with very uneven numbers of outliers between conditions. ABRs were averaged across conditions with no explicit justification. The statistical analysis of the ABRs is flawed as it does not compare across conditions (vocoded vs masked) but only within each condition separately (active v passive) - from which no across-condition difference can be inferred. The model simulation includes only 3 out of 9 active conditions. For the cortical responses, again only 3 conditions are discussed, with little apparent relevance.

5) The assumption that changes in non-invasive measures, which represent a selective, random, mixed and jumbled by-product of underlying physiological processes, can be linked causally to auditory function, i.e. that changes in these responses necessarily have a definable and directional functional correlate in perception, is very tenuous and needs to be treated with much more caution.

Reviewer #1:

This preprint investigates neural mechanisms for processing degraded speech, in particular regarding efferent feedback. The authors thereby study two main types of speech degradations: noise vocoded speech and speech in background noise. Efferent feedback is assessed by recording click-evoked otoacoustic emissions as well as click-evoked brainstem responses, and the measurements are taken when the degraded speech is attended as well as when it is ignored. In addition, the authors also measure cortical responses to speech onsets. They find that these measures are affected by the two types of speech degradation in very different ways. In particular, for the noise vocoded speech, the click-evoked otoacoustic emissions are reduced when the speech is attended than when it is ignored. The opposite behaviour emerges when subjects listen to speech in background noise. The authors rationalise these different mechanisms through a computational model, which, as they show, can exhibit similar properties.

Unfortunately, many of the obtained results suffer from a lack of proper controls, which renders them rather inconclusive. In addition, important details of the experimental methodology are not properly described.

1) An important aspect of assessing the efferent feedback through the CEOAEs and ABRs is to ensure that different stimuli have equal intensity. The authors write in the methodology that the speech stimuli were presented at 75 dB SPL. However, it is not stated if this applies to the speech stimuli only, such that the stimuli that include background noise would have a higher intensity, or to the net stimuli. If the intensity of the speech signals alone had been kept at 75 dB SPL while the background noise had been increased, this would render the net signal louder and influence the MOCR. In addition, it would have been better to determine the loudness of the signals according to frequency weighting of the human auditory system, especially regarding the vocoded speech, to ensure equal loudness. If that was not done, how can the authors control for differences in perceived loudness resulting from the different stimuli?

2) Many of the p-values that show statistical significance are actually near the threshold of 0.05 (such as in the paragraph lines 147-181). This is particularly concerning due to the large number of statistical tests that were carried out. The authors state in the Methods section that they used the Bonferroni correction to account for multiple comparisons. This is in principle adequate, but the authors do not detail what number of multiple comparisons they used for the correction for each of the tests. This should be spelled out, so that the correction for multiple comparisons can be properly verified.

3) Line 184-203: It is not clear what speech material is being discussed. Is it the noise vocoded speech, the speech in either type of background noise, or these data taken together?

4) Line 202-203: The authors write that "the ABR data suggest different brain mechanisms are tapped across the different speech manipulations in order to maintain iso-performance levels". It is not clear what evidence supports this conclusion. In particular, from Figure 1D, it appears plausible that the effects seen in the auditory brainstem may be entirely driven by the MOCR effect. To see this, please note that absence of statistical significance does not imply that there is no effect. In particular, although some differences between active and passive listening conditions are non-significant, this may be due to noise, which may mask significant effects. Importantly, where there are significant differences between the active and the passive scenario, they are in the same direction for the different measures (CEOAEs, Wave III, Wave V). Of course, that does not mean that nothing else might happen at the brainstem level, but the evidence for this is lacking.

5) The way the output from the computational model is analyzed appears to bias the results towards the author's preferred conclusion. In particular, the authors use the correlation between the simulated neural output for a degraded speech signal, say speech in noise, and the neural output to the speech signal in quiet with the efferent feedback activated. They then compute how this correlation changes when the degraded speech signal is processed by the computational model with or without efferent feedback. However, the way the correlation is computed clearly biases the results to favor processing by a model with efferent feedback. The result that the noise-vocoded speech has a higher correlation when processed with the efferent feedback on is therefore entirely expected, and not a revelation of the computational model. More surprising is the observation that, for speech in noise, the correlation value is larger without the efferent feedback. This could due to the scaling of loudness of the acoustic input (see point 1), but more detail is needed to pin this down. In summary, the computational model unfortunately does not allow for a meaningful conclusion.

6) The experiment on the ERPs in relation to the speech onsets is not properly controlled. In particular, the different acoustics of the considered speech signals -- speech in quiet, vocoded speech, speech in background noise -- will cause differences in excitation within the cochlea which will then affect every subsequent processing stage, from the brainstem and on to the cortex, thereby leading to different ERPs. As an example, babble noise allows for 'dip listening', while with its flat envelope speech-shaped noise does not. Analyzing differences in the ERPs with the goal of relating these to something different than the purely acoustic differences, such as to attention, would require these acoustic differences to be controlled, which is not the case in the current results.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Summary:

The authors address a very important and timely research question, namely whether, and if so, how, efferent feedback contributes to the neural processing of degraded speech. However, the reviewers have identified significant problems with the experimental design and the data analysis, as well as with the conceptualization and the interpretation of the findings.

Reviewer #3:

This manuscript by Yu et al. explores the potential predictive value of Hyperpolarized 13C MRI and DCE-MRI in detecting early response of ICB. 2 mouse tumor models with different sensitivities to ICB were used in the study. Early changes in tumor glycolysis and necrosis were evaluated via [1-13C] pyruvate and [1,4-13C2] fumarate MRI, and perfusion/permeability state could be reflected by DCE-MRI. While the paper describes several intriguing pieces of data concerns below limit enthusiasm:

1) Figure 1A-C. Tumor growth curves in the anti-PD-L1 and anti-PD-L1 plus anti-CTLA4 groups appear to be steadily increasing, albeit at a slightly delayed pace than the control treated tumors. Most reports showed that PD-1/PD-L1 blockade results in tumor clearance in MC38 model, particularly when the treatment was started at small tumor sizes as presented in Figure 1A. The combination of anti-PD-L1 and anti-CTLA4 antibodies displayed more effective clearance of MC38 tumors. That is not the case here, where tumors are growing progressively throughout.

2) Figure 2A. I am surprised that CD4 T cells were barely detected in MC38 and B16 tumors. An example gating strategy must be shown, including an isotype or FMO control for each of the antibodies used.

3) Figure 3A. Given the therapeutic effect relies on the blockad of the binding between PD-1 and PD-L1, a careful assessment of the contribution of PD-1 binding to the metabolic change of tumor cells should be performed to provide clarity.

4) The microenvironment and structure of transplanted tumors are quite different from spontaneous tumor models, which are similar to human tumors. To demonstrate the clinical relevance of these findings, the authors will need to show more results in spontaneous tumor models or human tumors.

Reviewer #2:

Saida et al. performed multi-modal imaging to detect the early response to immune checkpoint blockade (ICB) therapy in murine models. This non-invasive method is attractive to monitor ICB response, thus it is valuable to discover relevant biomarkers in preclinical animal models before potential application in clinics. In ICB sensitive MC38 model, the authors identified increased cell death and intratumor perfusion/permeability, by 13C fumarate MRI and DCE MRI, respectively. While these descriptive results are interesting, this referee has a concern for the limited conceptual advance brought by this manuscript.

Major comment:

In recent years, new MRI technology has been shown to be promising to study pathophysiological changes, particularly in the metabolic field. To identify the efficacy of ICB, particularly at the early stage of treatment, is an important issue in immunotherapy. Thus the authors have chosen two murine models with a purpose to discover potential biomarkers with MRI. For metabolism, the author focused on glycolysis. In ICB sensitive MC38 model, no glycolytic changes were observed. Can the authors further clarify the role of glycolytic changes in ICB sensitive models? For instance, by using another ICB sensitive model; checking ECAR by using ex vivo digested tumor cells.

Reviewer #1:

The identification and validation of non-invasive imaging biomarkers for early response to cancer immunotherapy is a research hotspot. Dr. Krishna and colleagues proposed a potential combination of [1-13C] pyruvate-based detection of glycolysis, [1,4-13C2] fumarate-based analysis of necrosis, and Gd-DTPA-based quantification of perfusion/permeability with MRI technologies. To make the conclusions more convincing, some major issues should be carefully addressed.

1) It is a bit unfair to compare two different tumor models (MC38 colon cancer versus B16 melanoma). Reasonable solutions can be: 1) to compare good responders versus bad responders in the same type of cancer; 2) to compare ICB resilient tumor cell clones versus ICB sensitive clones, which originate from the same parental cell lines. To test whether these potential biomarkers can be generalized to multiple cancer types. Several tumor models should be tested.

2) It seems that the authors didn't test these parameters at different time points. As delayed response can be frequently observed in ICB, it is recommended to monitor tumor-bearing mice at different time points. These recorded parameters can be correlated to the therapeutic outcomes, once the whole tumor growth kinetics is finalized.

3) It is not accurate to consider the area of necrosis as the equivalent of immunogenic cell death.

4) Were any of these findings validated in a small cohort of cancer patients?

5) With radioactive probe-based analysis of glycolysis, it is difficult to judge whether metabolic changes were from tumor cells or from tumor-infiltrating immune cells. Ex vivo seahorse-based analyses of ECAR and OCR do not resemble in situ metabolic status of tumor cell.

6) Once glycolysis is reduced, OXPHOS and fatty acid oxidation may be switched on. A systemic analysis of the metabolic programs may be necessary. Mechanistic explorations on why these parameters correlate with late therapeutic outcomes is weak.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Summary:

A major concern is that the two transplantable murine tumor models used in this study may not be appropriate: it is odd to compare the therapeutic efficacy of ICB in colon cancer versus that in melanoma; the responsiveness of MC38 tumors seem to be much less than a series of reports; the composition of immune cells in the tumor microenvironment seems to be a bit abnormal; and the reviewers also have concerns on whether these transplantable tumor models can mimic human cancer patients.

Reviewer #3:

The manuscript by Gann et al., investigates whether theta-burst TMS stimulation (TBS) of the DLPFC can alter hippocampal and striatal activity during a sequence-learning task (SRTT). Across two experiments, the authors provide a well-powered investigation of this question using MRS and fMRI. The first experiment describes a nice approach for selecting an anatomically accurate brain region, whilst the second experiment uses a robust 4-session within-subject design. The study is clearly written and has some very interesting results, with the authors concluding that it provides the first experimental evidence that brain stimulation can alter motor learning-related functional responses in the striatum and hippocampus. As described below, I believe the interpretation of these results is overstated and would be better framed in the context of the other changes across the brain (it was not a specific effect between DLPFC and hippocampus/striatum) and also several clear negative effects (behaviour, MRS, fMRI).

1) Interpretation of the results given the lack of a behavioural effect: I do appreciate the authors discussion of this, however the lack of a behavioural effect makes me wonder whether the imaging results are over interpreted. Generally, I found the negative results (behaviour, MRS, aspects of connectivity) to be understated and the positive results to be overstated, even though the positive results, linking DLPFC stimulation to changes in striatum and hippocampus, required a far more nuanced analysis of the data (Figure 6). The results seem to suggest that TBS has a general (and somewhat inconsistent) effect on connectivity across the brain rather than a specific effect on DLPFC-hippocampus/striatum connectivity. Given these issues, I believe a more cautious interpretation of the results are required in which it is not concluded multiple times that DLPFC brain stimulation can alter motor learning-related functional responses in the striatum and hippocampus without making clear this was in the context of other changes across the brain and also several clear negative effects. The manuscript would be improved if a more balanced picture were provided throughout.

2) Use of iTBS vs cTBS: By using these TMS conditions, we do not know what the normal brain activation pattern is for the sequence task. Although the authors have provided a good attempt at trying to interpret these results, as a reader it was difficult to comprehend the somewhat inconsistent results across the two TMS conditions. The manuscript would have benefited from a sham/null TMS condition.

3) Consistency of results for experiment 1: Although this experiment provides a nice mechanism to determine TMS location, the details of these results need to be more substantial. In particular, for the conjunction analysis, the reader needs to understand how consistent this effect (Figure 1B) was across participants. Does every participant show this conjunction map or what percentage of participants show this map? This feels like an important thing to report, and then possibly base a power analysis on for Experiment 2 i.e. how many participants do we expect to see the predicted TMS results given the % of participants who show this conjunction map?

4) Clarity of results for experiment 2: I found it difficult to follow the results for experiment 2, especially from page 17. I appreciate the authors refer to the methods but I think a little more explanation of the methodology within the results is warranted. In addition, it got pretty difficult to follow the results relating task (seq vs random), stimulation (iTBS vs cTBS) and their interaction. Maybe more informative sub-titles would help?

5) Interpretation of BOLD activity: Given recent work (https://elifesciences.org/articles/55241 ) could the authors discuss what increases and decreases in BOLD activity represent within a learning context? Is a decrease or increase beneficial?

-Why do the authors keep using the term 'proof of concept'?

-Figure 7B: which line is cTBS and iTBS?

Reviewer #2:

Gann and colleagues report the effect of iTBS and cTBS of DLPFC on GABA+, BOLD-activity, and functional connectivity during sequence learning (SRTT). Despite finding no difference between the brain stimulation conditions on behavioral performance, the authors report widespread differences in BOLD-activity and functional connectivity between intermittent and continuous TBS. The key result (reported in Figure 6), is a complex difference between the stimulation conditions and the GABA+ change in DLPFC with i) the learning-related activity in hippocampus and ii) the learning-related changes in functional connectivity between DLPFC and putamen. The authors affirm that these results are important, as they are the first to show an interaction between DLPFC stimulation, learning-related changes in MRS, and BOLD-activity change in the hippocampus and striatum.

The authors have undertaken a mammoth effort in running this study. The targeted brain stimulation appears to have been conducted in an exemplary fashion, and the integration of multiple MR modalities is impressive. Nonetheless, I feel that the lack of a control group in the study design is a major concern and makes interpreting the study's results challenging. In addition, I have several reservations regarding the analysis that should be addressed before this work is suitable for publication.

General comments:

1) This study does not include a control group, and all conclusions are drawn based on the comparison between inhibitory and excitatory TBS protocols. A control condition is necessary to put the difference between the i/cTBS differences in perspective. Without this perspective, it is challenging to interpret the directionality and magnitude of the effects reported in this study.

2) The authors stress that the major contribution of this work is revealing the effects of DLPFC stimulation on fMRI/MRS signals during/after learning (e.g., Abstract: line 43-45; Introduction: lines 102-104; Discussion: lines 498-500, 741-743). As it is written, this work is primarily interesting to the brain stimulation community. The article would be of substantially broader interest if the authors discussed their results with respect to the contribution of DLPFC to sequence learning, rather than as an exploratory investigation into the effect of brain stimulation.

Methodological/Analytical comments:

3) The small volume correction analysis and reporting has several issues. Throughout the results, the authors report analyses plotted on the whole brain, and do not make reference to any small volume correction being used (except for the results reported in Table 2). However, in the methods section, the authors report that analyses were conducted using small volume corrections (10mm spheres drawn around the points reported in Supplementary table 7). There are several problems here.

i) Most importantly, the authors use (by my count) 87 separate small volumes, and reconstructing the spheres from the coordinates in Supplemental table 7 shows that this mask covers a substantial portion of the brain. This seems highly unusual to me. However, it is not clear whether all of these small volumes were considered together, or whether they were each considered as an independent volume. In either case, the authors should report whether any of their results survive whole brain correction. Additionally, if the authors tested 87 regions independently, multiple corrections should be applied to account for all regions tested (0.05/87 = 0.00057 for the new FWE-corrected p-threshold). Alternatively, if the authors used this single mask for correction, they should provide a justification for using an analytical mask restricted in this way, which, again, seems highly unusual.

ii) In the main text and figures, the authors should note when small volume correction is being applied.

iii) In the whole brain figures, it should be made clear what voxels were considered for the analysis (e.g., by shading the brain that was outside the small volume).

4) The authors appear to have done two instances of spatial smoothing (8mm before fitting the GLM (line 1184), and 6mm on the resulting statistical map (line 1224)). Again, this seems highly unusual, and given that the majority of results are conducted within small volumes, it seems smoothing to this extent would introduce unwanted levels of spatial blurring. The authors should report the total smoothness of the image for all subjects (AFNI's 3dFWHMx can do this) and consider performing the group analyses without additional smoothing applied to the statistical maps.

5) Although Study 1 is obviously important to the manuscript, I think it is perhaps overstated and makes the present work difficult to parse. Specifically, it does not seem to be important for interpreting the effects of the stimulation during learning; rather, Study 1 is a means to localize a brain stimulation target (i.e., a methodological point). Further, in the methods section, the authors reveal that they constrained their search for a conjunctive target (connected to both Hippocampus and Striatum) to the superior frontal gyrus and middle frontal gyrus. Thus, the authors seemed to have "found what they were looking for", because they restricted their search to a fairly well circumscribed region before running this study. Taken together, the authors might consider moving these details entirely to the Methods section, and removing Study 1 and associated figure from the main text.

6) Are there any relationships between Glx levels and fMRI effects?

Reviewer #1:

This is a very ambitious and interesting study that uses a state-of-the art combination of multiple methods to provide new insights into functional network interactions during motor learning. However, I have several major concerns against the design and analyses that may have contributed to the overall very weak effects that are reported (mainly null effects in standard measures at the behavioural and neural network level). I also think that some of the conclusions are not justified given the partly non-significant and overall weak effects.

1) My main concern is that no baseline stimulation condition (sham TBS) was included. The authors address this in the discussion but I cannot agree with their argumentation. Without a baseline, it is impossible to assess whether each stimulation protocol had a significant impact on the outcome measures. For instance, it would be plausible that both protocols had opposite effects (which is also hypothesized by the authors) which were, however, only slightly or not significant from baseline. If cTBS slightly decreases connectivity and iTBS slightly increases it, this could result in a difference between both protocols that might not be observed when contrasting each protocol against baseline. Put differently, how do we know that these changes are meaningful and significantly different from zero (baseline)? I think this is especially important in the present study since the overall effects are weak and there is no significant modulation of behavior - so the functional / behavioral relevance of the observed modulation remains unclear. I think that without the inclusion of a baseline (sham), it is very hard to interpret the data.

2) Another main concern is that the reported effects are very weak and not properly corrected for multiple comparisons. I don't think that it is justified to apply small volume corrections for large-scale network effects and it seems that some of the results are at threshold. Given the weak effects in these analyses, in combination with the absence of any modulation in the "standard" analyses (fMRI, connectivity, behaviour, MRS only significant in exploratory post-hoc tests which are not well justified), I am not sure if the reported results are really reflecting any stimulation-induced modulations at all or mainly show some noise added by the TMS protocols. This of course affects the conclusions that can be drawn from the study.

3) There are a number of issues with the design that might have contributed to the weak findings. These include data loss (e.g. no MRS data for the hippocampal voxel) and somehow arbitrary sample sizes that are not well justified. I am also not sure why cortical excitability measures (MEPs) were performed after TBS because this is of minor importance and delayed the start of the fMRI sessions. Given that TBS effects are expected to decrease over time, I am not sure if this was necessary. Was the potential change of the TBS effects across session taken into account (e.g., by using a parametric modulation of the TMS effect)?

4) Given the overall weak effects the conclusions should be toned down. The discussion would further benefit from including additional work that demonstrated changes in remote subcortical regions and effective connectivity after TMS over a frontal area (e.g. Herz et al., J Neurosci 2014).

5) There is no modulatory effect of TBS on behaviour, which is surprising in light of previous neurostimulation studies on motor learning. I think the way this is sold in the discussion is a bit odd. I guess that initially, one would have expected a behavioural modulation that should ideally be correlated with any TBS induced changes in functional connectivity (or with the MRS data). If not, how would you be able to claim behavioural relevance? In the discussion, the absence of a behavioural modulation is sold as an advantage, I think this is not justified and should be toned down. Moreover, since the authors speculate about potential influences of TBS on motor consolidation, I was wondering if consolidation was assessed (which seems to be a relevant parameter here)?

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Summary:

The main concerns with the study were three-fold. First, the absence of a control group makes it hard to draw conclusions about the effects of inhibitory and excitatory TBS protocols separately, limiting the appeal of the study. Secondly, the control for multiple statistical tests is not adequate - conducting 87 independent "small volume corrected" tests will lead to an inflated family-wise error rate. Finally, all reviewers were unanimous in judging the effects to be somewhat interesting, but rather weak - with the absence of an effect on behaviour and simpler standard fMRI and connectivity measures being as remarkable as the positive effects reported.

Reviewer #3:

Short-summary:

Children (wide range) and adults participated in 3 MEG-experiments with auditory oddball paradigms varying in task demands. The focus is on the child N250m. Results show that although the N250m was not attenuated by task differences, increased activation in the left hemisphere (for at least the standard stimulus in the gng-task) was associated with better performances in inhibition tasks. Since the N250m in children was mainly located in the temporal cortices, whereas activation in adults was present in other areas, notable the ACG, this suggests that children differ from adults in the mechanisms required for cognitive control, and rely longer on sensori-motor areas.

Positive: well-written, great pictures.

Major comments:

1) The proposed link between auditory skills and inhibition is poorly explained and requires more elaboration. They want to relate auditory processing to " cognitive skills" (line 22, 77). Yet cognitive skills are a broad construct, encompassing many skills and abilities, including for instance reading, but also executive functions, which includes inhibition (Miyake et al., 2000) . Actually why zoom in on inhibition? Is it as one of the three components of executive function (Miyake et al., 2000) or is it viewed as part of self-regulation (Nigg, 2017)? You refer to cognitive control (46/47)- which suggests the latter explanation - but this remains unclear. It would help the reader to use consistent terminology (e.g., inhibition, cognitive control, executive control, inhibitory control are used now), or to highlight the links between the related concepts. Moreover, there are many paradigms to test inhibition, why did you chose the one you chose (Littman & Takacs, 2017)? And you also examine the behavioral performance sin the inhibition-MEG task (line 303)? Why the additional focus on attention in the results?

2) Your summary of the two child components (N1m and N250m) predicts different findings with the relationships with inhibition. That is, the link between the child N1m and inhibition should be smaller/non-existent, while it is mainly in the N250m that you expect it. While your results prove evidence towards the latter, your analyses do not concern the first component. It would be stronger if you do.

3) The logic of having three different auditory-listening tasks, and one behavioral outcome measure was not entirely clear to me. It seems that the paper is addressing various aims (e.g., replicate earlier work showing that the N250m is unaffected by task parameters in children while it is only present in adults for active tasks; another is linking the N250 m across all three tasks, or only for one of the three, if so, which? related to inhibition, but only for children, or also adults?) it would help to be explicit about this. For instance, there is an MEG-inhibition task and a behavioral task. Were you going to relate performances to both?

4) Why is age a significant predictor in explaining SSRT performance when adding left hemisphere OB-deviant, but not when adding LH GNG-S? Moreover, isn't it surprising that increase in activation yields better SSRT scores when this component disappears in adults?

5) From an association one cannot infer causal relationships - such limitations need to be discussed in more detail. Results do not allow for concluding that a sustained response ' aid inhibitory performance' (line 624).

Reviewer #2:

In this study the authors sought to explore the relationship between a child-specific auditory evoked response (N250) and cognitive control, using a classic auditory oddball paradigm. Here the cognitive control was manipulated by varying the tasks that participants were instructed to do while listening to the oddball tone sequence: (a) ignore all sounds ("passive listening"), (b) respond to the standard tones ("go/no-go") and respond to the deviant tone (which was called "oddball task" in this study).

Using the combined MEG and EEG as well as MRI, they reported an association between the strength of N250 in the left hemisphere and the behavioural performance in the go/no-go task and a separate inhibition task. Based on this observation as well as the fact that N250 was only visually observed in the children's brain response, the authors claimed that when doing sound involved cognitive tasks, different neural mechanisms were employed by adults and children. Considering the difficulty in operating a MEG and EEG combined experiment on children (6-14 years), the large sample size (n=78) is very, very impressive and the task was carefully embedded in a children-friendly game, which showed that the authors did a lot of work for this project.

However, it is hard to generalise such a conclusion based on the current paradigm and the results reported here. I also found it's a bit hard to follow the logic in the original manuscript, not because of the language but I think it might need more thorough revision to better explain what exactly the authors hypothesize, why use this specific paradigm, and why analyse the data in these ways.

Major comments:

1) While the task "press a button to standard tone" is called go/no-go task, the task "press a button to deviant tone" is called an oddball task. Why is the latter not a go/no-go task? It's definitely ok to have different names for different blocks, and also to analyse the data in these two blocks separately to double check. However, I would not expect fundamental difference in these two blocks. (However, as mentioned later, the authors reported divergence between these two tasks).

2) The main finding "Left hemisphere auditory responses at 250ms predicts behavioural performance on inhibition tasks" was based on the observation that, the brain activity in the left hemisphere (independent of the task) was negatively correlated with the within-individual variance in RT and the error rate in the go/no-go task (where subjects were instructed to respond to the standard tones) and the reaction time in a separate inhibition task done outside of the scanner. Why smaller within-individual variance in RT means better performance? Someone could be consistently very slow and this should not be a better performer. I found this is confusing, especially that based on Table 3, there was no correlation between RT and the brain response strength.

3) The scatterplots in Figure 7 shows the correlation reported in Table 3. However, the correlation seems to be largely driven by a few outliers: about 5 subjects whose source amplitude was much more negative than the rest of the population. Why did these subjects have a particularly strong source amplitude? After excluding these five subjects' data, will the correlation remain significant?

4) This point is related to points (1) and (2). In table 3, left hemisphere response during passive listening was strongly correlated with ICV, ERR and SSRT, but in table 6, there were no more correlations for passive listening. Can the authors explain why there is a difference between two passive listening sessions which in theory should be the same? Again, if there is no difference between "press a button to standard tone" and "press a button to deviant tone" and the correlation observed in table 3 was robust, then we would expect to see the significant correlations in table 6 for ICV, ERR too, but it is not true. These together make the finding less convincing. If there is any misunderstanding, the authors still need to justify these clearly in the manuscript and further analysis would be helpful.

5) Interpretation of the result: Even if the association between the amplitude of N250 and the behavioural performance is proven robust and true, this doesn't mean that this activity "aid the inhibitory performance in children" (line 624). Correlation does not imply causation. The authors need to provide more direct evidence to support such a claim or consider re-wording.

6) Design of the task: a. The block order: Why was the task order fixed for all participants? b. It is unclear why the passive listening block has a different number of trials (300) compared to the other two active blocks (360).

7) Sample size: Although the large sample size used in this study is very impressive, it is unclear how this sample size was determined and why the sample size of two groups (children vs adults) was so different (children n=78, adults n=16). It is crucial to justify this difference in this study because the motivation of this study is based on the hypothesis that N250 is present in children but not in the adult.

8) The unequal number of samples in statistical analysis: Related to the last two points, it is unclear whether the number of trials/participants was equalised before running the statistical analysis in this study.

9) Handedness: As the authors themselves mentioned in the discussion, the effect in left hemisphere observed here could be related to the handedness. Then the authors should also report the handedness amongst the participants.

10) Analysis: It is generally unclear why the children's data were divided into two groups: above or below 10 years old. The authors need to explain their rationale behind this clearly before doing so.

11) Figure 3: Each sub-figure includes 6 different conditions and makes it very hard to visualise. Please consider plotting the results in pairs for comparison, also show error-bar and run proper time-series statistics on the result. Also, it is unclear which channels are selected based on the black and white cap image at the centre. Please visualise it differently, for example, colours.

Reviewer #1:

This study by van Bijnen et al. used MEG/EEG recordings to examine the behavioral relevance of auditory processing in children, with a specific focus on an auditory cortical component around 250 ms, which only occurs in children but not in adults. They demonstrate that this component, particularly in the left auditory regions, covaries with several behavioral measurements in children. They conclude that the results suggest a shift in cognitive control function from sensorimotor regions in children to prefrontal involvements in adults.

The study addresses an important question in both auditory neuroscience and developmental science and is carefully performed. The modified design for children is interesting. However, I am not quite convinced that the findings constitute a great breakthrough. Moreover, I have major concerns about the correlation analysis that would support the central claim in the paper, that is, the attentional inhibition relevance of the M250 component in the left auditory cortex.

Major:

1) The child-specific M250 component occurring in the auditory cortex is interesting, but as mentioned throughout the paper, this is a well established observation. This study provides some evidence for the behavioral correlates of the component, but I am not convinced that the correlations supports the unique function of the component in attentional inhibition and its development trajectory from children to adults. First, the author only focused on the M250 component and calculated its correlation to behavior and thus could not exclude that other components might also be involved in the process. I would suggest the authors to do the correlation throughout the time course to thoroughly seek the behavioral-related components. Second, even for the passive listening conditions when inhibition is not required, the M250 also correlated with some behavioral measurements in certain task (Table 3) ? Third, only the to-be-inhibited sound was analyzed so how could the results support that the component only correlates with attentional inhibition? I understand that the authors might want to avoid the motor confounding factors associated with attended sound, but without comparison or control analysis, the conclusion could not firmly hold. Finally, behavioral relevance analysis was only done on children but not adults.

2) The authors calculated correlations between the M250 component with a series of behavioral measurements. Is there any way to do multiple comparison correction? Moreover, the results are inconsistent across different comparisons (e.g., Table 3, Table 6). For example, several behavioral indexes correlated with neural component for both PL and GN conditions (Table 3) while only SSRT showed correlation with the component under OB condition. I would suggest a more fair analysis by performing a GLM analysis using all the behavioral measurements (not just select factors that showed significant partial correlation which I think is double dipping to some extent, e.g., table 4, 7) as predictors.

3) To support the developmental trajectory of the M250 component, the authors could also perform the behavioral correlation for adults and compare it to that for children, even the behavioral-relevant component might be different in time and occur in distinct brain regions.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Summary:

All the reviewers acknowledged the importance of the question the paper aims to address, the big sample size, and the interesting experimental design for children. The paper is also clear and well written. However, the reviewers raised several critical concerns that question the main conclusions, including the interpretation of the results (i.e., relation to inhibition in cognitive control), inconsistency across experiments (i.e., differences in the results between the two experiments), and analysis details (i.e., behavioral-neural correlations). The paper could also be improved by a reframing in which the hypotheses and rationale behind the experiments are better explained.

Reviewer #3:

Summary:

The authors evaluate functional implications of two B9D2 missense variants identified in an individual with Joubert syndrome, by engineering the variants into a C. elegans model system. Few studies have evaluated the functional consequences of patient variants in model systems (rather than null alleles). Overall, the experiments are elegant and rigorous. The functional defects evaluated include decreased and altered localization of the variant proteins at the TZ, altered TZ function, altered cilium function (dye filling and behavioral assays), and reduced TZ protein localization, especially for TMEM216. The functional effects of homozygous null, homozygous missense variants, and compound heterozygous missense variants are compared. While most of the conclusions are well-supported, the work does not connect the functional consequences in C. elegans to phenotypic severity in humans, a critical validation of methods to test pathogenicity of human variants.

Major comment:

The authors introduce the concept of using C. elegans for genotype-phenotype correlations in the Abstract and Introduction, but do not interrogate an allelic series from humans with more and less severe phenotypes. The claims of genotype-phenotype correlation could be de-emphasized (eliminated? restricted to C. elegans), or the work could be strengthened by including more of an allelic series including variants predicted to be more deleterious (p.Ser101Arg identified in families segregating a Meckel syndrome phenotype. and p.His5Gln identified in a family segregating a possible Meckel syndrome phenotype), less deleterious (the p.Leu36Pro variant in a possibly less severely affected person with JBTS, also published in the Bachmann-Gagescu paper), and benign (i.e. common variants that are found homozygous in population databases like gnomAD and are unlikely to impair B9D2 function). It seems that this would be a lot of additional work; however, the Discussion highlights "it should be possible to generate hundreds of alleles in a relatively short time frame at relatively low cost and manpower compared to other multicellular systems. The workflow to generate and characterize ciliopathy associated variants described here can also be extended to other conserved cilia genes and ciliopathies."

Other comments:

1) Important considerations for data presentation and statistical analysis:

-Use dot (or violin) plots rather than bar graphs to show data structure for length, intensity, and other measurements (see PMID 32346721). For the curves of linescan intensities, it would be helpful to include supplemental figures with all of individual curves to see their shapes and variability.

-t-tests on all data points together may over estimate statistical significance; consider whether it would be more appropriate to compare mean measurements for each animal (or median if the data are not normally distributed). At a minimum, list the number of cilia and the number of animals for each experiment.

2) Could the lower levels of mutant protein in the TZ be due to lower levels of total mutant protein? Although there is no MKSR-2 antibody, this could be evaluated by Western blots of mNG::MKSR-2/mNG::MKSR-2(P74S) and mNG::MKSR-2/mNG::MKSR-2(G155S) animals.

Reviewer #2:

In this manuscript, the authors analyzed the function of two pathogenic missense variants (P74S, G155S) of Joubert Syndrome protein B9D2/ mksr-2 using a C. elegans model. The data shows that both P74S and G155S mutations change the distribution of MKSR-2 on TZ and disrupt the structure and function of cilia in C. elegans, indicating that both mutations are pathogenic.

Characterizing the function of pathogenic mutations associated with ciliopathies is important for us to understand the function of ciliopathy genes and the pathogenesis of ciliopathies, therefore, the topic of the manuscript is very important and interesting.

The manuscript is well organized, and the data is of high experimental quality. However, there is a lack of new insights about the function of MKSR-2 protein or the formation of TZ.

Major concerns:

What are the possible mechanisms by which P74S and G155S mutations affect the function of MKSR-2? Do these mutations affect the interaction between MKSR-2 with other TZ proteins? I do think some (even a little) new insights into the function of MKSR-2 are needed.

Reviewer #1:

The experiments are elegant, take advantage of the strengths of the model and the conclusions are mostly supported by the results, even if the discussion should address potential limitations a little more. Overall, this is thorough work of potential high impact.

Major comments:

1) The authors test the localization of the mutant B9D2 protein at the base of the cilium, show decreased fluorescent signal and conclude that the patient mutations affect the TZ localization of the protein. It seems important to me to also demonstrate that the overall protein stability is not affected by measuring the protein levels by western blot if possible. The competition assay between wildtype and mutant alleles with and without transgene somewhat supports the presence of product from the mutant alleles, but an objective measure of the amount would further strengthen their point. (One could imagine that the G155S mutation leads to decreased protein stability with increased degradation and this may explain why it is more similar to the knock-out than the P74S allele?).

2) One major claim made by the authors is that the experiments allow to classify the severity of the effect caused by the individual mutations, showing that the G155S is more severe than P74S. What I find puzzling, is that the ultrastructural consequences on the TZ appear to be similar in both mutants, whereas the TZ gating function is affected only in the G155S mutant. How do the authors explain this discrepancy? If the morphology of the gate is affected similarly, why is the function not affected similarly? Maybe some quantification of the ultrastructural defects would show that the ZT is more disrupted in the G155S mutant?

3) A more detailed discussion of the differences between C.elegans and mammalian cilia appears necessary to me, since these difference may prove to limit the applicability of the proposed assays (for example differences in the basal body of C.elegans may limit this approach for basal body resident proteins? Even for the TZ, in humans mutations in only on TZ component cause phenotypes, while in worms, double mutants are necessary for most genes, suggesting differences in the function of the individual proteins or the structure of the TZ). Beyond the species differences, evidence is appearing for cell-type specific roles of ciliary proteins, so that results from one type of cilium (including those shown here in worms), do not necessarily guarantee that this holds true in all cilia types, which would limit the interpretation for patients with many different cilia types. This being said, I still support the relevance of the current work, but just think that these potential limitations should be mentioned in the discussion in a more detailed manner.

4) Figure 2D: the curve for the P74S mutant overlays with the WT curve with respect to height (fluorescence intensity) and length (x-axis). Does this not contradict panels A-C where the signal is weaker and shorter?

5) Figure 6C: my impression from the graphs is that nphp4 and cep290 are just as much affected as mks14 and mks6 in both P74S and G155S mutants? The text does not mention that mksr2 mutants have any effect on nphp4, cep290 or mks5 whereas the graphs do show a mild effect? Wouldn't this contradict the model of how the TZ is built? Figure 6D again seems to show a different result than Figure 6C (mainly for mks6)?

6) Statistics: correction for multiple testing should be performed everywhere (no pair-wise t-tests).

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Summary:

The manuscript by Lange et al describes how C. elegans can be used to generate functional assays to interpret the significance of missense variants in known human ciliopathy genes. This work thus aims at being a proof-of-principle for a way to address the major problem of VUSs (variants of unknown significance) faced by human geneticists today and is therefore of high relevance to the field (even if no major novel biological insights with respect to ciliary biology are described). The reviewers agreed that characterizing the function of pathogenic mutations associated with ciliopathies is important for us to understand the function of ciliopathy genes and the pathogenesis of ciliopathies. The manuscript is well organized and the data are of high experimental quality.

Author Response:

All three reviewers agreed that establishing a link between a proteasome activator and heterochromatin stability was novel and intriguing. However, limited insight into the PA28-gamma mechanism of action (or possibly a new heterochromatin compaction mechanism) dampened reviewer enthusiasm. The reviewers offered many suggestions, including additional experiments, new controls, and structural changes to the Discussion, that we hope you find useful.

We would like to thank the reviewers for their suggestions and comments, which we will take into account to improve our manuscript as much as possible. As stressed by reviewers, our manuscript highlights a new and unexpected function of a proteasome regulator, PA28γ, in the regulation of heterochromatin compaction. We also provide evidences that this unexpected function of PA28γ is independent of its proteasome regulatory function. Moreover, we can show that PA28γ is required at least for proper maintenance of heterochromatin regions dependent on HP1 proteins, thereby providing a clear insight into the PA28γ mechanism of action on chromatin.

Reviewer #1:

In the manuscript entitled, "The 20S proteasome activator PA28γ controls the compaction of chromatin," Fesquet et al. establish a functional link between PA28γ and chromatin compaction in human cells. Previous work established a role for PA28γ in DNA repair and in chromosome stability through mitotic checkpoint regulation; however, a role, if any, for PA28γ in heterochromatin establishment/maintenance was not known. The authors use an elegant LacO-GFP system combined with PA28γ knockdown to support the possibility that this nuclear activator contributes to DNA packaging of repetitive DNA. A nucleosome proximity assay offers additional support that the most compacted chromatin is most sensitive to loss of PA28γ. Using a truncated version of PA28γ, the authors show that this chromatin function appears to be independent of its interaction with the 20S proteasome. ChIP-qPCR suggests that PA28γ binds repetitive DNA and ChIP-qPCR of PA28γ knockdown cells lose H3K9me and H4K20me, two silent heterochromatin marks. In addition to these data, the authors also attempt to establish that PA28γ and HP1β may work together to support heterochromatin formation/maintenance. The manuscript reports several intriguing pieces of data that have the potential to open new areas of inquiry into proteasome components and accessory factors in chromatin organization and remodeling. The potency of these key experiments, however, were diluted by unconvincing co-localization assays, poorly controlled PLA and ChIP-qPCR assays, and a highly speculative Discussion. Moreover, key controls were missing for several experiments (detailed below) that would have otherwise established the heterochromatin-specificity of PA28γ. Finally, important potential functional consequences of heterochromatin disruption, including chromosome segregation defects, transposable element proliferation, and accumulation of DNA damage, were not addressed while there was a focus instead on cell cycle without clear interpretations.

Major Comments:

1) Figure 2: The co-localization experiments were unconvincing - HP1β and PA28γ foci decorate most of the nucleus, making inferences about significant overlap difficult to grasp.

We fully agree with this criticism for Fig. 2A, in which classical indirect immunofluorescence (IF) and widefield microscopy were used. This is why in Fig. 2B, we set up a pre-extraction protocol of cells with a Triton X100 treatment, to remove almost all soluble proteins before cells fixation and IF. Then images were acquired as Z-stacks with an Airyscan confocal microscope, followed by a 3D reconstruction and analysis of the co-localization between PA28γ and PA28γ using Imaris co-localization software. This experiment highlighted that only a fraction of both endogenous proteins co-localize in the nucleus. Furthermore, we noted that the number of co-localization sites evidenced in Fig 2B (~32) was in the same range than the number of dots (~37) detected by another approach (is-PLA), suggesting that we can be confident with these results.

I also found the significance of the PLA assays difficult to discern. When both factors are so abundant in the nucleus, it seems inevitable to observe loss of proximity when one 'partner' is depleted. How do these data demonstrate the specificity of this potential proximity? A clearer explanation would be helpful.

PLA technique imposes numerous constraints to obtain a signal (i.e. distance less than 30-40 nm between the two epitopes, formation of a closed circular DNA template). As a control, we verified that the is-PLA approach gives specific signals between PA28γ and the 20S proteasome. Like PA28γ, the 20S proteasome is very abundant in the nucleus but only a small fraction of PA28γ interacts with the 20S proteasome by Co-IP (Jonik-Nowak, 2018). Consistent with this, less than 60 distinct PLA spots were detected in the nucleus between PA28γ and the 20S proteasome rather than a global nuclear PLA labeling suggesting that it is probably not the abundance of each protein tested that is responsible for PLA signal but rather, as suggested by this kind of techniques, their ability to interact.

Note that the PIP30 data were a distraction from the main thread - I recommend removing or explaining more clearly.

PIP30 is currently the only known regulator of PA28γ, for which we have previously shown a critical role in PA28γ interaction with different partners and localization (Jonik-Nowak, 2018). This is why we examined the potential requirement of PIP30 in this new chromatin regulatory function of PA28γ.

2) The ChIP-qPCR data were certainly exciting but the absence of a negative control locus made me wonder how specific this result was to DNA repeats.

As a control, we already used cyclin E2 promoter in our ChIP-qPCR for PA28γ. This led us to show that the detection of PPA28γ on heterochromatic repetitive DNA sequences is enriched by a factor of 2-3 as compared to this euchromatic loci bound by PA28γ. In a modified version of this manuscript, we will add other control loci located in euchromatin. We will also test these new loci as negative controls in ChIP-qPCR for H3K9me3 and H4K20me3.

3) The LacO-GFP data are really cool. Why didn't the authors not attempt to rescue compaction with a PA28γ transgene as was done for the FLIM-FRET?

Since, we could not obtain stable U20S-LacO-KO-PA28γ and -KO/KI-PA28γ cell lines, we decided to analyze the impact of PA28γ absence, using siRNA approaches. As it was shown that overexpression of PA28γ is sufficient to cause a disruption of Cajal Bodies (Cioce et al., 2006) and a decrease in the number of PML bodies (Zannini et al., 2009), and we also noticed in FRET-FLIM experiments that PA28γ expression level is critical for chromatin compaction, it is difficult to consider to overexpress a RNAi-resistant PA28γ protein in order to rescue the effect of the depleted endogenous protein.

4) Cell cycle data would be much more interesting if the authors set up a priori predictions based on Figures 1-5.

We agree with the comment, and we will correct it in the modified version of the manuscript.

5) The absence of any report of PA28γ KD/KO on genome instability was surprising.

As indicated in the manuscript, the potential effect of PA28γ depletion on genome stability has already been reported in the literature showing an increase in chromosomal instability (Zannini, 2008).

Loss of heterochromatin integrity is expected to compromise chromosome transmission/transposable element expression or insertions. Do the repeats to which PA28γ localizes upregulate upon PA28γ KD or KO? Does DNA damage signaling increase at the loci? These functional consequences would be rather more explicable that the S-phase result reported.

We did not detect any upregulation at these specific loci by RT-qPCR experiment using KO-PA28γ U2OS cells. Concerning the potential accumulation of DNA damage signaling at these loci in the absence of PA28γ, we have not studied this aspect because PA28γ depletion was reported to induce only a marked delay in DSB repair and not a DNA damage accumulation (Levy-Barda, 2011).

6) The histone mark ChIP-qPCR, like the PA28γ ChIP-qPCR, lacks a negative control locus/loci, again undermining the inference of specificity of PA28γ on heterochromatin.

We agree and these different control loci would be added in the modified version.

7) The LLPS paragraph in the discussion was weak - consider removing.

Yes, potentially. To be defined in the context of the modified version.

8) The speculation of 20S into foci does not add and, to my mind, detracts from the focus of the Discussion.

In the modified version of the manuscript, we will focus our study on endogenous proteins and therefore this aspect of the discussion concerning the 20S proteasome, and related to the overexpression of alpha4, will no longer be discussed.

Reviewer #2:

In this manuscript, Fesquet and colleagues describe an important role of the proteasome activator PA28-gamma in the compaction of chromatin. The authors first demonstrate that PA28-gamma colocalizes HP1-beta at nuclear foci induced by the ectopic expression of alpha-4 subunit of the 20S proteasome. They further show that a fraction of PA28-gamma colocalizes also with HP1-beta in cells without ectopic expression of the alpha-4. The authors then show that PA28-gamma is associated with heterochromatic regions and is required for the compaction of lacO array integrated at a pericentromeric region. They also performed the quantitative FLIM-FRET and demonstrate that PA28-gamma controls chromatin compaction in living cells, independently of its interaction with 20S proteasome. Finally, the authors show that PA29-gamma depletion leads to a decrease of heterochromatin marks, H3K9me3 and H4K20me3, at representative heterochromatic regions. From these findings they conclude that PA28-gamma contributes to chromatin compaction and heterochromatin formation.

Although PA28-gamma has been identified as an alternative component associated with 20S proteasome, its physiological roles remain obscure. The present study demonstrates that PA28-gamma is involved in chromatin compaction and heterochromatin formation. The results presented are in most cases of high quality and convincingly controlled. I have the following concerns that should be addressed by the authors.

Major points: 1) For the localization study (Fig. 1), the authors first show the colocalization of alpha-4, PA28-gamma, and HP1-beta in the nuclear foci induced by ectopic expression of alpha-4-GFP. While the authors point out the similarity of cell-cycle dependent patterns between the alpa-4 induced foci and HP1-beta foci (lines 135-138), this argument seems to be poorly reasoned.

We omitted to mention that we also tested the potential co-localization of alpha-4-GFP with different proteins associated with nuclear foci (SC35, PML PCNA, γH2AX) or BrdU-labelled replication foci without success, before to find a correlation with the accumulation of newly synthesized GFP-HP1β in nuclear foci.

The authors previously showed that ectopically expressed CFP-tagged alpha-7, another core component of 20S, accumulates into discrete nuclear foci, and the foci are colocalized with SC35, a well-characterized member of nuclear speckle (Baldin et al. MCB 2008). Considering that both alpha-4 and alpha-7 are core components of 20S proteasome, it is highly likely that the alpha-4-GFP- accumulating nuclear foci are corresponding to the nuclear speckles. If so, HP1-beta foci should be distinct from that of alpha-4-GFP foci. The authors should test the relationship between alpha-4-GFP foci and nuclear speckles, and if this would be the case, it might be better to omit the colocalization data using cells expressing alpha-4-GFP (Fig. 1) and start by potential colocalization of PA28-gamma and HP1-beta in cells without expressing alpha-4-GFP (Fig. 2).

As mentioned above alpha4-GFP did not co-localize with SC35, a marker of the nuclear speckles. When different alpha subunits of the 20S proteasome are overexpressed, only alpha7 and alpha4 show an accumulation in specific nuclear foci. This remains unclear but a possible explanation could be an alternative composition of alpha subunits in the 20S as previously reported for alpha4 (Padmanabhan A. et al., Assemnbly of an evolutionarily conserved alternative proteasome isoform in human cells, , 2016, Cell Reports). As this part of our study appears to confuse readers and to dilute the essential message of the manuscript, we are considering to exclude these data in the modified version.

2) Although the functional link between PA28-gamma and chromatin compaction seems quite interesting, it remains unclear how it contributes to the establishment of repressive histone marks such as H3K9me3 and H4K20me3. While the authors clearly show that 20S-binding-deficient PA28-gamma mutant (PA28-gamma ∆C) could restore the chromatin compaction defect caused by PA28-gamma KO, it is also possible that PA28-gamma controls the stability of factors involved in heterochromatin assembly. To exclude this possibility the authors should test whether PA28-gamma KD/KD does not affect the protein levels of core histone modifying enzymes and HP1 proteins by immunoblotting.

During this study we performed numerous immunoblots using anti-HP1 antibodies and we did not observe any significant variation of these proteins in KO-PA28γ cells. Furthermore, in an atempt to identify proteins whose stability could be controlled directly or indirectly by PA28γ, we performed a SILAC-based quantitative proteomic analysis comparing nuclear extracts from U2OS or HeLa wild type cells to U2OS- or HeLa KO-PA28γ cells. Under the tested conditions, we could not identify variation of the amount of factors involved in chromatin assembly, suggesting that the impact of PA28γ on chromatin organization is not driven by changes in the level of the important histone-modifying enzymes, nor core components of chromatin such as HP1 proteins.

Reviewer #3:

This manuscript explores the localization and function of a previously studied proteasome activator, PA28gamma. This protein is a nuclear activator of the 20S proteasome and is widely conserved during evolution, although largely absent in fungi. The authors report that (1) subunits of the 20S proteasome (alpha4 and alpha6) and GFP-tagged or endogenous PA28gamma colocalize with each other and with HP1beta in the nucleus, with HP1beta required for the localization of PA28gamma to nuclear foci, (2) depletion of PA28gamma results in decompaction of pericentromeric heterochromatin, and (3) use a FLIM-FRET based microscopy assay to show a broad role for PA28gamma in chromatin compaction, a function that PA28gamma shares with HP1beta. They also show that the C terminus of PA28gamma, which is required for its interaction with the 20S proteasome, is not required for its subnuclear localization or compaction functions, and that PA28gamma KO cells have reduced levels of H3K9me3 and H4K20me3 heterochromatin-associated histone modifications.

The identification of a role for PA28gamma in heterochromatin compaction and heterochromatin maintenance is interesting and raises intriguing possibilities about the role of this protein and the 20S proteasome in heterochromatic domains. The study is largely descriptive and does not provide new mechanistic insight into heterochromatin or PA28gamma. Although the experiments in the paper are of high quality and well-executed, they basically amount to identification of a new factor that affects heterochromatin stability. The fact that PA28gamma is a proteasome activator provides no mechanistic insight since the 20S proteasome does not seem to be required for the heterochromatin compaction function of PA28gamma.

The following suggestions may be helpful to the authors in preparing their manuscript for publication (in order of appearance).

1) The IP experiments in Figure 1D should be performed in the presence of nuclease (DNase/RNase A or benzonase) to test whether the interactions are bridged by RNA or DNA.

We actually tried several times to perform this IP experiments using notably benzonase. However, despite several attempts under various conditions, we could not obtain a clear and consistent answer to this question.

2) Figure 2. What percentage of PA28gamma and HP1beta foci overlap in the absence of alpha4 overexpression?

As indicated in the text, on average of 32 spot of co-localization between the two proteins were detected in Figure 2B and on average of 37 spots in is-PLA experiment (Figure 2C).

3) Figure 3. Does decompaction result in loss of silencing of heterochromatin targets such as HERV-K, LINE1, alpha satellite etc? Ideally, the authors should perform RNA-seq to provide a more complete picture of changes in gene expression as a result of PA28gamma depletion.

RT-qPCRs were performed on heterochromatin loci used for ChIP (HERV-K, L1 Line, SatII and alpha-sat) and no significant variation was observed. In order to determine whether the absence of PA28γ could affect gene expression, we performed a trancriptomic analysis using Affymetrix® Human Gene 2.1 ST Array Strip comparing mRNA expression in U2OS -WT and KO-PA28γ cells. This experiment revealed only very little variation between the two samples tested: 11 genes were up in KO-PA28γ (MFAP5 (Microfibrillar-associated protein 5), GLIPR1 (Glioma pathogenesis-related protein 1) and 9 that are still unannotated), and only 2 genes were significantly down: PSME3 (PA28γ) and MAGE-C1(Melanoma-associated antigen C1). These experiences led us to consider that PA28γ probably does not directly affect the level of transcription.

4) Based on experiments with PA28gamma-deltaC, which does not interact with the 20S proteasome, the authors conclude that the 20S proteasome is not required for the PA28gamma-mediated chromatin compaction. Although their IP data (Figure 4E) seem persuasive, a more convincing experiment would be to also perform the FRET assay for compaction with knockdown of subunits of the proteasome.

Knockdown of 20S proteasome subunits was not performed since in that condition all the proteasome family will be affected, and we already know that depletion of these proteins has several and pleiotropic effects (i.e. cell cycle progression), which could indirectly affect chromatin compaction.

5) Figure 6. It is critical that the effects on histone modifications are evaluated using siRNA KD (or other transient KD methods) of PA28g to complement the KO results. PA28gamma KOs have many defects including genome instability and aneuploidy that may affect K9me3 and K20me3 indirectly.

This is indeed a hypothesis that cannot be ruled out. But considering that these modifications (H3K9me3, H4K20me1/3) are crucial for the establishment of chromatin compaction and that the elimination of PA28γ (siRNA treatment) induces chromatin decompaction within 48h, it is reasonable to consider that the variation of these marks does not result from genome instability.

6) In general, the manuscript would benefit from the addition of genome-wide approaches such as ChIP-seq to gain broader insight into PA28gamma localization and general compaction functions.

We agree that the mapping of PA28γ distribution on non-repeated DNA sequences will be useful for the subsequent studies of PA28γ functions in DNA–related processes such as gene regulation. However, because of the difficulty to map HP1 proteins and heterochromatin regions by ChIP-seq, we do not believe that this approach will necessarily reinforce the current message of this first manuscript on the role of PA28γ in the regulation of heterochromatin compaction.

Reviewer #3:

This manuscript explores the localization and function of a previously studied proteasome activator, PA28gamma. This protein is a nuclear activator of the 20S proteasome and is widely conserved during evolution, although largely absent in fungi. The authors report that (1) subunits of the 20S proteasome (alpha4 and alpha6) and GFP-tagged or endogenous PA28gamma colocalize with each other and with HP1beta in the nucleus, with HP1beta required for the localization of PA28gamma to nuclear foci, (2) depletion of PA28gamma results in decompaction of pericentromeric heterochromatin, and (3) use a FLIM-FRET based microscopy assay to show a broad role for PA28gamma in chromatin compaction, a function that PA28gamma shares with HP1beta. They also show that the C terminus of PA28gamma, which is required for its interaction with the 20S proteasome, is not required for its subnuclear localization or compaction functions, and that PA28gamma KO cells have reduced levels of H3K9me3 and H4K20me3 heterochromatin-associated histone modifications.

The identification of a role for PA28gamma in heterochromatin compaction and heterochromatin maintenance is interesting and raises intriguing possibilities about the role of this protein and the 20S proteasome in heterochromatic domains. The study is largely descriptive and does not provide new mechanistic insight into heterochromatin or PA28gamma. Although the experiments in the paper are of high quality and well-executed, they basically amount to identification of a new factor that affects heterochromatin stability. The fact that PA28gamma is a proteasome activator provides no mechanistic insight since the 20S proteasome does not seem to be required for the heterochromatin compaction function of PA28gamma.

The following suggestions may be helpful to the authors in preparing their manuscript for publication (in order of appearance).

1) The IP experiments in Figure 1D should be performed in the presence of nuclease (DNase/RNase A or benzonase) to test whether the interactions are bridged by RNA or DNA.

2) Figure 2. What percentage of PA28gamma and HP1beta foci overlap in the absence of alpha4 overexpression?

3) Figure 3. Does decompaction result in loss of silencing of heterochromatin targets such as HERV-K, LINE1, alpha satellite etc? Ideally, the authors should perform RNA-seq to provide a more complete picture of changes in gene expression as a result of PA28gamma depletion.

4) Based on experiments with PA28gamma-deltaC, which does not interact with the 20S proteasome, the authors conclude that the 20S proteasome is not required for the PA28gamma-mediated chromatin compaction. Although their IP data (Figure 4E) seem persuasive, a more convincing experiment would be to also perform the FRET assay for compaction with knockdown of subunits of the proteasome.

5) Figure 6. It is critical that the effects on histone modifications are evaluated using siRNA KD (or other transient KD methods) of PA28g to complement the KO results. PA28gamma KOs have many defects including genome instability and aneuploidy that may affect K9me3 and K20me3 indirectly.

6) In general, the manuscript would benefit from the addition of genome-wide approaches such as ChIP-seq to gain broader insight into PA28gamma localization and general compaction functions.

Reviewer #2:

In this manuscript, Fesquet and colleagues describe an important role of the proteasome activator PA28-gamma in the compaction of chromatin. The authors first demonstrate that PA28-gamma colocalizes HP1-beta at nuclear foci induced by the ectopic expression of alpha-4 subunit of the 20S proteasome. They further show that a fraction of PA28-gamma colocalizes also with HP1-beta in cells without ectopic expression of the alpha-4. The authors then show that PA28-gamma is associated with heterochromatic regions and is required for the compaction of lacO array integrated at a pericentromeric region. They also performed the quantitative FLIM-FRET and demonstrate that PA28-gamma controls chromatin compaction in living cells, independently of its interaction with 20S proteasome. Finally, the authors show that PA29-gamma depletion leads to a decrease of heterochromatin marks, H3K9me3 and H4K20me3, at representative heterochromatic regions. From these findings they conclude that PA28-gamma contributes to chromatin compaction and heterochromatin formation.

Although PA28-gamma has been identified as an alternative component associated with 20S proteasome, its physiological roles remain obscure. The present study demonstrates that PA28-gamma is involved in chromatin compaction and heterochromatin formation. The results presented are in most cases of high quality and convincingly controlled. I have the following concerns that should be addressed by the authors.

Major points:

1) For the localization study (Fig. 1), the authors first show the colocalization of alpha-4, PA28-gamma, and HP1-beta in the nuclear foci induced by ectopic expression of alpha-4-GFP. While the authors point out the similarity of cell-cycle dependent patterns between the alpa-4 induced foci and HP1-beta foci (lines 135-138), this argument seems to be poorly reasoned. The authors previously showed that ectopically expressed CFP-tagged alpha-7, another core component of 20S, accumulates into discrete nuclear foci, and the foci are colocalized with SC35, a well-characterized member of nuclear speckle (Baldin et al. MCB 2008). Considering that both alpha-4 and alpha-7 are core components of 20S proteasome, it is highly likely that the alpha-4-GFP- accumulating nuclear foci are corresponding to the nuclear speckles. If so, HP1-beta foci should be distinct from that of alpha-4-GFP foci. The authors should test the relationship between alpha-4-GFP foci and nuclear speckles, and if this would be the case, it might be better to omit the colocalization data using cells expressing alpha-4-GFP (Fig. 1) and start by potential colocalization of PA28-gamma and HP1-beta in cells without expressing alpha-4-GFP (Fig. 2).

2) Although the functional link between PA28-gamma and chromatin compaction seems quite interesting, it remains unclear how it contributes to the establishment of repressive histone marks such as H3K9me3 and H4K20me3. While the authors clearly show that 20S-binding-deficient PA28-gamma mutant (PA28-gamma ∆C) could restore the chromatin compaction defect caused by PA28-gamma KO, it is also possible that PA28-gamma controls the stability of factors involved in heterochromatin assembly. To exclude this possibility the authors should test whether PA28-gamma KD/KD does not affect the protein levels of core histone modifying enzymes and HP1 proteins by immunoblotting.

Reviewer #1:

In the manuscript entitled, "The 20S proteasome activator PA28γ controls the compaction of chromatin," Fesquet et al. establish a functional link between PA28γ and chromatin compaction in human cells. Previous work established a role for PA28γ in DNA repair and in chromosome stability through mitotic checkpoint regulation; however, a role, if any, for PA28γ in heterochromatin establishment/maintenance was not known. The authors use an elegant LacO-GFP system combined with PA28γ knockdown to support the possibility that this nuclear activator contributes to DNA packaging of repetitive DNA. A nucleosome proximity assay offers additional support that the most compacted chromatin is most sensitive to loss of PA28γ. Using a truncated version of PA28γ, the authors show that this chromatin function appears to be independent of its interaction with the 20S proteasome. ChIP-qPCR suggests that PA28γ binds repetitive DNA and ChIP-qPCR of PA28γ knockdown cells lose H3K9me and H4K20me, two silent heterochromatin marks. In addition to these data, the authors also attempt to establish that PA28γ and HP1β may work together to support heterochromatin formation/maintenance. The manuscript reports several intriguing pieces of data that have the potential to open new areas of inquiry into proteasome components and accessory factors in chromatin organization and remodeling. The potency of these key experiments, however, were diluted by unconvincing co-localization assays, poorly controlled PLA and ChIP-qPCR assays, and a highly speculative Discussion. Moreover, key controls were missing for several experiments (detailed below) that would have otherwise established the heterochromatin-specificity of PA28γ. Finally, important potential functional consequences of heterochromatin disruption, including chromosome segregation defects, transposable element proliferation, and accumulation of DNA damage, were not addressed while there was a focus instead on cell cycle without clear interpretations.

Major Comments:

1) Figure 2: The co-localization experiments were unconvincing - HP1β and PA28γ foci decorate most of the nucleus, making inferences about significant overlap difficult to grasp. I also found the significance of the PLA assays difficult to discern. When both factors are so abundant in the nucleus, it seems inevitable to observe loss of proximity when one 'partner' is depleted. How do these data demonstrate the specificity of this potential proximity? A clearer explanation would be helpful. Note that the PIP30 data were a distraction from the main thread - I recommend removing or explaining more clearly.

2) The ChIP-qPCR data were certainly exciting but the absence of a negative control locus made me wonder how specific this result was to DNA repeats.

3) The LacO-GFP data are really cool. Why didn't the authors not attempt to rescue compaction with a PA28γ transgene as was done for the FLIM-FRET?

4) Cell cycle data would be much more interesting if the authors set up a priori predictions based on Figures 1-5.

5) The absence of any report of PA28γ KD/KO on genome instability was surprising. Loss of heterochromatin integrity is expected to compromise chromosome transmission/transposable element expression or insertions. Do the repeats to which PA28γ localizes upregulate upon PA28γ KD or KO? Does DNA damage signaling increase at the loci? These functional consequences would be rather more explicable that the S-phase result reported.

6) The histone mark ChIP-qPCR, like the PA28γ ChIP-qPCR, lacks a negative control locus/loci, again undermining the inference of specificity of PA28γ on heterochromatin.

7) The LLPS paragraph in the discussion was weak - consider removing.

8) The speculation of 20S into foci does not add and, to my mind, detracts from the focus of the Discussion.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 3 of the manuscript.

Summary:

All three reviewers agreed that establishing a link between a proteasome activator and heterochromatin stability was novel and intriguing. However, limited insight into the PA28-gamma mechanism of action (or possibly a new heterochromatin compaction mechanism) dampened reviewer enthusiasm. The reviewers offered many suggestions, including additional experiments, new controls, and structural changes to the Discussion, that we hope you find useful.

Reviewer #3:

The paper "Morphology and local connectivity of the plis de passage in the superior temporal sulcus" is an interesting and thoughtful paper which uses modern tractography methods quite skillfully to examine whether the finer features of gyrification are related to connectivity patterns. This is an understudied area of research in human MRI because it deals with inter-individual variability, and so is time consuming, not well-suited to existing analysis pipelines, and requires a high level of neuroanatomical expertise. The methods, which included impressive inter-rater reliability and a nice control condition, were well-suited to the question. I also very much appreciated the discussion section, which covered anatomical, historical, evolutionary, and developmental considerations quite effectively and with clarity of language. Overall, the paper is well thought out and executed and a joy to read!

Below are some comments that could improve clarity for the reader:

-Figure 2 is a bit difficult to understand - to clarify that a and b are from the first brain, and b and c are from the second brain, the authors might consider labeling them or putting them in boxes. It might be helpful to add some arrows to help illustrate the "pinching" they describe.

-End of results, p. 19, final paragraph. The authors write "Second, there was generally an increasing number of U-shape fibers from the anterior to the posterior part of the STS." I don't think the authors tested this, so I would rephrase this to say "on visual inspection, it appears that there was an increase in...". I would also replace the word "fibers" with "streamlines".

Reviewer #2:

A new characterization of the "plis de passage"(PP) is proposed. The interest of this new definition is demonstrated in a cortical area where a huge amount of variability exists, hence it is very difficult to study. The results shown are convincing. The new connection established between PP and U-fibers contributes to the understanding of the link between gross anatomy and connectivity.

Several questions for clarification:

1) The distribution of the number of PP in STS is given in the results. Did you try to match the PP across the subjects, to try to define a stable model? In terms of the location of the PPs, is a model possible or their positions span the whole main branch of STS in a continuum? Did you try to study the relationships between PP and sulcal pits?

2) Did you try to clarify whether all dense clusters of U-fibers correspond to PP across subjects? Due to the random selection of the extremities of the control PPs, such clusters with different trajectories (not necessarily facing each other) could be missed by your procedure in controls?

3) Is there a link found between the superficiality of a PP and the extent of the shift of the two extremities along the sulcus (the S and C shapes)?

Reviewer #1:

The study aims to improve the anatomical characterisation of STS plis de passage (PPs). Morphologically, the authors use the geometry of the surrounding surface to reveal deep PPs, which might be buried. Structurally, they explore associations with short-range u-shape connectivity across the two banks of the STS. This methodological advancements follow from previous work on the central sulcus (e.g. Zlatkina et al., 2016, European JNS; Catani et al., 2012, Cortex). The authors provide detailed characterisation of these anatomical features in 90 individuals from the HCP dataset, and focus their analysis in differences across the two hemispheres. But the study stops short of showing how this impacts functional organisation or behaviour. Overall, the methodological advancement offered here is incremental relative to other studies, and very little insight is provided about the impact of these morphological features and their variations on STS functional organisation. Considering the HCP offers high quality functional data, including tasks specifically relating to STS function, as well other highly related data (e.g. twins), I thought the present manuscript missed numerous precious opportunities to leverage the present findings into more significant impact and innovation.

Major Comments:

1) The abstract and introduction highlight the importance of studying inter-individual variability in PPs. But the results do not address this variability, as all the results are dedicated to inter-hemispheric differences. What is the significance of inter-individual structural variance, and how is it informed by experience (the introduction suggests that these folding patterns are determined in utero?)? For example, are they more similar in twins? Is there any clear evidence that it determines functional organisation and behaviour? Clinical symptoms? Also, are the inter-individual variations observed specific to the STS? Or do they reflect 'trait' like foldiness of the cortex? None of these questions are explored empirically, and as such, the present findings offer very little advancement to our understanding of STS function and functionality.

2) I'm not sufficiently qualified to determine, but I have to wonder if the 'control PPs' are suitable, considering they are much smaller than the 'true PPs'? Considering the probabilistic nature of the analysis and the fact that the experimenters were not blinded as to which aspect of the sulcus was 'true' or 'control', some more consideration should be given to the appropriateness of this control.

3) The u-shape analysis requires histological confirmation, as demonstrated by Catani et al. for the central sulcus.

4) Nonsignificant results (e.g. between hemispheres) require further consideration - are the two hemispheres truly similar, or is the study underpowered to find such differences? Bayesian statistics can inform this question.

5) I found the discussion to be overly speculative, and in particular the part relating to functional implications to be overly speculative, considering the very modest innovative contribution the current study offered.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Summary:

The reviewers very much appreciated the careful analysis, including very laborious manual segmentation. They agreed that the study provides a new level of detail of STS morphology that hasn’t been available to date. They also agreed that this characterisation has potential to support future research focusing on the inter-individual variability that is so common in this brain region. However, the study has not yet delivered on this promise, as the analysis is focused on inter-hemispheric differences across the group, without illuminating the impact of inter-individual morphological variability on the area's functional organisation or function.

Reviewer #3:

This is a very interesting paper that describes a novel zebrafish cardiac phenotyping pipeline consisting of high frequency echocardiography, cardiac magnetic resonance imaging (CMR) and micro-computed tomography (micro-CT). The work presented provides proof-of-principle that this suite of elegant techniques provides high resolution images of the adult fish heart. The concerns raised relate mainly to the adoption of this pipeline as a routine phenotyping method and the extent to which the data presented can be considered as a reference set for the field.

Pulsed wave Doppler tracings obtained from high frequency echocardiography are noted for their clarity and reproducibility. The authors took advantage of this, together with color Doppler, to identify abnormal blood flow jets in the alk5 mutant fish. These findings nicely show that echocardiography is a useful screening tool for evaluating mutants with unknown phenotypes or for those in which structural defects are anticipated.

Echocardiography is an established method for quantification of ventricular size and function in adult zebrafish when performed by experienced operators. As noted by the authors, echocardiographic images from a single fish can be collected within minutes and this technique can be used to evaluate large numbers of fish. The real question here is when to implement the complete pipeline and in which situations echocardiography (or one of the other techniques) might be adequate. The authors might consider making some recommendations about this. For example, echocardiography would be sufficient to evaluate adult fish that are expected to have cardiomyopathy phenotypes and completion of the extended imaging pipeline may not be necessary. Procedural tolerance, potential for serial assessment, throughput and cost also need to be considered, especially when substantial numbers of fish need to be evaluated. In order to better compare echocardiography and CMR for assessment of ventricular size and contractile function, echo data for these parameters needs to be included and a comparative analysis undertaken.

The wide range of heart rates in the echo data (58-143 bpm) is a concern and suggests that anesthetic and environmental factors are contributing to variability. The lower value of 58 bpm is notably unphysiological. These extremes of heart rate would confound cardiac assessment, particularly for ventricular size. The causes of these heart rate differences need to be identified, and at the very minimum, greater numbers of fish would need to be studied to be able to identify any biological differences between groups.

A major limitation is the relatively small numbers of fish that have been included in this study. Although looking at 10 WT fish and 12 mutants was sufficient to demonstrate the utility of these imaging methods, there was considerable variability for many of the cardiac parameters measured and the number of WT fish, in particular, is far too small to be robust as a reference data set. If this is an important goal of the paper, then more male and female WT fish of different ages need to be studied. Data also need to be provided for reproducibility, and inter- and intra-observer variability for measurement of cardiac parameters using the different methods.

Reviewer #2:

In this manuscript, the authors conducted phenotypic studies of a zebrafish adult alk5a/tgfr1 mutant by integrating different technologies, including echocardiography, MRI and microCT. They selected 10 WT and 12 alk5a mutants for their studies, and identified some mild phenotypes in OFT. They conducted correlation analysis among different parameters, and then selected fish with more severe phenotypes for further morphological characterization. The strength of the manuscript is optimization of novel technologies including MRI and microCT for cardiac studies, and their integration. However, there are some notable concerns as described below.

Major concerns:

1) There is excessively high variation in almost all parameters among different fish in the same group. For example, heart rate ranges from 58-143 bpm. It appears that adult zebrafish naturally exhibit high phenotypic variation in cardiac functions. However, the authors need to more carefully control their experimental conditions before reaching this conclusion. It has been reported that anesthesia and water temperature might affect cardiac functions in this animal model.

2) The experiments were not designed to deal with the excessively high variation. Fish from three different ages are phenotyped together as a single group, and the size of the group is small. This is a main weakness of the manuscript.

3) Fig. 3-figure supplement 1: contraction of the ventricle appears rather weak (difference between F' vs F" is small). Can you calculate ejection fraction? Is the EF significantly lower than EF in wild type fish that were obtained from high frequency echo or other technologies? Low EF might indicate that the fish is far from normal physiological condition, suggesting that the technology is premature for assessing cardiac function. Moreover, there is a huge difference in heart size between WT and mutant fish (F' vs G').

Reviewer #1:

This study by Benisimo-Brito and colleagues describes a comprehensive integration of functional imaging approaches for adult zebrafish cardiovascular phenotyping. The authors describe combined use of echocardiography, MRI and (ex vivo) micro-CT with light- and transmission electron microscopy to study alk5a-mutant zebrafish. They were able to identify multiple altered phenotypic parameters including abnormal hemodynamics (retrograde blood flow), compromised functional output, and morphological defects, including expanded outflow tract and altered atria and aortae. The authors were also able to nicely correlate the extent of morphological defects with function, across a highly variable range in severity of phenotypes.

This is an informative and elegant use of combined imaging platforms to study adult zebrafish; which has thus far been very challenging, given their opaque nature and the need for specialised adaptation of available clinical modalities. That said, use of some of these platforms has been applied previously for imaging adult zebrafish; for example, echocardiography and MRI (Gonzalez-Rosa et al., 2014; Koth et al., 2017) and micro-CT (most recently, Ding et al., 2019). The authors acknowledge this, but it remains the case that the technical novelty, as applied to functional cardiovascular imaging, is compromised. Instead, the strength here is in the combined, integrated use of multiple platforms. This study on the whole provides a very nice proof-of-principle, but it is unclear how this will be widely adopted by zebrafish laboratories elsewhere, given the need for significant high-end imaging facilities and appropriate in-house expertise. Moreover, the methodologies to adapt the platforms for zebrafish studies are not sufficiently well described herein to enable others to readily adopt.

Other specific comments:

1) The statement on page 8 needs qualifying. MRI has been used previously beyond generating static images in adult zebrafish: Koth et al., (2017) documented longitudinal imaging of live adult zebrafish during heart regeneration.

2) The monitoring of heart rate using self-gating (Figure 3, figure supplement 1C-C') is a nice addition - did the authors explore the use of telemetry probes to record the ECG, as this would be a novel addition to what has gone before?

3) Regarding the correlation analysis on page 10 the authors note 32 parameters. What are the prospects for applying machine learning/AI (eg. automated image analysis algorithms) here to enhance the number of parameters that can be recovered? This in turn would increase the depth of phenotyping and further inform the phenotypic-functional association.

4) The inherent variability of phenotypes between individuals is potentially a significant issue for basic studies, despite mapping to human variation in disease progression/outcome. Given the assumed relatively in-bred nature of the mutant background, why is there such variability and does this reflect on the sensitivity of the imaging? The authors note age and body size (page 11) as influencing variation; if they were to image fish of the same age (and sex) and within a narrow body size range is this variability reduced?

5) As under the general comment above, the methodology is insufficient in places for others to adopt the described imaging platform(s); for example, under echocardiography (page 19) the authors loosely describe a "bed made of modelling clay"- more details are required here and elsewhere to facilitate others utilising similar platforms.

6) Under the MRI procedure the authors decided to analyze specimens in a container without water flow, to reduce the imaging time to less than 20 minutes and consequently to maintain survival. This relatively short imaging time is reflected in the low resolution and somewhat suboptimal images shown in Figure 3C-D. Moreover, in the absence of water flow and gill perfusion it is unclear how any functional parameters obtained are physiologically meaningful? This approach renders the use of MRI more for 3D live imaging than for interrogating function. In the previous MRI study, by Koth and co-workers (2017), live adult zebrafish were placed under anaesthesia and physiological conditions, i.e. upright in water and with gills suitably perfused. This enabled imaging for several hours and with a 100% recovery rate and consequently, the resolution and image quality were higher and the functional parameters more physiologically relevant. The current MRI approach ought to be at least comparable in terms of quality of outputs as that which has gone before.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Summary:

The reviews highlight the value of imaging adult zebrafish to evaluate cardiovascular structure and function. However, they point out that each of the three imaging technologies has been reported before, and suggest that the manuscript would be strengthened by a more critical comparison between the imaging modalities. The reviewers also raised concerns about the value of the data as a reference for cardiac function parameters, given the small numbers of WT fish, variability in WT fish, and the lack of data for reproducibility, and inter- and intra-observer variability for the various cardiac parameters. Lastly, they felt that the platforms are highly technical and require significant resource and specialist insight into adaptation for use on zebrafish, thus making it unclear how it will be applicable more broadly and within other laboratories in the field.

Reviewer #3:

The article by Youssef G et al, focused on developing a Machine Learning system to use immunofluorescence data to detect metastatic cells in tumor stroma, which might be responsible for metastasis in case of OSCC. To detect single cells in the transition of EMT to MET they focused on EMT-Stem cells rather than only EMT phenotypes. They have shown that retention of epithelial marker EpCAM and stem cell marker CD24 and upregulation mesenchymal marker Vimentin can identify disseminating EMT stem cells in the tumor stroma. It is very well presented, well written and has high implication.

Comments to improve:

1) Strongly recommended to add the distribution of tumor status vs. proposed marker expression pattern. That is to show the distribution of EpCAM, CD24, Vimentin +/- in metastatic vs. other tumor status as mentioned in Supplementary figure 2. This might help you to establish these markers combination to follow a pattern in disease progression.

2) In all cell and tissue images add the scale.

3) For figure 3f, show enlarged picture of the single cell staining on the inset or add a separate panel to show only single cell staining.

4) Figure 4, the panel name or the font is too small to read, enlarge the font size (a, b, c, d, f).

5) Same problem with figure 6a, font size too small. In addition, in the heat maps, is it possible to add cluster names horizontally? Also for figure 6c, the cluster names are too small.

6) The EMT sub-populations are not associated with a spectrum of epithelial/mesenchymal genes expression (supplementary figure 5). The explanation is not very clear.

Reviewer #2:

The authors tackle the important and intractable question of the mismatch between the primacy of EMT in cell culture studies versus the rarity with which EMT is morphologically apparent in resected tumour tissues.

The early part of the study is convincing and well conducted, with identification of subpopulations of EMT cells with the ability to undergo MET, and associated marker profiles in flow cytometry.

They then develop an impressive multiplex assay for the identification of cells with the same profile in resected tumour material- a really promising approach bringing molecular findings into the context of primary tumour tissue.

The major issue that I have is in the application of this assay to tissues, and the subsequent AI analysis. Only one example of the putative invading population is shown (Fig 4C) and the stromal 'infiltrative' subpopulation is adjacent to a very flat and 'pushing' tumour/stroma boundary, with no apparent budding into the stroma. This would need to be addressed with several more examples and high-magnification H&E images. Furthermore, this is a major claim- namely that occult infiltrating EMT cells are commonly encountered in peritumoural stroma but can only be differentiated from somatic stroma by multiplex immunofluorescence- and it needs major evidence to back it up. What do these cells look like on H&E? Are they mesenchymal in their appearances on H&E? Can they be conclusively differentiated from other stromal constituents (eg myofibroblasts, plasma cells) immunohistochemically and/or morphologically? It could be that the power to predict metastatic status power is related to somatic stromal factors rather than EMT.

The AI prediction of metastatic status is compelling, but this fundamental point would need to be persuasively addressed in order to support the author's major claims. I do not feel qualified to comment upon the AI strategies used later in the study.

Reviewer #1:

This manuscript follows previous studies describing the existence of a subpopulation of mesenchymal-like cells (expressing Vimentin) that also express EpCAM and/or CD24 concomitant with the ability to undergo MET. These subpopulations appear to exist within oral squamous cell carcinoma (OSCC) cell lines and within primary tissues. The paper demonstrates that CD24 expression is requisite for plasticity and suggests that the presence of CD24+/EpCAM+/VIM+ cells in the stroma of OSCC tumors may be indicative of metastasis. Some whole genome transcriptome analysis was also done to determine differences between bulk, EMT restricted and EMT stem populations. Overall, the notion that specific cells have the plasticity needed to move between epithelial and mesenchymal states is intriguing, and the presumption that these cells contribute to metastasis seems logical. However, the work is still rather preliminary. Accordingly, it is difficult to make solid conclusions regarding the prognostic utility of this state or of what may regulate it.

Major comments:

The study uses a very small sample size (24 patients) for the test and validation cohorts. The study should be expanded to use a different set of patient samples for test and validation sets. Moreover, the utility of the stem-EMT signature should be tested using multivariate analyses.

In figure 4, it looks like CD24 is positive in the bulk of tumors (regardless of stage) and in skin. Is this specific? Also, there appear to be VIMENTIN/EPCAM/CD24 positive cells in the bulk of non-metastatic tumours. Can this be seen using sequencing? Overall, the images as presented are not overly convincing.

EMT stem versus restricted signatures should be validated using additional models. Also, greater evidence is required to determine how these cell fractions may differ. Are they sitting in different epigenetic states? Can trajectories be detected in human cancers, using single cell sequencing, for example? Finally, do they have different metastatic potentials?

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Summary:

This manuscript was reviewed by experts in the areas of cancer stem like cells, EMT events and pathology. Overall, all of the reviewers were intrigued by the concepts underlying this paper. However, it seems that the work is validating the existence of an EMT-stem like population, whilst also attempting to formulate a clinical prognostic application for the existence of these cells. The function of these cells as metastatic drivers requires further exploration. Moreover, the pathological assessments must be improved upon. We hope that these comments are helpful.

Reviewer #3:

General assessment:

Futai and colleagues present an extremely elegant study in hippocampal CA1 slice cultures which combines cell type-specific expression of inhibitory synapse markers and conditional deletion of neurexins (Nrxn), knockdown of neuroligin3 (Nlgn3) and rescue experiments with defined splice variants of Nrxn by biolistic transfection with paired patch-clamp recordings. They find that synaptic transmission between inhibitory cholecystokinin(&VGT3)-positive interneurons (VGT3+) and CA1 pyramidal neurons depends specifically on the combination of presynaptic Nrxn1α with insert in splice site #4 and postsynaptic Nlgn3 without A1&A2 splice inserts.

Major concerns:

1.) The role of neurexins for transmission at the VGT3+ interneuron-to-CA1-pyramidal cell synapse remains unclear: The authors claim that Nrxn are important for the transmission at the VGT3+ synapse. However, I do not see the necessary experiment to substantiate such a general claim, for example, by comparing VGT3+synapses of control/undeleted to deleted NrxnTKO slices. Figure 5 rather shows that Nrxn is required to mediate the effect of overexpression of transfected Nlgn3Δ in CA1 neurons but this might be due to the overexpression itself. Thus, this effect would be more convincing if lack of Nrxn at VGT3+ synapses caused the opposite result on uIPSCs.

2.) The idea of "A Specific Neuroligin3-αNeurexin1 Code ..." implies to most readers that a direct interaction between these two molecules is involved because numerous biochemical papers in the field have used the term splice code to refer to a hierarchy of binding affinities between Nrxn and Nlgn variants. However, such preferential binding of αNrxn1+AS4 to Nlgn3Δ is neither shown in the manuscript, nor is it likely: The authors report that „αNrxn1+AS4 and βNrxn3-AS4 are the unique Nrxn genes expressed in VGT3+ neurons compared with PV+ and Sst+ neurons" (Figure 6 & 7) but demonstrate that of these two isoforms, only αNrxn1+AS4 transfected into VGT3+ interneurons mediated the effect of Nlgn3Δ overexpressed in pyramidal neurons (Figure 8). If binding or direct physical interaction was involved in the mechanism, βNrxn3-AS4 should have performed better than αNrxn1+AS4 because both the LNS5-EFG-LNS6 cassette and the insert in AS4 reduced the affinity. The surprise is shared by the authors themselves in the last paragraph of the Results section (p.12). At least to me, it appears that additional pre- or postsynaptic molecules, or a different mechanism altogether, are involved in mediating the effect of αNrxn1+AS4&Nlgn3Δ on VGT3+ synapses.

3.) To actually prove the specificity of the impact of Nlgn3Δ splice variant on inhibitory transmission from VGT3+ interneurons (Figure 2), an important control is missing: Another Nlgn3 variant, in which the A inserts are present, should be tested in the overexpression experiment. I do acknowledge that the authors compared different Nlgn3 variants in a recent paper (Uchigashima et al., 2020, JBC) in a related setting but no data exist for the proposed specificity of the Nlgn3Δ splice variant at VGT3+ synapses as far as I can see.

Reviewer #2:

Motokazu et. al., identified a specific Nlgn-Nrxn pair that regulates GABAergic synapse function in a subset of interneurons. This is a really interesting study, in which they use complicated techniques to dissect NLGN3 and NRXN function. The authors performed elaborate experiments from a single cell level to a tissue level that support their conclusions. Overall the data appear of high quality and reliable, but the study would benefit from some clarification of text and figures.

1) They are doing overexpression experiments on a WT background, so it's impossible to know if this effect is from homodimers of NLGN3 or heterodimers of NLGN3 with either NLGN1 or NLGN2. Perhaps the authors could discuss this caveat in the manuscript.

2) The authors see an increase in IPSCs when o/e NLGN3 in pyramidal neurons when Sst+ neurons were stimulated using optogenetics, whereas Horn and Nicoll did not see any changes. Horn and Nicoll used NLGN3A2 (including A2 insert) and in this study the construct doesn't have A1 or A2 insert. Perhaps they can discuss if the A2 insert can potentially be the culprit for the discrepancy if this is a potential confounding factor.

Additional comments:

1) In Fig. 1, please indicate Fig. 1C in the legends and make a box for the enlarged region in the lower magnificent image. It would be better to take out the busy alphabetic labels (E1, E2, E3, etc.).

2) Please increase text font size for the sample traces in all figures.

3) Authors showed quantitative graphs showing connectivity but definition of the connectivity is not well explained. More detailed explanation for how they quantified the connectivity should be addressed in methods.

4) In Fig. 5A, it would be more accurate to normalize KO Nrxns to WT Nrxns (set WT Nrnx as 100 %). The current Fig. 5A graph looks like Nrxn3 is not dominant in WT mice (~ 0.1 %) but the Fig. 7B graph shows Nrxn3 is dominant. Is there a discrepancy or perhaps add an explanation?

5) In Fig. 6J, the graphs for βNrxn1, αNrxn2, and βNrxn2 can go together with the image data in Figure S3.

6) Authors should explain and provide more information about the parameters of the Fig. 7A plot in the main text and legends. Correct the missed indication of Fig. 2B in the results text.

7) What if presynaptic αNrxn1+AS4 couples with Nlgn3 KD or NlgnTKO condition? What would be the expectation?

Reviewer #1:

Gaining insights into synapse-type specific regulatory mechanisms is of significant general interest. Yet, substantial concerns need to be addressed to improve this study.

Major points:

1) The authors state that Nlgn3 is particularly enriched at VGT3+ synapses. This is based on the colocalization of immunolabeling for Nlgn3 and each of the markers for three interneurons types as well as with the general inhibitory synapse marker VIAAT in Figure 1. If the intensity of marker labeling is not similar across interneuron types and if imaged fields are not comparable, the use of Nlgn3 co-labeling to assess a preferential localization is compromised. This concern is apparent e.g. in the example image for SST+ synapses with its weak labeling (Fig 1J) and needs to be addressed.

2) The data in Figure 5 support that the lack of presynaptic Nrxns 1/2/3 abolishes the potentiation effect of VGT3+ inhibitory synaptic transmission by Nlgn3Δ. To interpret these data, the authors also need to show whether the Nrxn triple KO in VGT3+ cells affects the amplitude of uIPSCs in postsynaptic control neurons expressing Nlgns at endogenous level.

3) The physiological findings are based on paired recordings where genetically labeled VGT3+ interneurons are stimulated. These cells are sparse and heterogeneously distributed in CA1 (Pelkey et al., Physiological Reviews 2017). Given the issues with Cre driver lines, a more thorough analysis is needed to establish that bona fide VGT3+ interneurons contribute to the reported findings. The scattered distribution of the individual RFP+ cells in single-cell RNAseq data (Fig 7a) adds to this concern about cell identity. The only relevant evidence presented is the IHC analysis in Fig S1A-C but it does not include probes for other interneuron types in the CA1 that shows the specificity of the VGT3+ label.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Summary

This study by Uchigashima et al. investigates to what extent Neurexin-Neuroligin interactions define synapse functions in an inhibitory microcircuit in the hippocampal CA1. The authors propose that Neuroligin-3 and Neurexin-1α regulate inhibitory synaptic transmission at synapses formed by vGluT3-positive (VGT3+) interneurons on CA1 hippocampal pyramidal neurons. This is based on (1) immunohistochemical data that localize Nlgn3 to synapses of VGT3+ interneurons, (2) the regulation of unitary inhibitory postsynaptic currents by Nlgn3 overexpression or knockdown in postsynaptic pyramidal neurons in organotypic slices from VGT3+ reporter mice, and (3) the finding that Nrxn deletion in VGT3+ interneurons prevents the effect of Nlgn3 overexpression in postsynaptic neurons. Single-cell RNA sequencing and in situ hybridization are presented to show that Nrxn1α and Nrxn3beta mRNAs are prominent Nrxn isoforms in VGT3+ interneurons, and Nrxn1α SS4 rescued Nrxn deletion effects. With some additional critical controls and a more careful interpretation of the presumed mechanism, the manuscript would make a highly interesting contribution to the field of synapse specification by synaptic cell adhesion molecules.

Author Response

Reviewer #1:

The manuscript by Mitchell et al. finds that the NAIP-NLRC4 inflammasome in mice is a critical host factor that controls intestinal infection with the human specific bacterial pathogen Shigella flexneri. The work suggests that Shigella is actively suppressing the human NAIP-NLRC4 inflammasome possibly using an T3SS effector protein, which does not recognize its substrate in mouse cells. The authors use this information to determine that B6 mice lacking the NAIP or NLRC4 inflammasome components are susceptible to Shigella infection and observe disease symptoms similar to Shigellosis in humans. In addition, 129 mice exhibit additional disease symptoms, and the authors suggest that loss of Caspase-11 in 129 mice is responsible for this phenotype.

The strengths of this manuscript include the introduction of a new mouse model that mimics Shigellosis, the demonstration that NAIP/NLRC4 activation is important for epithelial cell defense, and the potential of these findings to clarify aspects of human infectious disease caused by this pathogen. The manuscript is well presented, and the experiments are conducted with a high degree of rigor. Overall, this is an important contribution to the Shigella field and also has significant implications on our understanding of inflammasomes in host defense against pathogens.

Response: We thank the Reviewer for recognizing the impact and rigor of our work.

There are some weaknesses that should be addressed. Experimentally, it has not been directly demonstrated that IECs from NLRC4-/- mice undergo cell death (using biochemical markers). This is a critical aspect of the model.

Response: Prior work in the field (e.g., Sellin et al, 2014; Rauch et al, 2017) has already established that inflammasome activation in IECs results in their death and expulsion from the intestinal epithelium. We are currently working on showing this also occurs with Shigella but we have no reason to doubt that it does; our preliminary data indicate that Shigella-infected propidium iodide (PI)-positive cells are expelled from IEC monolayer cultures in an NLRC4-dependent manner. We intend to provide these data in a revised version of the manuscript.

In addition, it would be useful for the authors to evaluate bacterial burden over the time course in Figure 6. Although this is not absolutely necessary to support the manuscript conclusions, this information would greatly benefit the community that intends to use these mice in the future.

Response: This is indeed an experiment we plan to complete in the future. At present we are constrained by the numbers of available mice. We agree with the reviewer that the timecourse is not essential to establish the main conclusions of the present manuscript, and have thus prioritized other experiments.

There are also some discussion points about the mouse model that would enhance the overall impact of the work. For example, a more in depth discussion about the differences between human Shigella infection and the new model would be helpful. It is important to emphasize that the mouse model requires a much greater inoculum of the pathogen to induce disease and requires microbiota-deficiency to be effective. What are the implications of this finding on our understanding of human disease?

Response: Although it is often (correctly) stated that as few as 10-100 bacteria can infect humans with Shigella, there is actually considerable heterogeneity in the infectious dose. DuPont et al 1989 summarizes several human challenge studies in their Table 1, which shows that while 25-39% of humans exhibit symptoms after low dose infection (<200 CFU), 36-44% of humans are resistant to high doses (10^4-10^8 CFU). Therefore we do not consider the infectious dose in our mouse model to be out of the range of what is ‘normal’ in humans. Indeed, our new model may help us understand some of the factors that confer resistance to certain humans. We used a dose of 5x10^7 in our manuscript to ensure reproducible infection of all mice. However, in limited studies, we have observed disease in oral route infected, antibiotic pre-treated NAIP–NLRC4-deficient mice with 10^6 CFU (4/4 mice) and 10^5 CFU (2/3 mice). We are currently repeating these experiments, which we intend to include in a revised manuscript. We also agree with the reviewer that the infectious dose in humans vs. mice merits more discussion in a revised manuscript.

In lines 274-285 the authors present an either/or scenario in which either macrophage pyroptosis is required for IEC infection or inhibition of NAIP/NRLC4 pyroptosis in IECs is required for IEC infection. However, these scenarios are not mutually exclusive. For example, it is plausible that the extremely low burdens of Shigella required to infect humans (<100 CFUs) is due to the pathogen initially crossing the epithelial barrier (e.g. through M-cells) to infect macrophage, and then re-infection of IECs after macrophage pyroptosis. In this scenario, the NAIP/NLRC4 inflammasome could prevent further expansion of bacterial in IECs by eliminating the cell-to-cell spread that have been described by others. Importantly, the macrophage lifecycle stage may not be necessary in mice in which the microbiota has been removed and Shigella is delivered at a very high inoculum. While, additional ideas could be, and should be, put forth since the mouse model provides new insights or challenges an existing dogma in the field.

Response: We do clearly state in our manuscript (line 277) that our results do not directly address the question of whether Shigella might benefit from inflammasome activation in macrophages. In a revised version of the manuscript we will further expand on the discussion of the role of inflammasomes in macrophages and IECs to acknowledge multiple, non-mutually exclusive scenarios.

Reviewer #2:

Mitchell et al explore the role of NLRC4 in defending against Shigella infection by demonstrating that NLRC4 contributes to resistance to shigellosis in mice. Using in vitro assays, they first show that mouse but not human macrophages undergo NLRC4-mediated pyroptosis in response to Shigella infection despite an ability for both species to successfully detect Shigella NLRC4 agonists. They then demonstrate that C57BL/6 background mice, which normally resist shigellosis, become susceptible to infection when deficient in NAIPs or NLRC4. In parallel, 129 background mice develop more significant infection including intestinal bleeding. Furthermore, using a mouse line in which NLRC4 expression is restricted to intestinal epithelial cells (IECs), they show that IEC expression of NLRC4 is sufficient to resist shigellosis. Finally, using a known attenuated Shigella mutant, they demonstrate that their shigellosis model can mimic kinetics seen in humans.

Mitchell et al convincingly demonstrate both the importance of NLRC4 in protecting mice against Shigella and the utility of their mouse model for studying Shigella infections, both of which are significant and will push the Shigella field forward. There are mechanistic questions to be addressed in future studies beyond the current manuscript, attesting to the importance of the paper in opening up new areas in the field of research. In some places, the authors draw conclusions that reach beyond what is proven in the data, which should be addressed in text edits to the manuscript. In summary, this article presents an important new model for Shigella infection. The impact of the manuscript is the development of a mouse model with which to study Shigella infection in vivo.

Response: We thank the Reviewer for emphasizing the importance of our new shigellosis model for the field. We have addressed their comments below.

Major comments:

Many questions remain concerning why NLRC4-deficient THP1 cells still undergo pyroptosis. The authors provide evidence that Shigella activates PYRIN and/or AIM2 inflammasomes in humans, and that somehow mouse macrophages would fail to have this same detection. At face value, the data would suggest that humans are able to detect Shigella by Pyrin and AIM2, but for some reason these two inflammasomes are insufficient, and instead NLRC4 is required for in vivo defense. Then in mice, it would imply that everything is flipped - for some reason detection by Pyrin and AIM2 is not important, but now the bacteria can be detected by NLRC4 and this is important. The NLRC4 focused conclusions are consistent with the in vivo data, that NLRC4 in humans fails to detect, but NLRC4 in mice succeeds in detecting Shigella. However, the data that Pyrin and AIM2 in human cells successfully detect Shigella are inconsistent with the overall conclusions of the paper. I suspect that this is an artifact of THP1 cells, and that the in vivo situation in humans is that these two inflammasomes will fail to detect Shigella. There is published precedent from other infections where in vitro detection belies in vivo lack of detection (e.g. Listeria is detected by AIM2 in vitro, but probably not in vivo). It may be difficult to make direct comparisons between how inflammasomes act in THP1 cells as compared to BMMs, due to artifacts arising from the different origins and passage levels of the two cell types. It may be that the inflammasomes response is most important in IECs, as proposed by the authors, and that IECs may not express Pyrin or AIM2. There is evidence from publicly available IEC transcriptional profiles that IECs do not express Pyrin (Mefv) (Reikvam, doi: 10.1371/journal.pone.0017996), although this profile does show Aim2 expression in IEC. It is my understanding that BMMs do not express Pyrin unless they are strongly stimulated with some TLR agonist. As it stands, the in vitro data appear to contradict one of the main conclusions of the paper, because it would seem that human Pyrin and AIM2 inflammasomes can detect Shigella, and so these should compensate for NLRC4. The explanation as to why Pyrin and AIM2 are insufficient to compensate for NLRC4 evasion in human infection should be addressed at least in discussions of the data to explain the apparent discrepancy.

Response: The reviewer states that our claim that human PYRIN and AIM2 inflammasomes can detect Shigella in THP1 cells is “inconsistent” with the overall conclusion of our paper, which is that the NLRC4 inflammasome provides necessary defense of mouse intestinal epithelial cells. We do not agree that there is an inconsistency and indeed many of the points the reviewer makes in their comments fit with our view, so perhaps there is less disagreement than it might seem.

As the reviewer discusses, differences in inflammsome expression in humans vs. mice, and in IECs vs. macrophages vs. THP1 cells, and the kinetics of inflammasome responses, as well as several other factors, can easily account for the results we obtain. It appears that PYRIN is not well expressed in mouse IECs (Price et al. 2016), at least not uniformly at levels in all cells that are sufficient to confer protection. AIM2 is expressed in colonic IECs (Price et al. 2016), but it is not clear that it would be engaged in every infected IEC. For example, AIM2 detects bacterial DNA, which might only be released if the Shigella bacteria lysed in the cytosol. As noted by the reviewer, this may be a relatively rare event, as previously documented for AIM2 activation by Listeria-infected macrophages (Sauer JD et al, 2010). AIM2 activation may also be kinetically delayed in IECs. It appears instead that NLRC4 is the main inflammasome that can respond to Shigella in mouse IECs; thus loss of NLRC4 is sufficient to lead to susceptibility of mice. It remains possible that there is some functional AIM2 or PYRIN (or CASP11 or NLRP1B) in mouse IECs; thus, the further removal of these inflammasomes might lead to even greater susceptibility. Alternatively, a low level of activation mediated by these additional inflammasomes (perhaps in macrophages instead of in IECs) might even be necessary to produce the inflammation that causes disease symptoms.

In humans, consistent with our data in Fig. 1, we propose that the NLRC4 inflammasome is antagonized or otherwise evaded by Shigella. The reviewer wonders why PYRIN or AIM2 cannot compensate for NLRC4, and is suspicious that the activation of PYRIN/AIM2 we observe in THP1 cells is not representative of what would occur in vivo. Certainly we agree that THP1 cells are non-physiological and we do not attempt to make claims in the manuscript that our observation of AIM2/PYRIN activity in these cells means anything for human shigellosis.

The reviewer states: “the in vitro data [in THP1 cells] appear to contradict one of the main conclusions of the paper, because it would seem that human Pyrin and AIM2 inflammasomes can detect Shigella, and so these should compensate for NLRC4.” For all the reasons discussed above, we do not agree there is a contradiction. There are many reasons why PYRIN and AIM2 might function in THP1 cells (and possibly even human macrophages) but would not compensate for NLRC4 in IECs.

In sum, we agree that there is more to learn about which inflammasomes, if any, are activated by Shigella in human IECs, but given the many uncertainties, we do not feel it is fair to say that our results are internally contradictory. We will endeavor to discuss some of these points in a revised manuscript.

Reviewer #3:

Mitchell et al describe the development of a mouse model for shigella gastroenteritis, the lack of which has been a serious impediment to Shigella research. They identified a difference in recognition of shigella between human and mouse Naip/NLRC4 which contributes to the resistance of mice to Shigella gastroenteritis. They suggest that Shigella specifically inhibits human Naip/NLRC4 activation and that the difference between mice and human susceptibility to infection is due to differential inhibition. This was confirmed by the ability of NLRC4-/- mice can recapitulate human infection. Furthermore they show that it is inhibition of NAIP-NLRC4 in IEC that is required for infection to occur. This manuscript therefore describes a number of important findings and uses these to develop a very useful animal model of shigellosis.

We are grateful for the Reviewer’s comments and suggestions, and provide point-by-point responses below:

I have three suggestions that I believe would improve the manuscript:

1) Determine the inflammasome that causes cell death in Shigella-infected THP1's. WT Shigella infection did not induce pyroptosis of colchicine-treated (PYRIN inhibitor) AIM2-/- THP1 cells, indicating one or both of these inflammasomes is responsible for the cell death observed in shigella infected THP1 cells. Why not test these separately to determine which?

Response: We have now made AIM2/MEFV–/– THP-1 cells. Our preliminary finding is that cell death and IL-1B levels in these cells are impaired in response to Shigella infection. We intend to include these data in a revised manuscript.

2) Markers of inflammation during disease. Clinical features of the disease (diarrhoea, weight, CFU/organ, fecal blood) are described well. But since Shigellosis is an inflammatory disease, it would have been nice to have seen some inflammatory molecules/cytokine levels measured, in addition to clinical features. The authors did measure levels of MPO, but that was as a marker for neutrophil recruitment.

Response: We agree that additional readouts of inflammatory disease are warranted. We are planning to repeat our experiments and measure cytokines in the blood. We intend to provide these data in a revised manuscript.

3) Further refinement of the mouse model. The authors present the inhibition of human NAIP/NLRC4 as the main factor that affects the difference in infection between humans and mice but a high innolcum (5 x 10(7) cfu/mouse compared to approx. 100 cfu for humans) is still required in addition to streptomycin treatment. It is not discussed whether any refinement of these procedures was attempted or why such a high inoculum and streptomycin treatment is still required. Presumably microbiota differences in addition to naip-/nlrc4 is an important species specific determinant of infection, hence the streptomycin treatment. Why is such a high innoculum required?

Response: this comment is similar to one of the comments of Reviewer 1. As we state above, it is actually not entirely clear that the infectious dose for humans is consistently ~100 CFU. Indeed, there appears to be great variation, with some humans exhibiting resistance to doses more than 10^5 CFU. Although we used high inoculums in our experiments, this was just to ensure consistent infection of all mice. Preliminary experiments in which we reduce the dose suggests that, like some humans, some mice are also susceptible to lower doses (e.g., 10^5 CFU). Thus our model exhibits an infectious dose within the range of what is observed in humans and we do not feel there is a large discrepancy here, though it appears that we do not recapitulate the extreme susceptibility seen in some humans. We don’t find this particularly surprising as Shigella is a human-specific pathogen and it is likely that at least some of its virulence factors may not work well in mice. Instead, we think what is most surprising is that loss of one host defense component (NLRC4) is sufficient to produce disease symptoms that are strikingly similar to what is seen in humans. We acknowledge that one difference is the need for streptomycin in our model. Clearly this suggests, as the reviewer states, that the microbiota can influence susceptibility. This is a well-described phenomenon with many enteric pathogens and it will be of interest in future studies to determine what components of the microbiota afford protection in our model.

Reviewer #3:

Mitchell et al describe the development of a mouse model for shigella gastroenteritis, the lack of which has been a serious impediment to Shigella research. They identified a difference in recognition of shigella between human and mouse Naip/NLRC4 which contributes to the resistance of mice to Shigella gastroenteritis. They suggest that Shigella specifically inhibits human Naip/NLRC4 activation and that the difference between mice and human susceptibility to infection is due to differential inhibition. This was confirmed by the ability of NLRC4-/- mice can recapitulate human infection. Furthermore they show that it is inhibition of NAIP-NLRC4 in IEC that is required for infection to occur. This manuscript therefore describes a number of important findings and uses these to develop a very useful animal model of shigellosis.

I have three suggestions that I believe would improve the manuscript:

1) Determine the inflammasome that causes cell death in Shigella-infected THP1's. WT Shigella infection did not induce pyroptosis of colchicine-treated (PYRIN inhibitor) AIM2-/- THP1 cells, indicating one or both of these inflammasomes is responsible for the cell death observed in shigella infected THP1 cells. Why not test these separately to determine which?

2) Markers of inflammation during disease. Clinical features of the disease (diarrhoea, weight, CFU/organ, fecal blood) are described well. But since Shigellosis is an inflammatory disease, it would have been nice to have seen some inflammatory molecules/cytokine levels measured, in addition to clinical features. The authors did measure levels of MPO, but that was as a marker for neutrophil recruitment.

3) Further refinement of the mouse model. The authors present the inhibition of human NAIP/NLRC4 as the main factor that affects the difference in infection between humans and mice but a high innolcum (5 x 10(7) cfu/mouse compared to approx. 100 cfu for humans) is still required in addition to streptomycin treatment. It is not discussed whether any refinement of these procedures was attempted or why such a high inoculum and streptomycin treatment is still required. Presumably microbiota differences in addition to naip-/nlrc4 is an important species specific determinant of infection, hence the streptomycin treatment. Why is such a high innoculum required?

Reviewer #2:

Mitchell et al explore the role of NLRC4 in defending against Shigella infection by demonstrating that NLRC4 contributes to resistance to shigellosis in mice. Using in vitro assays, they first show that mouse but not human macrophages undergo NLRC4-mediated pyroptosis in response to Shigella infection despite an ability for both species to successfully detect Shigella NLRC4 agonists. They then demonstrate that C57BL/6 background mice, which normally resist shigellosis, become susceptible to infection when deficient in NAIPs or NLRC4. In parallel, 129 background mice develop more significant infection including intestinal bleeding. Furthermore, using a mouse line in which NLRC4 expression is restricted to intestinal epithelial cells (IECs), they show that IEC expression of NLRC4 is sufficient to resist shigellosis. Finally, using a known attenuated Shigella mutant, they demonstrate that their shigellosis model can mimic kinetics seen in humans.

Mitchell et al convincingly demonstrate both the importance of NLRC4 in protecting mice against Shigella and the utility of their mouse model for studying Shigella infections, both of which are significant and will push the Shigella field forward. There are mechanistic questions to be addressed in future studies beyond the current manuscript, attesting to the importance of the paper in opening up new areas in the field of research. In some places, the authors draw conclusions that reach beyond what is proven in the data, which should be addressed in text edits to the manuscript. In summary, this article presents an important new model for Shigella infection. The impact of the manuscript is the development of a mouse model with which to study Shigella infection in vivo.

Major comments:

Many questions remain concerning why NLRC4-deficient THP1 cells still undergo pyroptosis. The authors provide evidence that Shigella activates PYRIN and/or AIM2 inflammasomes in humans, and that somehow mouse macrophages would fail to have this same detection. At face value, the data would suggest that humans are able to detect Shigella by Pyrin and AIM2, but for some reason these two inflammasomes are insufficient, and instead NLRC4 is required for in vivo defense. Then in mice, it would imply that everything is flipped - for some reason detection by Pyrin and AIM2 is not important, but now the bacteria can be detected by NLRC4 and this is important. The NLRC4 focused conclusions are consistent with the in vivo data, that NLRC4 in humans fails to detect, but NLRC4 in mice succeeds in detecting Shigella. However, the data that Pyrin and AIM2 in human cells successfully detect Shigella are inconsistent with the overall conclusions of the paper. I suspect that this is an artifact of THP1 cells, and that the in vivo situation in humans is that these two inflammasomes will fail to detect Shigella. There is published precedent from other infections where in vitro detection belies in vivo lack of detection (e.g. Listeria is detected by AIM2 in vitro, but probably not in vivo). It may be difficult to make direct comparisons between how inflammasomes act in THP1 cells as compared to BMMs, due to artifacts arising from the different origins and passage levels of the two cell types. It may be that the inflammasomes response is most important in IECs, as proposed by the authors, and that IECs may not express Pyrin or AIM2. There is evidence from publicly available IEC transcriptional profiles that IECs do not express Pyrin (Mefv) (Reikvam, doi: 10.1371/journal.pone.0017996), although this profile does show Aim2 expression in IEC. It is my understanding that BMMs do not express Pyrin unless they are strongly stimulated with some TLR agonist. As it stands, the in vitro data appear to contradict one of the main conclusions of the paper, because it would seem that human Pyrin and AIM2 inflammasomes can detect Shigella, and so these should compensate for NLRC4. The explanation as to why Pyrin and AIM2 are insufficient to compensate for NLRC4 evasion in human infection should be addressed at least in discussions of the data to explain the apparent discrepancy.

Reviewer #1:

The manuscript by Mitchell et al. finds that the NAIP-NLRC4 inflammasome in mice is a critical host factor that controls intestinal infection with the human specific bacterial pathogen Shigella flexneri. The work suggests that Shigella is actively suppressing the human NAIP-NLRC4 inflammasome possibly using an T3SS effector protein, which does not recognize its substrate in mouse cells. The authors use this information to determine that B6 mice lacking the NAIP or NLRC4 inflammasome components are susceptible to Shigella infection and observe disease symptoms similar to Shigellosis in humans. In addition, 129 mice exhibit additional disease symptoms, and the authors suggest that loss of Caspase-11 in 129 mice is responsible for this phenotype.

The strengths of this manuscript include the introduction of a new mouse model that mimics Shigellosis, the demonstration that NAIP/NLRC4 activation is important for epithelial cell defense, and the potential of these findings to clarify aspects of human infectious disease caused by this pathogen. The manuscript is well presented, and the experiments are conducted with a high degree of rigor. Overall, this is an important contribution to the Shigella field and also has significant implications on our understanding of inflammasomes in host defense against pathogens.

There are some weaknesses that should be addressed. Experimentally, it has not been directly demonstrated that IECs from NLRC4-/- mice undergo cell death (using biochemical markers). This is a critical aspect of the model. In addition, it would be useful for the authors to evaluate bacterial burden over the time course in Figure 6. Although this is not absolutely necessary to support the manuscript conclusions, this information would greatly benefit the community that intends to use these mice in the future.

There are also some discussion points about the mouse model that would enhance the overall impact of the work. For example, a more in depth discussion about the differences between human Shigella infection and the new model would be helpful. It is important to emphasize that the mouse model requires a much greater inoculum of the pathogen to induce disease and requires microbiota-deficiency to be effective. What are the implications of this finding on our understanding of human disease? In lines 274-285 the authors present an either/or scenario in which either macrophage pyroptosis is required for IEC infection or inhibition of NAIP/NRLC4 pyroptosis in IECs is required for IEC infection. However, these scenarios are not mutually exclusive. For example, it is plausible that the extremely low burdens of Shigella required to infect humans (<100 CFUs) is due to the pathogen initially crossing the epithelial barrier (e.g. through M-cells) to infect macrophage, and then re-infection of IECs after macrophage pyroptosis. In this scenario, the NAIP/NLRC4 inflammasome could prevent further expansion of bacterial in IECs by eliminating the cell-to-cell spread that have been described by others. Importantly, the macrophage lifecycle stage may not be necessary in mice in which the microbiota has been removed and Shigella is delivered at a very high inoculum. While, additional ideas could be, and should be, put forth since the mouse model provides new insights or challenges an existing dogma in the field.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Summary

In this manuscript, the authors introduce a new mouse model of Shigellosis, provide evidence for NAIP/NLRC4 activation as being important for epithelial cell defense, and apply these findings to observations made in humans infected by this pathogen. These are important findings and provide an opportunity to further advance the field in ways not previously possible. However, there are areas where the in vitro and in vivo data presented contradict each other, and there are inconsistencies with previously published work by the authors. In addition, with the development of the new mouse model being a major highlight of this manuscript, significantly more detail and discussion must be added to explain this mouse model.

Reviewer #3:

Luo and colleagues use a combination of viral tracing and targeted neuronal manipulation tools to dissect the role of GABAergic retinal ganglion cells (RGC) in mediating aversive responses to looming visual stimuli. This paper reports the existence of a population of GABAergic RGCs projecting to the superior colliculus (SC). These conclusions were based on a set of retrograde and anterograde tracing experiments in two mouse lines that putatively label GABAergic neurons (vGAT-Cre and GAD2-Cre). Targeted ablation of the GABAergic RGCs compromised looming-triggered escape behavior, which suggests a possible involvement of the superior colliculus projecting GABAergic RGCs in mediating the looming-evoked flight response. Although these findings could provide important insights into the neural circuitry that mediates aversive behaviors, tracking the origin of these circuits back to the retina, we have major concerns with the paper in its current format.

The current data set raises three major concerns that need to be addressed.

-First, the specificity of the labelling strategies is insufficient to make the current claims. The viral tools used to kill or manipulate RGCs are not specific for either RGCs (shRNA experiment), or SC-projecting RGCs (DTA experiments), and hence do not support the pathway specific claims in the manuscript. Also, the presented data raises questions as to whether all labeled neurons in these mouse lines are functionally inhibitory in the adult retinal.

-Second, the behavioral tests performed do not check for effects of killing GABAergic RTGCs on thalamic dependent visual processing.

-Third, the presentation of the data makes it very difficult for the reader to ascertain the claims made by the authors. In addition, the writing needs major revision.

Major concerns:

1) Lack of specificity of the labelling strategy. The authors claim that GABAergic RGCs mediate escape responses via GABA release in the SC. The current data does not support this claim since none of the used tools is specific enough. To maintain these claims, the authors need to either test if the SC-projecting GABAergic RGCs have no (or minimal) collateral projections to other targets or if the ganglion cells that collaterally project to other brain areas are not involved in the aversive behavior being tested. Further, it is necessary to narrow down the cell populations affected by their manipulations and to show that GABA-release by RGCs is involved in the tested escape behavior.

a. We are concerned that the mouse lines used, in particular the vGAT line, do not label cells that are functionally GABAergic in an adult animal. The gene coding for vGAT, Slc32al, is found in amacrine cells, but not in RGCs (Siegert et al. 2011). In Figure 1, the GABAergic positive cell bodies are not confirmed as being RGCs, i.e. having an axon. In Figure S2 the authors do not differentiate between GAD2 and vGAT.

b. The viral tools used for ablating SC-projecting GABAergic neurons are not specific for the SC, but will also label very common collaterals to brain targets other than the SC including the thalamus (e.g. Ellis et al., 2016).

c. The shRNA approach to knock down vGAT expression removes vGAT from all types of vGAT-expressing retinal neurons, not only RGCs. It is very likely that vGAT-expressing amacrine cells are affected by this manipulation.

d. Please remove the claims that the behavior is mediated through the PBGN pathway. The transsynaptic HSV approach to label multisynaptic targets of GABAergic RGCs does not support this claim. It is unknown whether the axon terminals in the PBGN labelled in these experiments stem from the SC. Also, other SC-targets that are known to mediate escape, such as the PAG (Evans et al. 2018), are also labelled in these experiments.

2) Inadequate test of visual circuitry function. The approaches used by the authors to test for different aspects of visual processing focus on a few known reflex pathways, but do not directly test for thalamic/cortical dependent visual behaviors, i.e. image formation. This needs to be changed in the description of the tests and the interpretation of the results. The description in the figure itself is good, but the conclusions drawn are misleading. The authors use four different approaches to test for visual function and draw the following conclusions:

a. Looming-evoked escape is decreased in two experimental conditions where vGAT-expressing neurons are impaired. The authors conclude that GABAergic RGCs projecting to the SC mediate escape. As described in point 1, these experiments are not specific enough to make those claims.

b. Electroretinograms (ERG) have unchanged a- and b- waves, which leads to the claim that GABAergic RGCs are not necessary for normal retina function. This is misleading as the largest contributors to an ERG signal are the photoreceptors and bipolar cells (e.g. Smith, Wang ... and Trembley, 2014).

c. Optokinetic reflex is unchanged after vGAT ablation. The authors conclude from these experiments that image formation is independent of GABAergic RGCs. This approach only tests for very specific retinal projections, probably to the AOS, but does not test for the function of the LGN-cortex projections, which form the major image formation pathway.

3) Insufficient data presentation. The currently presented histological sections are not sufficient to draw the same conclusions as the authors. In addition, several of the experiments lack clear quantifications to back up the claims in the text. The authors need to provide complete and readable pictures, and add quantifications to support their claims.

a. The role of PV+ SC neurons in the present study is unclear. The authors do not provide adequate evidence that GABAergic RGC-recipient neurons in the colliculus are PV+ (line 196). The referenced figure (Fig. 4B) shows only a single example of a staining. Quantification of the % of labeled neurons that are PV positive is required to strengthen this claim.

b. Please provide complete images of the histology at a readable size for all figures and add outlines of brain areas where necessary. Importantly, in Fig. 1G it looks as if the RGC axon terminals are only present in the intermediate layers of the medial SC. Since it is claimed that the GABAergic RGCs include many different types, one would expect axon terminals across all depths of the superficial SC.

c. The re-analysis of the published scRNA results from Rheaume et al 2018 should be made clear in the manuscript. Currently there is no information in the main text about the underlying data set or analysis.

d. It is not clear in the text what the differences/similarities are between vGAT- and GAD2-Cre mouselines. Please make clear in the narrative and conclusion how each mousseline was used.

Reviewer #2:

In this study, Luo et al. report that GABAergic retinal ganglion cells projecting to the superior colliculus (spgRGCs) drive defensive responses to looming. Previous studies demonstrated that neurons in the superior colliculus (SC) mediate behavioral responses to looming. Most of the >40 ganglion cell types in mice project to SC. Which of these convey the relevant looming signals from the retina is unclear. Most ganglion cells express VGLUT2 and release glutamate from their axon terminals, but anatomical evidence suggested that a subset of ganglion cells may contain GABA. Furthermore, a recent study (Sonoda et al., 2020) showed that some intrinsically photosensitive retinal ganglion cells are labeled in Gad2-Cre mice and reduce the light sensitivity of photoentrainment and pupillary light responses.

Here, Luo et al. find that intravitreal injections of Cre-dependent adeno-associated virus (AAVs) reporters in Vgat-Cre and Gad2-Cre transgenic mice label ganglion cell axons in many retinorecipient brain areas, including SC. The authors reanalyze a published single-cell RNA sequencing dataset (Rheaume et al., 2018), which suggest that subsets of ganglion cells of most types express Gad2. Using optogenetics, the authors confirm that activation of Gad2-Cre- and Vgat-Cre-positive ganglion cells elicit inhibitory postsynaptic currents (IPSCs) in SC neurons. Based on retrograde tracing, the authors suggest that these ganglion cells belong to a variety of types. Next, Luo et al. demonstrate that the deletion of spgRGCs abolishes defensive responses to looming stimuli and looming-evoked cFos expression in SC. The authors illustrate the selectivity of these effects by showing that electroretinograms, optomotor responses, and pupillary light responses are unaffected by spgRGC deletion. Finally, the authors use an AAV-based shRNA strategy to knock down Vgat in the retina and show that this abolishes looming responses.

Overall, this study reports a surprising and potentially transformative finding (i.e., that a small subset of many RGC types uses GABA to drive looming responses in SC and behavior). The authors leverage a wide range of techniques to study spgRGCs, but some results and interpretations are confusing, and some conclusions are insufficiently supported evidence.

Specific comments:

1) The Vgat knockdown experiments are critical to show that GABAergic transmission matters. The current strategy targets all Vgat-expressing neurons in the retina. The vast majority of these are amacrine cells. Silencing amacrine cells will likely have widespread effects among ganglion cells. The authors should use a dual AAV strategy similar to the one they employed for DTA to restrict Vgat-shRNA expression to spgRGCs and show that ganglion cells' responses to looming are unchanged.

2) Previous studies show that activation of SC neurons (particularly PV+cells) promotes defensive responses to looming, and the cFos labeling in this study suggest that spgRGCs activate SC neurons. Yet, optogenetics experiments indicate that spgRGCs elicit IPSCs in SC neurons. These findings seem at odds. Although the authors show that some spgRGCs elicit a mixture of EPSCs and IPSCs, the Vgat knockdown experiments suggest that the GABAergic transmission mediates looming signals and elicits behavioral responses. The authors should characterize looming responses in SC by electrophysiology or optical recordings (as they have done in previous studies) to clarify the contributions of spgRGCs.

3) Details of the cFos experiments were missing. The authors should compare cFos labeling and changes in cFos labeling after spgRGC ablation between looming and other visual stimuli, to discern the specificity of these effects.

4) The characterization of spgRGC types is superficial. The authors should show patch-clamp recordings from a small number of RGCs, which seem to encompass a variety of types. The authors should record light responses characterization (incl. responses to looming stimuli) and reconstruct the morphology of a larger number of ganglion cells to classify types in line with other studies (e.g., Bae et al., 2018, Reinhard et al., 2019).

Reviewer #1:

The goal of this study is to identify the retinal ganglion cells that mediate the flight response of mice to a looming stimulus. The candidate they focus on are a subset of RGCs that release GABA at synapses with a particular subtype of neuron in the SC that was previously implicated in this behavior.

The impact of the paper is limited for two main reasons. First, there was a paper using a similar mouse line that was just published (Sonoda et al, Science 2020) that revealed that GABAergic intrinsically photosensitive RGCs shape several of the non-vision forming behaviors in mice (such as photoentrainment of circadian rhythms and the pupillary light reflex). The authors may not have been aware of this work when they submitted this paper but now that it is published, the authors need to more rigorously compare their results to that study.

Second, it is not at all clear that the authors have identified a subtype of RGCs that mediate the looming responses. Rather their data (particularly Figure 3) seems to argue that a lot of different RGC subtypes have GABA. So the model is that the 13% of multiple RGC subtypes project to PV cells in the SC and together they mediate the looming response?

Finally, there is a lack of quantitative description of many of the experiments that undermines many of the conclusions the authors want to make. These are described explicitly below.

1) The authors make use of both a GAD2-Cre and vGAT-Cre to label cells in the retina, apparently the results from the two lines are combined throughout the paper. The authors need to verify that the same cells are labeled for each line.

2) In Figure 1, the authors show beautiful images of their labeling but the quantification of RGCs that express GABA is not described. In the mouse retina 50% of the cells in the ganglion cell layer are amacrine cells. They do show some labeling in the optic nerve so clearly some RGCs are labeled but there is no way to know how many. Rather the authors rely on a re-analysis of an RNA-seq data set to estimate that 13% of RGCs across all subtypes! Of course, protein levels and not transcripts are what matter for this sty so at least a co-stain for a RGC marker would strengthen the finding. This would also resolve the issue brought up in point 1 above.

3) Figure 2. The authors use optogenetics to characterize the synaptic connections with target neurons in the SC. Again, there is a surprising lack of quantification. In Figure 2C they show light activation ChR induces an inward current but they don't say how many times they do that experiment. Most experiments are done in TTX + glutamate receptor blockers to isolate GABAergic currents but there is a subset in which the igluR blockers are absent and excitatory currents were detected. The authors need to clarify in what percent of neurons did they see GABAergic currents and in what percentage excitatory currents and in what percentage did they see both? Basically, the authors need to clarify if these RGCs are releasing both GABA and glutamate. This is critical for interpreting the experiments in which they kill this population of neurons and inhibit the behavior.

4) Figure 3. The authors use retrograde labeling to begin to identify the GABAergic RGC subtypes that project to SC. Again, the quantification is lacking - what percent of SC projecting cells were positive for GABA? It is really a confusing result because they find an array of RGC subtypes that seem to express GABA. Hence it does not appear that one type of RGC projects to SC but rather all types - but just the subset that release GABA along with glutamate. 5) Figure 4AB appears quite impressive but the logic is not clear. Does Herpes simplex virus work as an anterograde transsynaptic virus? More explanation is required. Again, there is no quantification of the results - just examples of single neurons found in several retinorecipient brain regions.

(Note: Figures 4C-G are impressive - killing this subpopulation of cells seems to eliminate the response to looming stimuli while other visually guided behaviors are retained.)

6) Figure 5H - this is a difference with the Sonoda paper - they find an effect on PLR when they reduce GABA release from ipRGCs.

7) Figure 6 - the authors use RNAi to reduce vGAT expression in spgRGCs and this also impacts behaviors. There are many controls that need to be done here primarily showing the glutamate release is normal. Otherwise this could just be a synaptic transmission deficit.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 2 of the manuscript.

Summary:

This study reports that a small subset of different RGC neuron types that release GABA at synapses with a particular class of neurons on the super colliculus mediate the looming responses in mice. This result is potentially highly significant and as noted by one reviewer, potentially transformative in our thinking of how RGC cell types mediate behaviors. However, all three reviewers agree that many of the conclusions are insufficiently supported by the evidence. The reviewers offer many details for necessary experiments and clarifications that need to be made in order for the authors to be able to reach their conclusion.

Reviewer #3:

The bHLH transcription factor Atoh7 has been studied as a critical regulator of retinal ganglion cell (RGC) generation in several species but, as the authors detail in the Introduction, it is not clear how or at what stage it acts. For example, some (most) data suggest it is required to specify the RGC fate in precursors, while other data suggest it may be required for RGC differentiation and/or survival following their generation. Here, Brodie-Kommit et al. use a well-established method to distinguish these possibilities, deleting Atoh7 in the absence of Bax, a powerful proapoptotic gene. Both naturally occurring and genetically-provoked apoptosis of many neuronal types, including RGCs, have been shown to be prevented in Bax mutants, which are viable and generally healthy.

The authors show that RGCs survive and are functionally normal in the absence of both Atoh7 and Bax, but few axons leave the retina, so of course light-induced behaviors are greatly decreased. Single cell RNAseq demonstrates a delay in RGC differentiation in the absence of Atoh7 (with or without Bax) and a variety of gene expression changes.

As expected for a paper from two superb laboratories, the work is done to the highest standard and uses the best available methods. The result that blocking apoptosis rescues RGCs in the absence of Atoh7 is important and should help resolve controversies about its role, providing a strong argument against what is likely still the best-accepted model.

On the other hand, the paper does not go far beyond that simple result: it shows what Atoh7 does not do, but not what it does do, either to the RGCs that express it or to the RGCs that do not express it but nonetheless require it for survival. The physiological and histological data largely back up the survival result; the behavioral defects are sort of trivial once one knows that RGC axons fail to reach the brain; and the RNAseq data do not lead to substantial novel insights that shed light on either the presumably cell-autonomous or the clearly cell-nonautonomous mechanisms.

Reviewer #2:

In the present manuscript the authors reveal that RGC differentiation is largely rescued in the absence of Atoh7 when the pro apoptotic gene Bax is also removed in the developing retina. These rescued RGCs show some proper physiological responses but fail to develop proper connections to the brain. Retina vasculature is also affected by the absence of Atoh7 even when RGCs are "rescued". Finally by single cell analysis they reveal that Atho7 is required for proper timing of RGC differentiation but the expression of major markers for RGC can be independent from Aoh7 transcriptional activity. The paper is based on a series of very elegant genetic experiments and the single cell analysis is particularly illuminating in this context.

Major Points:

Cell death is only one of the RPC possible fates in the absence of Atoh7. Indeed the author and a vast amount of literature showed that in the absence of Atoh7 more adopt photoreceptor precursor fate among others. Is the block of apoptosis by Bax inactivation reducing this "ectopic differentiation phenotype" in addition to RGC fate restoration?

Linked to the previous point, does the single cell data reveal why some progenitors die in the absence of Atho7 while others change fate?

The authors should discuss this point in more detail.

Reviewer #1:

This manuscript challenges the notion that the transcription factor Atoh7 is required to confer neurogenic retinal progenitors the competence of generating retinal ganglion cells (RGCs), the first-born neurons of the retina. This idea is based on the evidence that Atoh7 inactivation in mice causes the loss of the majority of RGCs. Here the authors have generated a Atoh7Cre/Cre;Bax-/- mouse line to ask what happens if apoptotic cell death is prevented in Atoh7 null mice. Using a number of RGC markers, they show that in the adult retina a large number of RGCs are no longer lost and are functionally connected with other retinal cell types as the retinas generate light driven photic responses. However, the RGCs of the Atoh7Cre/Cre;Bax-/- mice cannot connect with brain targets as the axons (when present) do not exit the optic disk but grow in a disorganized manner within the fibre layer. As an additional feature, the hyoloid artery does not regress. In Atoh7Cre/Cre;Bax-/- embryos, RGC generation is delayed as determined by analysis of single cell RNA-seq. The authors conclude that Atoh7 is required for RGC survival but dispensable for their specification.

This is an interesting study that adds up to the existing literature related to the role of Atoh7 in RGC generation/differentiation. However, the conclusion seems rather stretched: do the cells generated in the absence of Atoh7 and Bax really have a (full) RGC identity as claimed in the title? Is the specification of ALL RGC really independent of Atoh7? Conclusions should be toned down and alternative interpretations should be offered. Indeed, preventing apoptosis does rescue the full number of RGCs (see for example melanopsin positive cells). The lack of Isl1 in Fig. 4 and the low number of Brn3a+ cells in Fig. S6 is rather striking and suggests more than a delay. Thus, at least a subset of RGCs seems to require Atoh7, likely early born RGCs. There are several studies indicating that RGCs secrete factors that regulate their own number (GDF11, Kim et al., 2005, Science, as an example). Lack of this feed-back at early stages may favour the generation of RGCs that are not full Atoh7-dependent, creating an imbalance between Atoh7-dependent (early) and Atoh7-independent (late) RGCs.

The second problem that remains unanswered is related to the "identity" of the RGCs present in Atoh7Cre/Cre;Bax-/- embryos. Are they really bona fide RGCs? These cells cannot connect properly with their brain target nor secrete the putative factors needed to induce hyaloid artery regression. These defects could perhaps be explained by asynchrony (cells are generated late to read the axon guidance cues, for examples) but they may also be interpreted as lack of full identity.

The authors need to consider these possibilities and further address the related points below:

1) The difference in cell number detected with RBPMS and Isl1 is puzzling (Fig. 1). Isl1 recognises RGCs but also amacrine cells, which should be increased in absence of Atoh7. How do the authors explain that Isl1+ cells are less than the RBPMS+ ones in Atoh7Cre/Cre;Bax-/- mice.

2) The sentence "Brn3b-positive ipRGCs differentiate normally in the absence of Atoh7" is an overstatement. Only 35% of them do, the others are presumably lost. Furthermore, the presence of a cell specific marker does not ensure that the cells are fully differentiated.

3) Line 435. Presumably a sentence describing the response of RGC in Atoh7Cre/Cre;Bax-/- is missing.

4) Lines 506-509. Failed vasculature regression: the authors state "...implies that Brn3b and Isl1 may activate expression of secreted factors that drive vascular regression". If this is the case why in Atoh7Cre/Cre;Bax-/- retinas the hyaloid artery is still present? The retinas do express levels of Isl1 and Brn3b so that these factors should be present.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Summary:

The three reviewers agree that the study is very elegant and well performed. However, they also find that the conclusions are rather stretched and there is no clear demonstration of what Atoh7 is needed for. Major concerns relate to the real identity of the rescued cells and the claimed independence of RGC specification from Atoh7. Unfortunately, the RNAseq data do not illuminate this issue or solve the cell-autonomous and non cell-non-autonomous mechanisms that are at the basis of the present observations.

Reviewer #2:

The focus of this paper is the zinc metalloprotease ADAMTS-5. This protein has received attention as a therapeutic target for the treatment of degenerative joint diseases such as osteoarthritis. The primary effort is devoted to the development of non-zinc chelating exosite type inhibitors. The authors have previously identified exosites in hypervariable loops that are required for or proteolysis of both aggrecan and versican. Targeting these sites with the hope of selectivity is certainly a good approach. The authors used the glycosaminoglycan (GAG) feature of substrates to build in exosite affinity. To this end the authors probed ADAMTS-5 with a small library of GAG-mimetic glycoconjugated arylsulfonamides.

With some minimal SAR, the authors were able to achieve some selectivity of ADAMTS-5 over ADAMTS-4 and some increase in potency over other inhibitors they have developed. They report IC50 values with the most potent (molecule 4b) at 9.4±2.8 µM. Some further SAR to more fully understand exosite binding (4b did not inhibit a peptide cleavage assay) did not lead to a more potent inhibitor. Further characterization of 4b inhibitory activity was carried out looking at synergism with a known zinc chelating inhibitor and some molecular docking studies. The docking studies led to experiments mutating residues that were thought to involve inhibitor binding. The results largely supported the in silico predictions.

Overall the reported results advance the idea that selective inhibitors of ADAMTS enzyme that are not dependent on zinc coordination are possible; however, in the absence of more detailed studies of inhibition in cells and potentially in animals it is not possible to say how important and influential molecules such as those described here will be on sorting out complicated in vivo physiology. The potency reported for 4b suggests significant optimization would be needed before in vivo significance could be assessed.

Reviewer #1:

This study pursues the development of ADAMTS-5 protease inhibitors by screening compounds linking a glycan (GlcNAc) with an arylsulfonamide, using click chemistry as the tether contains a triazene. ADAMTS-5 is a metalloprotease that has been implicated as a drug target for osteoarthritis. In prior work, this lab has identified exosites in ADAMTS-5 that can contribute to substrate recognition and processing. Here they identify a hybrid compound, 4b, that can block the protease activity of ADAMTS-5 with 9 µM potency. Using docking, they implicate several Lys residues that might confer interaction and show that potency of 4b is reduced with ADAMTS-5 mutants. Overall, compound 4b may bind as predicted although no additional experimental structural studies are performed to validate binding mode. While the study is a solid but limited medicinal chemistry effort, it is not felt that this manuscript will be of broad interest.

-The compound 4b potency is still rather weak relative to other previously published agents which show sub-µM potency. 1) Biochem J paper (2016) from this lab and BBRC (2016) from a Japanese lab reported antibodies that blocked ADAMTS-5 in the low nM range and worked in human chondrocytes. 2) Thiazolidine-diones (sub µM) were reported as cell active ADAMTS-5 inhibitors (Eur J Med Chem 2014). 3) Acylthio-semicarbazides are sub-µM ADAMTS-5 inhibitors (Eur J Med Chem 2013) although also target ADAMTS-4 more weakly, and showed selectivity against other metallohydrolases.

-Compound 4b was not used in a cell-based let alone animal model to analyze its pharmacological effects or promise. It is thus not clear how compound 4b stacks up to earlier agents. Compound 4b is a rather large compound for advancing clinically.

-No new insight into ADAMTS-5 biological function was gained here.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Note: This rebuttal was posted by the corresponding author to Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

INITIAL RESPONSE TO REVIEWERS / REVISION PLAN

We are grateful to the three reviewers for reviewing our manuscript and providing their comments which helped to improve further the quality of the current study. We attach an initial revised version of the manuscript with changes corresponding to reviewers’ comments being highlighted. We now provide:

• 18 new main figure panels (Fig.1E, Figs.2D-F, Figs.3E-F, Figs.4B,C,E, Figs.6B-F, Figs.7B,D,E,F),
• 9 new supplementary figures, and
• 13 new supplementary tables, that correspond to the points raised by the reviewers. In this initial response to reviewers and revision plan we have already performed the bioinformatics analysis and the majority of new wet lab experiments requested by the reviewers, while we are still awaiting only for the results of three sets of wet lab experiments (RIP-seq, additional protein/RT-qPCR confirmations and B2 incubations with other proteins), which, due to their nature, take longer. We have also revised the main text accordingly with only a number of updates (regarding some methods of experiments currently in progress and the respective discussion) still missing.

In detail:

REVIEWER 1

Reviewer #1 (Evidence, reproducibility and clarity (Required)):

B2 RNAs, encoded from SINE B2 elements has been directly implicated in stress response by its inherent ability to bind RNA Pol II and suppress stress response genes (SRG) in homeostatic conditions. However, upon stimuli, B2 RNAs are cleaved and degraded, resulting in the release of RNA pol II and upregulation of SRGs. Previous work from the senior author identified PRC2 component EZH2 to be the B2 RNA processing factor, cleaving B2, and releasing POL2. SRGs are upregulated upon stress, for example in age-associated neuropathologies like Alzheimer's disease (AD). Considering that the hippocampus is a primary target of amyloid pathologies as well as since SRGs are suggested to be key for the function of a healthy hippocampus, the authors set to understand the role of B2 RNAs that are linked to SRG regulation in the mouse hippocampus with amyloid pathology. They use disease-relevant in vivo and in vitro models combined with unbiased RNA seq data analysis for this endeavor, which indicates the potential relevance of B2 RNAs in APP mediated neuronal pathologies in mice as well as identifies Hsf1 as the factor cleaving B2 RNAs in the hippocampus.

This reviewer generally remarks that “The work is interesting and identification of Hsf1 as the processing factor for B2 RNAs in the hippocampus is significant. I would like to credit the authors for their elegant in vivo experimental design in Figure 2.”

We appreciate the encouraging comments made by this reviewer.

General comment: The reviewer finds “some of the conclusions to be overstated” and has brought a number of concerns to our attention. Indeed, we agree that provision of additional data and details is needed to avoid any confusion about the gene pathways to which our findings apply. In the initial manuscript, (Figures 2 D, F and 6 D, F), we presented the gene expression levels of all B2 RNA regulated SRGs identified in our previous study (Zovoilis et al, Cell 2016), referred as B2 RNA regulated SRGs or B2-SRGs throughout the manuscript. To this end, we performed the respective statistical tests between the different conditions considering these genes, in order to show the transcription dynamics of these genes in either amyloid beta pathology (APP mice /Figs. 2D, F) or amyloid beta toxicity (HT22 cells / Figs. 6D, F). Since we were not looking for new candidate genes upregulated in APP mice or in our HT22 cell culture system, we did not narrow our analysis only to genes delivered by a general-purpose differential gene expression approach such as DESeq but tested all B2-SRGs. However, based on the reviewer’s comments below, we realize that the paper would benefit by presenting in the main figures only those B2 RNA regulated SRGs that overlap with differentially expressed genes identified by DEseq in each experimental system. This will help to avoid confusion and any misunderstanding that all B2 RNA regulated genes are equally affected in our system, which is not the case and would be an overstatement. We are now presenting in new Figure 2 (2E, 2F) only those B2-SRGs that overlap with upregulated genes identified by DESeq in 6m old APP mice (listed in new Suppl. Table 5) and in new Figure 7 (7D, F) we are now presenting only those B2-SRGs that overlap with upregulated genes identified by DESeq in HT22 cells treated with amyloid beta (listed in new Suppl. Table 11). The conclusions drawn by the new figures remain the same as with the old ones and we believe that this new way of presentation of this data will prevent confusion and potential over-statements. We thank the reviewer for bringing this to our attention. Based also on this reviewer’s minor point 3, we recommend that the old figures that included all B2-SRGs (and not only the differentially expressed ones identified by DESeq) are moved to the Supplement as new Supplementary Figures 1 and 7, respectively, so that readers can still get a view of all the data and the transcription dynamics of all B2-SRGs, while we provide both in text and the supplement an explanation about the value as well as limitations of these figures.

**Major comments:**

Major point 1. The reviewer asks: “In figure 1, the authors indicate a strong connection between B2 RNA regulated SRGs and learning and memory. In figure 2, they identify the SRGs in the hippocampus, please provide a direct comparison of learning and memory associated SRGs and the SRGs they identify in figure 2 that are significantly upregulated in APP mice in 6 months.”

In the revised version of the manuscript we now provide: i) As a new figure panel (lower panel in new Fig.1E), the number of B2 RNA regulated SRGs that are associated with learning based on our Peleg et al, Science 2010 paper and as a new Supplementary Table 3, the exact list of these genes. ii) As a new Supplementary Table 4, the list of all genes that are significantly upregulated in APP mice (6 months). iii) As a new Supplementary Table 5, the list of those genes upregulated in amyloid pathology (APP 6 months) that are B2-SRGs (expression levels of these genes are presented in new Figure 2E,F). Per reviewer’s question, we now provide as a new Supplementary Table 6, the list of B2 RNA regulated SRGs that are both learning associated genes and upregulated in 6 month old APP mice. In the text (first two sections of the results), we provide direct comparisons of the number of genes in each category and their overlap.

Major point 2. The reviewer asks: “To better understand the data in the context of hippocampal function, please include functional annotation of SRGs they identified in Figure 2F as they do it in Figure 1 (desirably for each time point, at least for 6M). How many of the SRGs they identify in Figure 1 are part of Figure 2F? Please include functional annotation of significantly upregulated B2 regulated SRGs in Fig2 and compare them with that of Figure 1.”

The number of B2 RNA regulated SRGs in Figure 1 that are part of Figure 2 (in particular Figs.2E,F) is now presented in the new Supplementary Table 5 and also in the text. We now provide as a new Supplementary Table 7 the functional annotation of these genes (see also general comment for this reviewer) and discuss the findings in the text.

We recommend to include only the 6M old mice as this is the time point in which B2 RNA processing was found to differ between WT and APP mice. However, if the reviewer thinks that this is necessary we will add also differential expression lists of other ages as additional supplementary tables.

Major point 3. The reviewer asks: “In figure 3, the authors report that the B2 processing rates are high at the 6M time point at in hippocampi of the APP mice. Please include the levels of unprocessed and processed B2 RNAs in these samples along with this figure, without which it is difficult to gauge the significance of its correlation with SRGs in Figure 2.”

We now provide as new figure panels 3E and 3F the levels of processed B2 RNA fragments and unprocessed (full length) B2 RNAs in these samples, respectively, along with the processing ratio which is now labeled as subfigure 3G.

Major point 4. The reviewer asks: “What is the % of B2 regulated SRGs that are hsf1 bound in Figure 4C? What is there dynamics in the wild type and APP hippocampi?”.

Old Figure 4C is now Figure 4A. The exact number of B2 RNA regulated SRGs that are close to Hsf1 binding sites is now presented as a new figure (Figure 4C) and discussed in the text. A list of these genes is provided as new Supplementary Table 8. For genes that are upregulated in APP mice compared to wild type, the difference in Hsf1 binding dynamics between B2 RNA regulated and not regulated genes is now presented as Suppl. Figure 4D.

Major point 5. The reviewer asks: “What is the distribution of Hsf1 binding sites on (a) non-B2 regulated SRGs and (b) non-SRG genes in hippocampi?”.

This point is related with point 4. We now present a new panel (Fig. 4B) for non B2 RNA regulated genes (listed in Suppl. Table 13) along with the distribution we have in the initial manuscript for all B2 RNA regulated SRGs (now presented as Fig. 4A). The direct comparison of these genes is presented in the new Suppl Figure 4C together with a similar comparison only for genes upregulated in APP mice (Suppl. Fig.4D)

Major point 6. The reviewer notes: “In Figure 4D, the 3months old Wt HSF1 levels are high, yet B2 processing (Figure 3E) is low. Please comment.”

The reviewer’s comment made us realize that we should include a plot that describes the correlation between Hsf1 levels and B2 RNA processing ration across all sequenced samples. This should reveal whether differences such as those observed by the reviewer affect our conclusion regarding the relationship between these two parameters. We now provide this in the new Supplementary Figure 6D, where we found a strong positive correlation between Hsf1 levels and B2 RNA processing ratio. We thank the reviewer for this comment which helped us to substantiate further this relationship.

Major point 7. The reviewer notes: While the authors show in vitro cleavage of B2 RNA by Hsf1, the experiment lacks controls to be conclusive. At least, please include a similar size protein as HSF1 with no-known RNA binding activity and a similar size protein with RNA binding activity as controls in 5A. Please justify the use of PNK as the control protein. Please include the use domain-based deletions of Hsf1 to map the region of HSF1 that is binding and potentially cleaving the B2 RNA. Please include an RNA of similar size and Antisense-B2 RNA to show the specificity of the Hsf1 based cleavage of B2 RNA. Without these controls, the conclusions in Figure 5 cannot be substantiated.

The endogenous ribozyme activity of B2 RNA compared to other control RNAs has already been shown in two previous works but we will also include the relative controls here by providing control incubations with other RNAs. We will also include the incubations with additional control proteins as suggested by the reviewer. We are currently performing these experiments and will include them in the revised version. PNK is used as a control protein because it is an RNA binding protein that is used in the construction of our short RNA libraries and we wanted show that short RNA seq data are free of such confounding factors that could potentially generate artificial fragments. We now include this information in the text.

We feel that the application of domain based deletions for Hsf1, while it would add additional information on the exact biochemistry underlying B2 RNA processing though Hsf1, is beyond the scope of this manuscript. In the current manuscript we are just focusing on the fact that Hsf1 can accelerate B2 RNA processing in vitro and not on the mechanism how this happens. This should be addressed in our opinion on a separate manuscript.

Major point 8. The reviewer asks: “The authors should show that the incubated APP peptides are taken up by the cells (experiments in Figure 5F and Figure 6).” These figures are now labelled as Fig.6C and Figure 7, respectively. That’s a very interesting point and we thank the reviewer for this comment. Multiple studies have shown that toxicity after incubation by amyloid beta is mediated mainly by cell surface receptors, which through cell signalling leads to the response to cellular toxicity that induces stress genes such as Hsf1. Nevertheless, APP peptides may enter the cell, and the reviewer’s questions raised the possibility that oligomers entering the cell could have a direct impact on the stability of the B2 RNA. In that case, providing evidence that the amyloid enters the cell would be important if we had indications that amyloid beta interacts directly with B2 RNA. We did test this and we found no direct effect of amyloid beta on B2 RNA, so the processing in our case is not induced by oligomers that may have entered the cell. We were planning to present this information in a different manuscript, but if the reviewer or editor thinks that it would be beneficial for the paper, we could present this as supplement figure that shows that amyloid beta incubations with B2 RNA do not induce further processing beyond what Hsf1 causes. For the moment we just present this below:

Major point 9. The reviewer asks: “Please provide the list, functional annotation, and % of the SRGs upregulated upon incubation with APP in HT22 cells in comparison to 6month old APP mice. Comment on learning-related Genes.”

In the revised version, we now provide and mention in the text the following data: i) a list of genes upregulated in HT22 cells during amyloid toxicity upon incubation with amyloid beta (new Suppl. Table 9), ii) a list of genes according to point (i) that are common with genes upregulated in APP mice (new Suppl. Table 10), iii) the list and number of B2-SRGs that are upregulated in HT22 cells during amyloid toxicity (the reviewer’s question) (new Suppl. Table 10). We mention in the text the gene numbers and also the genes that are common in all three lists. iv) Functional annotation of genes of point (iii) (new Suppl. Table 12),

We also mention in the text the limitations of our comparisons between the in vivo model of amyloid pathology (APP mice) and the in vitro cell culture model of amyloid toxicity (HT 22 cells) and we clarify that the cell culture model is used just as a simulation of the effect of amyloid beta in gene pathways associated with response to cellular stress and the role of Hsf1 on B2 RNA processing.

Major point 10. The reviewer asks: “The authors should show the efficient downregulation of Hsf1 (protein) upon anti-Hsf1 LNA transfection.”

In the revised version, in addition to the RNA-seq data we provide a second confirmation at the mRNA level with an independent method (RT-qPCR) in new figures 4E and 7B (lower panel). We are currently performing the protein extractions and will provide a WB or an Elisa in the revised version.

Major point 11. The reviewer asks: “Please present the total B2 RNA levels for conditions in Figure 6C.”

We now provide as new supplementary figure (Suppl. Fig. 6B and C) the levels of processed B2 RNA fragments and the total levels of unprocessed full length B2 RNAs of these samples that relate to old Figure 6C (now labeled as Fig.7C)

Major point 12. The reviewer notes: “Hsf1 levels are not significantly downregulated in Control cells which were inoculated with the reverse APP peptide. Please comment.”

We assume that the reviewer here refers to the lack of reduction in Hsf1 levels in the cells inoculated with the reverse peptide and the anti-Hsf1 LNA. Indeed, this lack of reduction is confirmed also by the new qPCR we performed (new Figure 7B, lower panel, R-ctrl vs R-anti-Hsf1). This should likely be attributed to compensation during non-stress conditions. In contrast, under stress conditions, Hsf1 is heavily used in stress response, which could explain the differences we see as cellular needs surpass the available Hsf1 transcripts due to degradation by the LNA. This is also supported by the new RT-qPCR experiments we have performed for B2-SRGs (new Figure 7E). In agreement with what is known for stress response genes such as immediately early genes (for example FosB), levels of these genes are minimal in both R-ctrl and R-anti-Hsf1 conditions and only become activated during stress response. We now discuss this in the text of the revised manuscript.

Major point 13. The reviewer asks: “Please compare and contrast the % of genes, the overlap, and the functional distinctions in 6F to that of 5G and Figure1. What are the genes that are common between Figure1, and that are specifically upregulated upon Anti-Hsf1 LNA transfection along with 1-42 APP. What is % of the occurrence of B2 binding sites in those genes? What are their functional annotations and what is their connection to learning, memory, and cell survival?”

Old Figure 6F is now Figure 7F, while old Figure 5G is now Figure 6C. This point is discussed in the response to points 1 and 9 of this reviewer. In summary, genes upregulated in our amyloid toxicity model included 25 B2-SRGs (new Suppl. Table 11). When testing for enriched terms in these 25 genes, biological processes related with apoptosis, such as regulation of apoptotic process and programmed cell death were at the top of the list (new Suppl. Table 12) and included, among others, genes such as FosB and Mitf that have been connected with Alzheimer’s disease. Out of the 25 genes that are up-regulated in both mice and our cell culture system, six are B2-SRGs (4932438A13Rik, Fosb, Pag1, Ptprs, Sema5a, and Sgms1) and include a well-known immediate early gene (Fosb), genes associated with sensitivity to amyloid toxicity (Pag1, Sema5a, Sgms1, Fosb), as well as genes associated with p53 (Ptprs, Fosb). All these genes get upregulated in amyloid toxicity (42-Ctrl vs R-Ctrl) but are not upregulated when Hsf1 LNA is applied (42-anti-Hsf1 vs R-anti-Hsf1, no significant difference). This information is now included in the text.

**Minor.**

1 . Please include TPM/ FPKM values for hippocampal markers as control in Figure 2 to do justice to the hippocampus specific RNA seq conducted by the Authors.

To our understanding, the reviewer here suggests the testing of well-known hippocampal markers in our mouse data as controls to confirm that they are indeed hippocampus specific. We have selected as reference markers, the genes employed by the Allen Brain Atlas RNA-sequencing project and we provide a comparison of their data in hippocampal cells with our data from mouse hippocampus. This is now presented as new Supplementary Figure 2.

2 . In figure 2D the authors show that B2 RNA regulated SRGs in the 3 months' wild type mice are significantly high. P53 has been reported to be high in young wild types hippocampus, but not SRGs in my opinion. The authors should comment on this.

Old Figure 2D is now Figure 2E. We now mention the reviewer’s comment particularly in the discussion and cite a landmark review article in Neuron journal by Michael Greenberg regarding the role of stress response genes, such as FosB, early during development. As to prevent any confusion, we have also replaced SRGs with B2-SRGs since we tested only B2-SRGS in our study.

3 . In figure 2F, under the 6m APP condition, the replicate 3 looks substantially different from the other replicate. This can significantly impact the analysis and conclusions made. Either remove that replicate and present the analysis without it or please provide a valid explanation. To make the data more valid, please provide hierarchical clustering of the entire data, the non-B2 regulated genes and the B2 regulated SRGs.

We now provide in the new Supplementary Figure 9C a PCA plot, which includes 6m APP mice vs. their WT counterparts and HT22 cells, and shows that this variability is within the biological replicate variability we can expect in these models. To substantiate this further, we have constructed the correlation matrix of the RNA-seq data of both WT and APP 6 month old mice in the new Supplementary Figure 9D. As shown in this matrix, all APP mice clearly correlate with each other and not with their WT counterparts.

In the initial manuscript the heatmaps of former Figure 2 were indeed provided with hierarchical clustering of the entire data and also included non-B2 RNA regulated genes. This data is included now as Supplementary figure 2.

In Figure 2C RNA seq data is represented in TPM while its FPKM in Figure 2D.

Figure 2D is now Figure 2E, while Figure 2C remains labelled with the same number. Given that TPM already includes scaling of the data, it is unsuitable for the averaging of the gene expression levels of multiple genes (B2-SRGs) used in the boxplots of Figure 2. This does not apply in the case of single genes as in Fig 2C (p53) or in the heatmap where each gene is presented in a separate row. This explanation is now included in the methods section.

Figure 2: the number of replicates in the case of 3-month-old wild types only 2. Please specifically denote it and comment why only 2 replicates are provided.

During the hippocampal RNA extractions, the RNA of one of the three 3m old mice had very low RIN scores, which could be a confounding factor for the short-RNA-seq. As this happened some months after the hippocampal extractions, we did not have any other 3 month mice of the same cohort used for the behavioral and IHC studies. Thus, we decided to include only two replicates in this condition. Since the results presented in the current study focus mainly on 6 month old mice, we expect the impact to be minimal. We include this note in the methods section.

4 . Considering that p53 and SRGs are significantly upregulated in 6months in the APP model, it would be great if (allowing that these samples are still available) the authors can include a staining for apoptotic markers, for example, Active Casp3 or similar. This will allow us to better gauge the gene expression changes presented by the authors especially regarding SRGs.

Unfortunately, we do not have these slides but in the revised version we will provide qPCR data for some of these markers.

5 . Under subheading: Hsf1 accelerates B2 RNA processing, 3rd paragraph when the authors comment on known hsf1 binding sites on SRG genes, please correct from: Increased Hsf1-binding was found.... "To the increased number of hsf1 binding sites were found", unless the authors would like to show increased Hsf1 binding by performing CHIP-seq for Hsf1 in the hippocampus at least at the 6-month time point between Wt and APP mice.

We have changed the text accordingly.

Reviewer #1 (Significance (Required)):

B2 RNAs, encoded from SINE B2 elements has been directly implicated in stress response by its inherent ability to bind RNA Pol II and suppress stress response genes (SRG) in homeostatic conditions. However, upon stimuli, B2 RNAs are cleaved and degraded, resulting in the release of RNA pol II and upregulation of SRGs. Previous work from the senior author identified PRC2 component EZH2 to be the B2 RNA processing factor, cleaving B2, and releasing POL2. SRGs are upregulated upon stress, for example in age-associated neuropathologies like Alzheimer's disease (AD). Considering that the hippocampus is a primary target of amyloid pathologies as well as since SRGs are suggested to be key for the function of a healthy hippocampus, the authors set to understand the role of B2 RNAs that are linked to SRG regulation in the mouse hippocampus with amyloid pathology. They use disease-relevant in vivo and in vitro models combined with unbiased RNA seq data analysis for this endeavor, which indicates the potential relevance of B2 RNAs in APP mediated neuronal pathologies in mice as well as identifies Hsf1 as the factor cleaving B2 RNAs in the hippocampus.

The work is interesting and identification of Hsf1 as the processing factor for B2 RNAs in the hippocampus is significant. I would like to credit the authors for their elegant in vivo experimental design in Figure 2.

REVIEWER 2

Reviewer #2 (Evidence, reproducibility and clarity (Required)):

**Summary:**

This manuscript follows from previous work by the corresponding author showing that SINE-encoded B2 RNAs function as regulators of the expression of stress response genes (SRGs). Specifically, stimulus triggers the processing of repressive B2 RNAs that are bound at the SRGs, thereby activating SRG transcription. In this work, the authors investigate whether a similar mechanism might be controlling the expression of genes in models of amyloid beta neuropathology (i.e. mouse hippocampi from an amyloid precursor protein knock-in mouse model, and a cell culture model of amyloid beta toxicity). They performed RNA-seq in these models. Their data show a correlation between the progression of amyloid pathology, expression of genes thought to be regulated by B2 RNA, and the processing of B2 RNA. In addition, they show biochemical data supporting a role for Hsf1 in enhancing the processing of B2 RNA. Knockdown of Hsf1 also reduced B2 RNA processing and the expression of SRGs.

**Major comments:**

Major point 1. The reviewer asks: “In the RNA-seq data one cannot distinguish between Pol III transcribed B2 RNA and Pol II transcribed B2 RNA (typically embedded within introns and UTRs of mRNAs). The models they present, and the structures they show, clearly imply regulation by Pol III transcribed B2 RNA. However, there is no way to know that the short B2 RNAs they sequence aren't coming from degraded mRNAs. This needs to addressed. Minimally, in writing as a caveat of their model. Ideally, it would be addressed experimentally.”

That’s a very interesting point, as it implies that the regulatory role of B2 RNAs may extend from PolIII transcribed B2 RNAs into B2 RNAs embedded into mRNAs (likely nascent ones) that may be also under the same endogenous ribozyme activity of this sequence, suppress PolII and are processed in response to stimuli. The RNA RIN values of our samples were pretty high except one 3m old mouse sample which was for this reason excluded from further analysis. Moreover, during the library construction shorter and longer RNAs have been separated. Thus, any generation of B2 RNA fragment that may have originated from mRNA should be biologically but not technically related and must have happened in the cell before our RNA extraction. To address this point, we now provide a new supplementary figure (Suppl. Figure 8), where we have separated the B2 elements against which we map the RNA fragments into two categories, those that fall within exonic/genic regions and those outside of these regions. Although B2 RNAs are produced by multiple copies in the genome, each copy does harbor multiple SNPs, insertions and deletions, which means that each B2 RNA fragment is mapped to a specific set of B2 elements and not to all of them. In other words, despite multiple mapping a level of spatial specificity is maintained. If the B2 RNAs we map were coming exclusively from either only Pol III B2 elements or mRNA embedded B2 elements, we would expect at least some difference in the distribution of fragments between B2 elements of these two categories, as the second one overlaps with mRNAs. As shown in the new supplementary figure 8, the fact that distribution models are very similar between the two categories indeed supports the hypothesis that both types of B2 elements may contribute to B2 RNA processing. Most importantly, the profile of B2 RNAs in genic regions shows that B2 RNA processing is not random but follows the same processing rules as B2 RNAs from Pol III promoters. Given the limitations posed by the repetitive nature of B2 RNAs, it remains difficult though to provide an exact number regarding the portion of B2 RNA fragments produced by each category and this is clearly noted in our revised discussion part. However, even the indication that B2 RNAs embedded in mRNAs may also play an important role in our model provides a new perspective that should be investigated further in future studies.

Major point 2. The reviewer asks: “The direct regulation of SRGs by B2 RNA was not shown in their model systems for amyloid beta neuropathology. Rather, the authors' used the genes identified in their prior studies as B2 RNA-regulated, which I believe were in the NIH3T3 cell line. Given that transcription is highly cell-type specific, these genes might not be regulated by B2 RNA in mouse hippocampi or their cell culture model, despite the correlations shown. This needs to be addressed. Ideally, a targeted approach to show that transcription of even a couple genes in their system is indeed regulated by B2 RNA would provide stronger support for their conclusions.”

We agree with the reviewer and we now provide a new figure (Fig.6D-F) with the targeted approach that this reviewer proposed. In particular, we have tested whether fragmentation of full length B2 RNAs is in connection with activation of target genes also in our biological system (HT22 cells) as it did in NIH/3T3 cells in our Cell paper. We now show in new Figure 6 that this is indeed the case.

Major point 3. The reviewer proposes a number of additional information that needs to be provided: “The following bioinformatics analyses would strengthen their conclusions. This should be straightforward to do because it involves data they already have, and perhaps analyses they have already have performed.”

a. Regarding the plot in Figure 3A (lower panel). The same plot should be shown for the 3m old and the 12m old APP mice (i.e. not just the 6m data). This would show the specificity of processing B2 RNA and that it indeed correlates with disease progression.

We now provide this plot as new supplementary figure (Suppl. Figure 3). It shows that increased B2 RNA processing coincides only with the active neurodegeneration phase at 6 months and not the terminal stage.

b. Regarding the plots of B2 RNA processing rate. This value could increase either due to more short RNAs or less full length RNA. Which is it for the 3m, 6m, and 12m APP mice? Showing the short and long B2 RNAs as boxplots (as opposed to only the processing rate) would address this and also provide additional insight into the regulation involved. The same applies to the data in Figure 6. (As an aside... do the authors mean processing ratio as opposed to rate? I'm not clear where the time component is coming into play to call this a rate.)

Old Figure 6 is now Figure 7. We now provide all these figures that show that increase in processing ratio at 6 months is mainly due to increase in the processed fragments and not a decrease in full length B2 RNAs. For APP mice these are new Figures 3E and F, and for HT22 cells , these are new Supp. Figures 6B and C.

c. The random genes in Figures 2E and 6E are plotted as heat maps, but statistical significance is hard to see. What do boxplots of the random genes look like, and is the significant difference between 6m old APP and 6m old WT then lost?

Old Figure 2E is now new Suppl. Figure 1C, while old Figure 6E is now new Suppl. Figure 7C. We now provide these boxplots in new supplementary figures 1B and 7B.

Major point 4. The reviewer comments: “ It is interesting that B2 RNA self-processing is enhanced by both Ezh2 and also Hsf1. It would strengthen the data to perform a control with a protein prepared more similarly to the Hsf1 (rather than PNK) to confirm that the enhanced B2 RNA breakdown is indeed attributable to Hsf1 and not a contaminant in the protein prep. Similarly, the authors should provide information on which RNA was added as the negative control for Hsf1-stimulated breakdown (i.e. the ~80 nt RNA).”

This point is also discussed in Reviewer 1 point 7. The ribozyme endogenous activity of B2 RNA has been shown already in two previous studies that performed incubations with control RNAs and proteins. We are currently preparing and will provide these additional incubations as anew supplementary figure in the revised manuscript.

**Minor comments:**

1 . Regarding the GO analyses in Figure 1 (panels B, C, and D). I wasn't clear whether the authors are showing all statistically enriched terms, or only those relevant to neuronal processes and learning. I recommend showing a supplemental table with all terms that have an adjusted p value below a specified cut-off (e.g. 0.05).

The statistical threshold used was an EASE score of 0.05 and all presented terms were above this threshold. In the initial manuscript we filtered only the top 5 terms in tissue enrichment and the top 10 terms for GO Biol process and Cell Compartment that had passed the threshold. We now provide all the terms that passed the threshold as a new Supplementary Table 2, including gene counts, exact gene numbers and related statistics.

2 . The authors show several figures that are not new data (2B, 4A, 4B, Suppl. Fig 1 and 2). I think it would be more clear if these data were summarized and referenced in the results, rather than shown.

Old Suppl. Fig1 and 2 that were results of previous studies or web resources directly available (such as Human Protein Atlas) have been now removed and they are now just referenced in the text. Old Figures 4A and 4B have been removed from the main figures but may be helpful to the readers if they are still available in the Supplement (currently as Suppl. Figure 4A and B), as not all users are familiar with the RNA-seq browsing tools of Allen Brain Atlas resources. Regarding figure 2B that contains data from our previous study on this exact cohort of mice: If the reviewer and the editor agree we recommend that it remains in the main figure (with the appropriate image credit citations), as it provides in an efficient way the clear connection between amyloid load and our results at the molecular level, and, most importantly, it clearly draws a line in amyloid pathology progression between 3m old and 6m old, that agrees with our findings in the RNA-seq data of these mice.

3 . In Figure 3A the schematic shows that B2 is 155 nt, the plots in Figures 3A,B,C show B2 RNA is 120 nt, and Figure 5 shows the RNA is 188 nt. Can the authors please clarify these differences?

The full length of B2 consensus sequence is 188nt and this is the one we use for the in vitro experiments. However, the structure of the B2 RNA has been resolved only for the first 155nt by the Kugel lab, and this is the only publicly available structure that we can reference in our figures. For the mapping of 5’ends of short fragments in Fig.3A we have used the same range tested in our Cell paper to maintain consistency of the results. The reason why this 120nt threshold was selected in the Cell paper was to exclude artifacts from short RNAs mapping partially in our metagene as well as downstream of those B2 elements that are shorter from the consensus sequence. We now explain in methods section these differences.

4 . In the Methods section, the sequence of the g block template didn't contain the T7 promoter sequence that was used as the forward primer for PCR amplification?

We have now included this sequence in lower case.

5 . In Figure 6B, why were Hsf1 levels not decreased in the R treated cells after treatment with the LNA?

Old Figure 6B is now new Figure 7B. Please see response to Reviewer 1, major point 12.

Reviewer #2 (Significance (Required)):

Finally, this reviewer generally remarks that “The models presented for the regulation of stress response genes (SRGs) in amyloid beta neuropathologies are compelling. As are the correlations they found between the progression of amyloid pathology, expression of genes thought to be regulated by B2 RNA, and the processing of B2 RNA. This is a unique direction of research for brain disease and represents an interesting conceptual advance. Most prior studies in this area use common model cell lines, and this lab seems well-positioned to unravel the proposed molecular mechanisms in neuronal systems.”

We appreciate the encouraging comments made by this reviewer.

REVIEWER 3

Reviewer #3 (Evidence, reproducibility and clarity (Required)):

This manuscript describes a regulatory mechanism involving Hsf1 and B2 RNAs in the control of stress response genes (SRGs) during amyloid induced toxicity. In particular Hsf1, upregulated in 6m old APP mice and in HT22 cells treated with beta amyloid peptides, is shown to stimulate the B2 RNA destabilization leading to SRGs activation. While in healthy cells this upregulation can be reverted once the stimulus is removed, the pathological condition fuels the circuitry leading to p53 upregulation and neuronal cell death. The authors previously described the same mechanism acting during cellular heath shock response but in this case the protein identified as trigger of B2 RNA destabilization and SRGs activation was EZH2 (Zovoilis et al, 2016).

This reviewer generally remarks that “Indeed, the first part of the manuscript describes additional analyses of the previous data that prompts further investigation on the potential role of B2 RNA in AD condition. Nevertheless, it is not clear how the prior findings obtained in not biologically related cellular models might be used to obtain helpful indication of B2 RNA neuronal activity.”

We thank the reviewer for this comment. Indeed, the current study’s main aim was to expand the findings of our previous work on the role of B2 RNA in cellular response to thermal stress in NIH/3T3 cells to other types of cellular response to stress, in our case to amyloid toxicity and the resulting amyloid pathology in neural cells. Response to thermal stress (Heat Shock) has been used for years as a basic study model for cellular response to stress. Proteins and gene pathways initially identified in heat shock have been subsequently shown to play identical pro-survival roles in other biological systems and there are studies showing the role of Hsf1, heat shock related proteins and cell stress response pathways in neural cells and the mammalian brain (we will provide these references in the revised version). For example, pathways such as the MAPK pathway and early response genes, that constitute the basis of response to heat shock, have been shown in studies by us and others to be activated and play a critical role in hippocampal function. Thus, examining the role of B2 RNA in the context of neural response to stress constituted a natural continuation of our previous study in NIH/3T3 cells. The fact that the list of B2 RNA regulated SRGs was found to be highly enriched in neuronal tissue terms and cellular compartments related to neuronal functions plainly confirms the close relationship among cellular response pathways in the two biological systems. Due to these facts we were compelled to investigate in more detail our previous findings also in a neural cell model. However, as discussed in point 2 of Reviewer 2, the initial manuscript did not confirm the direct control of B2 RNA on expression of target genes also in our cellular model. This information is now part of the new figure 6 and we thank both reviewers for bringing this to our attention.

The reviewer also remarks that “The research fields of non coding RNAs and neurodegeneration are attractive and challenging and, in my opinion, the molecular circuitry involving B2 RNAs might add important insights for understanding beta amyloid toxicity and neuronal death; however, the data provided are not in the shape making the manuscript suitable for publication: some controls are missing, the way the experiments are presented is not easy to follow and more importantly the authors does not provide any data (tables or lists) of the NGS experiments and the study lacks validation of them. Therefore, in my opinion the manuscript needs a profound revision before to be considered for publication in Review Commons.”

Based on this reviewer’s and the other reviewers’ suggestions we now provide additional controls, detailed tables and gene lists, and qPCR validation of these results. We have also substantially revised the text in the first section of the results and beginning of the discussion, to make our rational for testing B2-SRGs more clear and easier to follow.

**major concerns:**

Major point 1. The reviewer asks: “The first paragraph of the Results is entirely dedicated to re-analyze the data previously published by the same group (Zovoilis et al., 2016). However, this is not adequately explained. In line with this, the table 1 is not required since the data are already provided by Zovoilis et al., 2016, unless the authors handled the data using additional new criteria that have to be explained.”

We now explain our rational for using this data in more detail in the text. Please see also response to the general comment of this reviewer and response to the next point.

In the Zovoilis et al (2016) study, the data presented did not include the list of regulated genes in a direct way but as part of the annotation of the B2 CHART peaks. This may pose difficulty to non-experts to extract the gene list from that data and we thought to include them as separate gene list here so that readers can directly use it for their analysis. Nevertheless, if the reviewer or the editor think that the list is redundant, we can surely omit it.

In addition, the reviewer comments: “Moreover, Zovoilis and colleagues (2016) focused on SRGs regulated upon heat shock and using NIH/3T3 and HeLa cell lines, therefore, it is difficult to me understand how, searching for "cellular function connected with B2 RNA regulated SRGs", the list resulted enriched of neuronal tissue terms or cellular compartments related to neuronal functions. Please clarify this point since the following analyses are based on these findings.”

Neural pathologies, such as amyloid pathology in brain, are often connected with cellular stress due to proteotoxicity. The ability of neural cells to respond to proteotoxicity challenges is connected with various molecular mechanisms, including stress related proteins that were firstly described in the context of heat shock. Thus, both contexts (heat shock and amyloid toxicity) refer to cellular response to stress, which explains why genes identified to be regulated during stress response in NIH/3T3 cells constitute part of the basic stress response toolbox that neural cells have also been described to possess. We have now modified the text accordingly to make our rational more clear.

Major point 2. The reviewer comments: “In Figure 1F there is no arrow indicating that some of the SRGs regulate directly miR-34 as stated in the main text. Moreover, it is more appropriate to replace SRGs with learning‐associated genes both in the figure and in text (2nd paragraph of the results) since Zovoilis and colleagues focused on them. Finally, they did not show in their manuscript the rescue of p53 expression mediated by mir-34; indeed, for miR-34-p53 regulatory axis Zovoilis and colleagues referred to Peleg et al, 2010 and Yamakuchi & Lowenstein, 2009. Please fix all these concerns.”

We have restructured the figure as suggested by the reviewer and made clear the distinction between learning genes and B2 RNA regulated SRGs (B2-SRGs) from the two different studies. In connection with point 1 of Reviewer 1, we believe that new Figure 1E, that includes the exact number of B2-SRGs that are learning associated, will represent more efficiently and accurately the data. We have also corrected in the text the citation regarding miR-34c and p53 in both the introduction and first section of the results (last paragraph).

-The Fig.1A and Fig.1F are wrongly indicated at the end of the sentence "....levels of these genes are normally downregulated in 6m and 12m old mice compared to 3m old mice (p=0.02 and p=0.04, respectively)"; please correct this point.

The error has been corrected.

Major point 3. The reviewer comments regarding Figure 2:

a) Since three mice for each condition have been used for the RNA seq analyses, please provide a blot with the Principal Component Analysis (PCA).

Please see also response to minor point 3 of Reviewer 1. We provide the PCA plots for WT and APP mice in the new Supplementary Figure 9 and we also provide a comparison of the six month old mice with the HT cell samples as well as a correlation matrix for 6 month old mice in the same figure.

b) Fig 2F comes first of Fig 2E in the text, however, I suggest to move this latter to supplementary material.

Old figure 2E has now been moved to supplementary material as new Supplementary Figure 2C and we also provide in a boxplot the exact gene expression levels as new Supplementary Figure 2B.

c) In general, this study lacks validation of the RNA-seq results. Western blot and/or qRTR-PCR to verify the variation of p53 and of some selected SRGs have to be provided.

In the current revised version we already provide qPCRs for p53 and Hsf1 in APP mice and we will include additional genes in the final version.

d) It is also not clear how the authors defined SRGs in the hippocampus: do they correspond to learning‐associated genes described by in Zovoilis et al, 2011 or to B2 RNA H/S regulated genes by Zovoilis et al, 2016?

The way we presented B2 RNA SRGs in the results with regard to learning associated genes was indeed unclear. We now present the distinction between the two gene categories and their relationship as a new Fig.1E panel and we also provide detailed gene lists of common genes and the exact numbers (please see also response to Review 1, major point 1).

-APP 12 month old mice show the sever phenotype of the terminal AD-like pathology, however this does not correlate with significant SRGs and B2 processing increase. Can the author make a comment on this?

That’s a very important point and we thank the reviewer for raising this point. We now comment on this in the discussion part explaining how our findings are characteristic of the initial active neurodegeneration phase of amyloid pathology rather than more terminal stages.

Major point 4: The reviewer comments regarding Figure 5:

a) a gel with no-protein control for the time course of panel B was cited in the text but missing among the panels. Moreover, the time course shown in the graph in 5C does not correspond to the one in 5B.

Indeed, the no-protein control time line should refer only to panel C and not to B, we have now corrected the text. Nevertheless, we now present in the new Supplementary Fig. 5 the gels, based on which the graph in panel C was calculated, including also the gel with no protein timeline. The time course shown in the initial 5C had been mislabeled. It has now been corrected. We apologize for this and we thank the reviewer for bringing this to our attention.

b) 5G indicates that four samples for each condition have been analysed by RNA-seq, since they do not seem to be homogeneous please provide a PCA analysis together with the validation by qRT-PCR of a selected group of deregulated genes.

Old Figure 5G is new Figure 6C. PCA analysis for these samples is now provided in Supplementary Figure 9 and qPCR validation of a number of these genes is provided in new Fig. 7E.

Moreover, it is not clear whether all the genes shown in the heatmap or a number of them, as stated in the text, were found upregulated in 6m old APP mice. Please clarify this point and modify the figure and the text accordingly. A Venn diagram showing the overlap between genes upregulated in 42vsR treatment and those upregulated in 6m old APP mice might help the comprehension of the experiment.

Please see response to Reviewer 1, point 9. We now provide as new supplementary tables the exact overlapping lists and mention these numbers in the text.

Major point 5: The reviewer comments regarding Figure 6 (now labeled as Fig.7):

a) The evaluation of the levels of Hsf1 mRNA and protein upon LNA transfection is missing for both R and 42 treated HT22 cells. From TPM in panel B, Hsf1 downregulation seems to have been more effective in 42 than in R condition. This would mess up the interpretation of the data.

We now provide qPCR data for Hsf1 gene expression levels which confirm the ones from the RNAseq. The reason why Hsf1 downregulation seems not to affect the R condition is discussed in our response to Reviewer 1, major point 12, and the respective explanation is provided in the revised text.

b) Again, in this case any validation of the RNA seq data is provided (any B2 regulated SRGs).

Now, we provide qPCR data for these genes in Fig.7B and new Fig.7E

c) Panels E and F should be swapped or panel E moved to supplementary material.

Panel E is now moved to supplementary material as new Suppl. Figure 7C.

Major point 6. The reviewer comments: “In a previous paper the authors discovered B2 RNAs as a class of transcripts bound to EZH2 and this interaction leads to B2 RNA destabilization in heath shock (H/S) condition. The authors also conclude that the genes controlled by B2 RNAs may not overlap with the ones controlled by Hsf1 during H/S. The author should make a comment on this explaining why during H/S B2 RNAs work independently from Hsf1 and on different target SRGs while, during beta amyloid stress ,the two act together on the same SRGs. Moreover, as shown for EZH2, Hsf1-RIP experiment should be performed in order to confirm the direct involvement of Hsf1 in the SRGs-B2 destabilization.”

In the last two paragraphs of our discussion we indicate that B2 RNA regulation is a new process implicated in the response to stress in amyloid pathology but certainly not the only one. We have revised the text in this part accordingly in the revised version to prevent any confusion. We are currently performing a series of RIP-seq experiments with various antibodies. As, to our knowledge, there is no prior published study performing RIP-seq or CLIP-seq for any tissue using Hsf1 antibodies, the success of this experiment is not guaranteed and depends on the existence of appropriate antibodies.

Major point 7. The reviewer comments: “There is any table listing the results of the RNA seq experiments performed in this paper: control vs APP 3-6-12 m old mice and in R vs 42 treated HT22 cells in presence or absence of LNA against Hsf1. Please provide these data.”

We now provide these lists as new supplementary tables. Please see response to major points 1 and 9 of reviewer 1.

Major point 8. The reviewer comments: “In the discussion the authors claim that healthy cells are able to restore the expression of Hsf1, SRGs and B2 RNA upon removal of the stress. Since there are evidence for the rescue of SRGs and B2 RNA expression post H/S, no data are available for Hsf1, SRGs and B2 RNA upon the removal of 1-42 beta amyloid peptide. This might be a nice information to add to the manuscript.”

This would indeed substantiate further our results in our HT22 cell model. We have now performed this experiment, in which HT-22 cells were removed from the amyloid 42 (and the respective R peptide control) and left to recover for 12 hours before estimating through RT-qPCR the Hsf1 levels ( see graph below, REC corresponds to recovered HT-22 cells). Hsf1 levels in 42-REC have returned to the same levels as in R, p We currently perform the RT-qPCRs of these samples also for B2-SRGs and will include them in the final version as a supplementary figure.

**Minor criticisms:**

-In the introduction the reference Yamakuchi M and Lowenstein CJ, (2009) MiR‐34, SIRT1 and p53: the feedback loop. Cell Cycle, should be added in the sentence: "In contrast, hippocampi of mouse models of amyloid pathology and post- mortem brains of human patients of AD.....and neural death (Zovoilis et al., 2011)."

We have now changed the text at that point accordingly and also updated the legend of Figure 1F that also refers to this same study.

-Authors refer to Hernandez et al., 2020 to state that B2 self cleavage is stimulated by some proteins however, Hernandez and colleagues studied only the effect of EZH2 protein. Please rephrase the sentence accordingly.

Text has been modified accordingly.

-Indicate a reference for the sentence: "......Ezh2, was reported as being responsible for the B2 RNA accelerated destabilization and processing during response to stress."

The respective citation was added.

-The format of many references is not consistent and has to be revised.

We have switched to the Vancouver style. Some references in the legend and methods sections are referred independently from EndNote in case these text sections have to be moved to supplement in the final version in order to not create inconsistencies with endnote.

Reviewer #3 (Significance (Required)):

Finally, this reviewer generally remarks that “The research fields of non coding RNAs and neurodegeneration are attractive and challenging and, in my opinion, the molecular circuitry involving B2 RNAs might add important insights for understanding beta amyloid toxicity and neuronal death.

However, this manuscript does not really add technical advances since the authors employed experimental approaches and bioinformatic analyses previously published by Zovoilis and colleagues in 2011 and 2016.”

Our aim in the current manuscript was not to introduce a new method or experimental approach but rather to study the mechanisms behind B2 RNA regulation of gene expression in neural cells and particularly in amyloid pathology. Nevertheless, the current study constitutes the first reported short-RNA seq in this tissue and offers for the first time the ability to study B2 RNA processing in this tissue which is not possible with standard small and long RNA-seq.

The reported findings might of interest of an audience of experts in non coding RNAs and neurodegeneration. The area of my expertise almost regards the biology of non coding RNAs from biogenesis to function manly focusing on neuronal and muscular systems both in physiological and pathological conditions.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #3

Evidence, reproducibility and clarity

This manuscript describes a regulatory mechanism involving Hsf1 and B2 RNAs in the control of stress response genes (SRGs) during amyloid induced toxicity. In particular Hsf1, upregulated in 6m old APP mice and in HT22 cells treated with beta amyloid peptides, is shown to stimulate the B2 RNA destabilization leading to SRGs activation. While in healthy cells this upregulation can be reverted once the stimulus is removed, the pathological condition fuels the circuitry leading to p53 upregulation and neuronal cell death. The authors previously described the same mechanism acting during cellular heath shock response but in this case the protein identified as trigger of B2 RNA destabilization and SRGs activation was EZH2 (Zovoilis et al, 2016). Indeed, the first part of the manuscript describes additional analyses of the previous data that prompts further investigation on the potential role of B2 RNA in AD condition. Nevertheless, it is not clear how the prior findings obtained in not biologically related cellular models might be used to obtain helpful indication of B2 RNA neuronal activity. The research fields of non coding RNAs and neurodegeneration are attractive and challenging and, in my opinion, the molecular circuitry involving B2 RNAs might add important insights for understanding beta amyloid toxicity and neuronal death; however, the data provided are not in the shape making the manuscript suitable for publication: some controls are missing, the way the experiments are presented is not easy to follow and more importantly the authors does not provide any data (tables or lists) of the NGS experiments and the study lacks validation of them. Therefore, in my opinion the manuscript needs a profound revision before to be considered for publication in Review Commons.

major concerns:

-The first paragraph of the Results is entirely dedicated to re-analyze the data previously published by the same group (Zovoilis et al., 2016). However, this is not adequately explained. In line with this, the table 1 is not required since the data are already provided by Zovoilis et al., 2016, unless the authors handled the data using additional new criteria that have to be explained. Moreover, Zovoilis and colleagues (2016) focused on SRGs regulated upon heat shock and using NIH/3T3 and HeLa cell lines, therefore, it is difficult to me understand how, searching for "cellular function connected with B2 RNA regulated SRGs", the list resulted enriched of neuronal tissue terms or cellular compartments related to neuronal functions. Please clarify this point since the following analyses are based on these findings.

-In Figure 1F there is no arrow indicating that some of the SRGs regulate directly miR-34 as stated in the main text. Moreover, it is more appropriate to replace SRGs with learning‐associated genes both in the figure and in text (2nd paragraph of the results) since Zovoilis and colleagues focused on them. Finally, they did not show in their manuscript the rescue of p53 expression mediated by mir-34; indeed, for miR-34-p53 regulatory axis Zovoilis and colleagues referred to Peleg et al, 2010 and Yamakuchi & Lowenstein, 2009. Please fix all these concerns.

-The Fig.1A and Fig.1F are wrongly indicated at the end of the sentence "....levels of these genes are normally downregulated in 6m and 12m old mice compared to 3m old mice (p=0.02 and p=0.04, respectively)"; please correct this point.

-Figure 2:

a) Since three mice for each condition have been used for the RNA seq analyses, please provide a blot with the Principal Component Analysis (PCA).

b) Fig 2F comes first of Fig 2E in the text, however, I suggest to move this latter to supplementary material.

c) In general, this study lacks validation of the RNA-seq results. Western blot and/or qRTR-PCR to verify the variation of p53 and of some selected SRGs have to be provided.

d) It is also not clear how the authors defined SRGs in the hippocampus: do they correspond to learning‐associated genes described by in Zovoilis et al, 2011 or to B2 RNA H/S regulated genes by Zovoilis et al, 2016?

-APP 12 month old mice show the sever phenotype of the terminal AD-like pathology, however this does not correlate with significant SRGs and B2 processing increase. Can the author make a comment on this?

-Figure 5:

a) a gel with no-protein control for the time course of panel B was cited in the text but missing among the panels. Moreover, the time course shown in the graph in 5C does not correspond to the one in 5B.

b) 5G indicates that four samples for each condition have been analysed by RNA-seq, since they do not seem to be homogeneous please provide a PCA analysis together with the validation by qRT-PCR of a selected group of deregulated genes. Moreover, it is not clear whether all the genes shown in the heatmap or a number of them, as stated in the text, were found upregulated in 6m old APP mice. Please clarify this point and modify the figure and the text accordingly. A Venn diagram showing the overlap between genes upregulated in 42vsR treatment and those upregulated in 6m old APP mice might help the comprehension of the experiment.

-Figure 6:

a) The evaluation of the levels of Hsf1 mRNA and protein upon LNA transfection is missing for both R and 42 treated HT22 cells. From TPM in panel B, Hsf1 downregulation seems to have been more effective in 42 than in R condition. This would mess up the interpretation of the data.

b) Again, in this case any validation of the RNA seq data is provided (any B2 regulated SRGs).

c) Panels E and F should be swapped or panel E moved to supplementary material.

-In a previous paper the authors discovered B2 RNAs as a class of transcripts bound to EZH2 and this interaction leads to B2 RNA destabilization in heath shock (H/S) condition. The authors also conclude that the genes controlled by B2 RNAs may not overlap with the ones controlled by Hsf1 during H/S. The author should make a comment on this explaining why during H/S B2 RNAs work independently from Hsf1 and on different target SRGs while, during beta amyloid stress ,the two act together on the same SRGs. Moreover, as shown for EZH2, Hsf1-RIP experiment should be performed in order to confirm the direct involvement of Hsf1 in the SRGs-B2 destabilization.

-There is any table listing the results of the RNA seq experiments performed in this paper: control vs APP 3-6-12 m old mice and in R vs 42 treated HT22 cells in presence or absence of LNA against Hsf1. Please provide these data.

-In the discussion the authors claim that healthy cells are able to restore the expression of Hsf1, SRGs and B2 RNA upon removal of the stress. Since there are evidence for the rescue of SRGs and B2 RNA expression post H/S, no data are available for Hsf1, SRGs and B2 RNA upon the removal of 1-42 beta amyloid peptide. This might be a nice information to add to the manuscript.

Minor criticisms:

-In the introduction the reference Yamakuchi M and Lowenstein CJ, (2009) MiR‐34, SIRT1 and p53: the feedback loop. Cell Cycle, should be added in the sentence: "In contrast, hippocampi of mouse models of amyloid pathology and post- mortem brains of human patients of AD.....and neural death (Zovoilis et al., 2011)."

-Authors refer to Hernandez et al., 2020 to state that B2 self cleavage is stimulated by some proteins however, Hernandez and colleagues studied only the effect of EZH2 protein. Please rephrase the sentence accordingly.

-Indicate a reference for the sentence: "......Ezh2, was reported as being responsible for the B2 RNA accelerated destabilization and processing during response to stress."

-The format of many references is not consistent and has to be revised.

Significance

The research fields of non coding RNAs and neurodegeneration are attractive and challenging and, in my opinion, the molecular circuitry involving B2 RNAs might add important insights for understanding beta amyloid toxicity and neuronal death. However, this manuscript does not really add technical advances since the authors employed experimental approaches and bioinformatic analyses previously published by Zovoilis and colleagues in 2011 and 2016.

The reported findings might of interest of an audience of experts in non coding RNAs and neurodegeneration.

The area of my expertise almost regards the biology of non coding RNAs from biogenesis to function manly focusing on neuronal and muscular systems both in physiological and pathological conditions.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

Summary:

This manuscript follows from previous work by the corresponding author showing that SINE-encoded B2 RNAs function as regulators of the expression of stress response genes (SRGs). Specifically, stimulus triggers the processing of repressive B2 RNAs that are bound at the SRGs, thereby activating SRG transcription. In this work, the authors investigate whether a similar mechanism might be controlling the expression of genes in models of amyloid beta neuropathology (i.e. mouse hippocampi from an amyloid precursor protein knock-in mouse model, and a cell culture model of amyloid beta toxicity). They performed RNA-seq in these models. Their data show a correlation between the progression of amyloid pathology, expression of genes thought to be regulated by B2 RNA, and the processing of B2 RNA. In addition, they show biochemical data supporting a role for Hsf1 in enhancing the processing of B2 RNA. Knockdown of Hsf1 also reduced B2 RNA processing and the expression of SRGs.

Major comments:

1 . In the RNA-seq data one cannot distinguish between Pol III transcribed B2 RNA and Pol II transcribed B2 RNA (typically embedded within introns and UTRs of mRNAs). The models they present, and the structures they show, clearly imply regulation by Pol III transcribed B2 RNA. However, there is no way to know that the short B2 RNAs they sequence aren't coming from degraded mRNAs. This needs to addressed. Minimally, in writing as a caveat of their model. Ideally, it would be addressed experimentally.

2 . The direct regulation of SRGs by B2 RNA was not shown in their model systems for amyloid beta neuropathology. Rather, the authors' used the genes identified in their prior studies as B2 RNA-regulated, which I believe were in the NIH3T3 cell line. Given that transcription is highly cell-type specific, these genes might not be regulated by B2 RNA in mouse hippocampi or their cell culture model, despite the correlations shown. This needs to be addressed. Ideally, a targeted approach to show that transcription of even a couple genes in their system is indeed regulated by B2 RNA would provide stronger support for their conclusions.

3 . The following bioinformatics analyses would strengthen their conclusions. This should be straightforward to do because it involves data they already have, and perhaps analyses they have already have performed.

a. Regarding the plot in Figure 3A (lower panel). The same plot should be shown for the 3m old and the 12m old APP mice (i.e. not just the 6m data). This would show the specificity of processing B2 RNA and that it indeed correlates with disease progression.

b. Regarding the plots of B2 RNA processing rate. This value could increase either due to more short RNAs or less full length RNA. Which is it for the 3m, 6m, and 12m APP mice? Showing the short and long B2 RNAs as boxplots (as opposed to only the processing rate) would address this and also provide additional insight into the regulation involved. The same applies to the data in Figure 6. (As an aside... do the authors mean processing ratio as opposed to rate? I'm not clear where the time component is coming into play to call this a rate.)

c. The random genes in Figures 2E and 6E are plotted as heat maps, but statistical significance is hard to see. What do boxplots of the random genes look like, and is the significant difference between 6m old APP and 6m old WT then lost?

4 . It is interesting that B2 RNA self-processing is enhanced by both Ezh2 and also Hsf1. It would strengthen the data to perform a control with a protein prepared more similarly to the Hsf1 (rather than PNK) to confirm that the enhanced B2 RNA breakdown is indeed attributable to Hsf1 and not a contaminant in the protein prep. Similarly, the authors should provide information on which RNA was added as the negative control for Hsf1-stimulated breakdown (i.e. the ~80 nt RNA).

Minor comments:

1 . Regarding the GO analyses in Figure 1 (panels B, C, and D). I wasn't clear whether the authors are showing all statistically enriched terms, or only those relevant to neuronal processes and learning. I recommend showing a supplemental table with all terms that have an adjusted p value below a specified cut-off (e.g. 0.05).

2 . The authors show several figures that are not new data (2B, 4A, 4B, Suppl. Fig 1 and 2). I think it would be more clear if these data were summarized and referenced in the results, rather than shown.

3 . In Figure 3A the schematic shows that B2 is 155 nt, the plots in Figures 3A,B,C show B2 RNA is 120 nt, and Figure 5 shows the RNA is 188 nt. Can the authors please clarify these differences?

4 . In the Methods section, the sequence of the g block template didn't contain the T7 promoter sequence that was used as the forward primer for PCR amplification?

5 . In Figure 6B, why were Hsf1 levels not decreased in the R treated cells after treatment with the LNA?

Significance

The models presented for the regulation of stress response genes (SRGs) in amyloid beta neuropathologies are compelling. As are the correlations they found between the progression of amyloid pathology, expression of genes thought to be regulated by B2 RNA, and the processing of B2 RNA. This is a unique direction of research for brain disease and represents an interesting conceptual advance. Most prior studies in this area use common model cell lines, and this lab seems well-positioned to unravel the proposed molecular mechanisms in neuronal systems.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

B2 RNAs, encoded from SINE B2 elements has been directly implicated in stress response by its inherent ability to bind RNA Pol II and suppress stress response genes (SRG) in homeostatic conditions. However, upon stimuli, B2 RNAs are cleaved and degraded, resulting in the release of RNA pol II and upregulation of SRGs. Previous work from the senior author identified PRC2 component EZH2 to be the B2 RNA processing factor, cleaving B2, and releasing POL2. SRGs are upregulated upon stress, for example in age-associated neuropathologies like Alzheimer's disease (AD). Considering that the hippocampus is a primary target of amyloid pathologies as well as since SRGs are suggested to be key for the function of a healthy hippocampus, the authors set to understand the role of B2 RNAs that are linked to SRG regulation in the mouse hippocampus with amyloid pathology. They use disease-relevant in vivo and in vitro models combined with unbiased RNA seq data analysis for this endeavor, which indicates the potential relevance of B2 RNAs in APP mediated neuronal pathologies in mice as well as identifies Hsf1 as the factor cleaving B2 RNAs in the hippocampus. The work is interesting and identification of Hsf1 as the processing factor for B2 RNAs in the hippocampus is significant. I would like to credit the authors for their elegant in vivo experimental design in Figure 2. However, I find some of the conclusions to be overstated and I would like to bring the following concerns I have to your attention:

Major comments:

1 . In figure 1, the authors indicate a strong connection between B2 RNA regulated SRGs and learning and memory. In figure 2, they identify the SRGs in the hippocampus, please provide a direct comparison of learning and memory associated SRGs and the SRGs they identify in figure 2 that are significantly upregulated in APP mice in 6 months.

2 . To better understand the data in the context of hippocampal function, please include functional annotation of SRGs they identified in Figure 2F as they do it in Figure 1 (desirably for each time point, at least for 6M). How many of the SRGs they identify in Figure 1 are part of Figure 2F? Please include functional annotation of significantly upregulated B2 regulated SRGs in Fig2 and compare them with that of Figure 1.

3 . In figure 3, the authors report that the B2 processing rates are high at the 6M time point at in hippocampi of the APP mice. Please include the levels of unprocessed and processed B2 RNAs in these samples along with this figure, without which it is difficult to gauge the significance of its correlation with SRGs in Figure 2.

4 . What is the % of B2 regulated SRGs that are hsf1 bound in Figure 4C? What is there dynamics in the wild type and APP hippocampi?

5 . What is the distribution of Hsf1 binding sites on (a) non-B2 regulated SRGs and (b) non-SRG genes in hippocampi?

6 . In Figure 4D, the 3months old Wt HSF1 levels are high, yet B2 processing (Figure 3E) is low. Please comment.

7 . While the authors show in vitro cleavage of B2 RNA by Hsf1, the experiment lacks controls to be conclusive. At least, please include a similar size protein as HSF1 with no-known RNA binding activity and a similar size protein with RNA binding activity as controls in 5A. Please justify the use of PNK as the control protein. Please include the use domain-based deletions of Hsf1 to map the region of HSF1 that is binding and potentially cleaving the B2 RNA. Please include an RNA of similar size and Antisense-B2 RNA to show the specificity of the Hsf1 based cleavage of B2 RNA. Without these controls, the conclusions in Figure 5 cannot be substantiated.

8 . The authors should show that the incubated APP peptides are taken up by the cells (experiments in Figure 5F and Figure 6).

9 . Please provide the list, functional annotation, and % of the SRGs upregulated upon incubation with APP in HT22 cells in comparison to 6month old APP mice. Comment on learning-related Genes.

10 . The authors should show the efficient downregulation of Hsf1 (protein) upon anti-Hsf1 LNA transfection.

11 . Please present the total B2 RNA levels for conditions in Figure 6C.

12 . Hsf1 levels are not significantly downregulated in Control cells which were inoculated with the reverse APP peptide. Please comment.

13 . Please compare and contrast the % of genes, the overlap, and the functional distinctions in 6F to that of 5G and Figure1. What are the genes that are common between Figure1, and that are specifically upregulated upon Anti-Hsf1 LNA transfection along with 1-42 APP. What is % of the occurrence of B2 binding sites in those genes? What are their functional annotations and what is their connection to learning, memory, and cell survival?

Minor.

1 . Please include TPM/ FPKM values for hippocampal markers as control in Figure 2 to do justice to the hippocampus specific RNA seq conducted by the Authors.

2 . In figure 2D the authors show that B2 RNA regulated SRGs in the 3 months' wild type mice are significantly high. P53 has been reported to be high in young wild types hippocampus, but not SRGs in my opinion. The authors should comment on this.

3 . In figure 2F, under the 6m APP condition, the replicate 3 looks substantially different from the other replicate. This can significantly impact the analysis and conclusions made. Either remove that replicate and present the analysis without it or please provide a valid explanation. To make the data more valid, please provide hierarchical clustering of the entire data, the non-B2 regulated genes and the B2 regulated SRGs. In Figure 2C RNA seq data is represented in TPM while its FPKM in Figure 2D. Figure 2: the number of replicates in the case of 3-month-old wild types only 2. Please specifically denote it and comment why only 2 replicates are provided

4 . Considering that p53 and SRGs are significantly upregulated in 6months in the APP model, it would be great if (allowing that these samples are still available) the authors can include a staining for apoptotic markers, for example, Active Casp3 or similar. This will allow us to better gauge the gene expression changes presented by the authors especially regarding SRGs.

5 . Under subheading: Hsf1 accelerates B2 RNA processing, 3rd paragraph when the authors comment on known hsf1 binding sites on SRG genes, please correct from: Increased Hsf1-binding was found.... "To the increased number of hsf1 binding sites were found", unless the authors would like to show increased Hsf1 binding by performing CHIP-seq for Hsf1 in the hippocampus at least at the 6-month time point between Wt and APP mice.

Significance

B2 RNAs, encoded from SINE B2 elements has been directly implicated in stress response by its inherent ability to bind RNA Pol II and suppress stress response genes (SRG) in homeostatic conditions. However, upon stimuli, B2 RNAs are cleaved and degraded, resulting in the release of RNA pol II and upregulation of SRGs. Previous work from the senior author identified PRC2 component EZH2 to be the B2 RNA processing factor, cleaving B2, and releasing POL2. SRGs are upregulated upon stress, for example in age-associated neuropathologies like Alzheimer's disease (AD). Considering that the hippocampus is a primary target of amyloid pathologies as well as since SRGs are suggested to be key for the function of a healthy hippocampus, the authors set to understand the role of B2 RNAs that are linked to SRG regulation in the mouse hippocampus with amyloid pathology. They use disease-relevant in vivo and in vitro models combined with unbiased RNA seq data analysis for this endeavor, which indicates the potential relevance of B2 RNAs in APP mediated neuronal pathologies in mice as well as identifies Hsf1 as the factor cleaving B2 RNAs in the hippocampus.

The work is interesting and identification of Hsf1 as the processing factor for B2 RNAs in the hippocampus is significant. I would like to credit the authors for their elegant in vivo experimental design in Figure 2.

Note: This rebuttal was posted by the corresponding author to Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

We thank the reviewers for their useful suggestions to improve the manuscript and their support for publication. We have addressed all the comments that have been raised and carried out the suggested additional analyses, resulting in a significantly improved revised version of the manuscript. We provide hereafter a detailed point-by-point response to all questions and comments of the three reviewers.

Reviewer #1 (Evidence, reproducibility and clarity (Required)):

Centriole structure has been an attractive but challenging research topic for years. Pierre Gonczy's group has been working on its structure using cryo-electron tomography (cryo-ET). While the axoneme, which has longitudinal periodicity, was analyzed by several groups by cryo-ET for more than a decade, cryo-ET study on the centriole suffers from poor signal to noise ratio due to its limited length and thus fewer periodicity. They chose the centriole of flagellate Trichonympha, which have exceptionally long centrioles and thus offer opportunity of relatively straightforward sub-tomogram averaging. Their approach has been successful, and they revealed intermediate resolution structure of the cartwheel, key of 9-fold symmetry formation, and it's joint to triplet microtubules (Guichard et al. 2012, 2013, 2018).

In this work, they employed modern state-of-art cryo-ET technique, such as direct electron detection and 3D image classification to upgrade our knowledge of centriole structure. In their past works, the central hub of the cartwheel, made of SAS-6 protein forming 9-fold complex, was described as an 8nm periodic object. With improved spatial resolution, they provided further detail with clear polarity, which will deepen our thought about the initial stage of ciliogenesis. They also compared two Trichonympha species (spp and agilis) as well as another flagellate, Teranympha mirabilis, and extended their intriguing evolutional and mechanical hypotheses based on structural differences.

Despite improved spatial resolution, it is still not possible to identify proteins in the cryo-ET map (cellular cryo-ET will not reach such high resolution in the near future). Therefore, this work is rather geometrically descriptive, which will inspire molecular biologists to identify molecules by other methods. Nevertheless, this work demonstrated capability of cellular cryo-ET, especially analysis of structural heterogeneity. Thus, while biological topics handled are rather specialized for cilia from flagellate, this work will attract attention of any biologist interested in molecular structure in vivo. It is worth for publication in a high Journal after addressing the points below. This reviewer believes that the authors can address these points easily with additional analysis.

We are grateful to the reviewer for the favorable evaluation and the many valuable suggestions, in particular concerning the processing pipeline, which we addressed by additional analyses, as detailed below.

Major points:

1. Entire scheme A graphic diagram of the entire cartwheel area, summarizing this work, is necessary for the readers' understanding (similar to Fig.6 of the other manuscript, Klena et al.).

We thank the reviewer for this interesting suggestion, which we fully adhere to. As a result, we have generated a graphical summary of the work, which is shown in the new Figure panels 6B-F. Moreover, Figure 6A provides an evolutionary perspective regarding the presence of the CID and of what is now referred to as the fCID (filamentous CID, previously: FLS, see response to reviewer 3). This also helps to link our findings with the companion manuscript by Klena et al. This new Figure 6 is referred to extensively in the discussion of the revised manuscript (pages 13-16).

Then average scheme should be shown in more detail, especially assumption of periodicity, Materials and Methods. The cartwheel hub was averaged with 25nm periodicity (as discussed below). Was the pinhead averaged with 16nm (as detected by FFT in Fig.S2L)? How about the triplet?

This reviewer is not completely sure if the longitudinal averaging strategy is justifiable. Since periodicity of each domain is not trivial, logically the initial average must be done with the size of least common multiple (or larger). It is likely 96nm, assuming 25nm of the central hub is 3 times of microtubule periodicity and 16nm of the pinhead is twice of MT. 96nm average should be possible with a long cartwheel in this work. Alternative, in case periodicity is independent of MT and thus there is no least common multiple, is random picking and classification mentioned in "4. Periodicity". This should also be possible, since they can pick enough number of particles from long cartwheels.

We apologize that the initial version of the manuscript was not sufficiently clear regarding the averaging pipeline that was pursued. To rectify this, we now provide a new Figure S1B to graphically explain the approach followed for STA. As depicted in this figure panel, the step size for sub-volume extraction was 25 nm both centrally and peripherally. This step size was selected because it corresponds to ~3x the major periodicity of ~8.5 nm observed in the power spectra of the sub-volumes. The 25 nm step size is larger than that previously used (i.e. 17 nm in Guichard et al. 2013), in order to identify potential features with larger periodicities. The fact that the step size was of 25 nm in all cases is now mentioned explicitly in the Materials and Methods section of the revised manuscript (line 649).

We agree with the reviewer that 96 nm averaging is possible given the long cartwheel analyzed here, and such a piece of data was in fact included in the original submission, although with a different purpose. Indeed, we carried out STA using ~(100 nm)3 sub-volumes (with binning 3 to reduce computational time), the results of which are reported in Figure S7 (previously Fig. S6). For the purpose of this analysis, we focused on the lateral organization of the cartwheel, but did not use this dataset to explore other periodicities because of the limitations inherent to a binning 3 data set.

• Classification*

The authors analyzed structural heterogeneity inside the cartwheel hub, employing reference-free classification by Relion software. The program reveals multiple coexisting structures - two from Trichonympha agilis and three from Teranympha, respectively. Whereas this is an exciting finding and shows future research direction of this field, interpretation of this classification must be done carefully. ** It is puzzling that major (55%) population of T. agilis shows more ambiguous features than the minor population (45%), while spatial resolutions by FSC are not so different - for example, Fig.2H vs Fig.S5C. In case of Teranympha, it is even more drastic - Fig.4D (major class) seems blurred along the centriolar axis, compared to Fig. 4E (minor class). This reviewer is afraid that these "major" classes might contain more than one structure and after subaveraging be blurred in detailed features. The apparent good spatial resolution could be explained, when two structures coexist and subtomograms are aligned within each subclass. Probably lower resolution at the spoke region of the major class (Fig.S2A) than that of the minor class (Fig.S2D) is a sign of heterogeneity within this class. Another risk could be subtomograms with poorer S/N being categorized to one class (due to lack of feature to be properly classified). Fig.S5F (black dots localized in one tomogram) raised this concern.

The following investigation will help to solve this issue. 1. Extract and re-classify subtomograms belonging to the major population. 2. Direct observation of tomograms. The authors could plot two classes of Teranympha (as they did for T. agilis in Fig.S5) and find features of the cylindrical cartwheel hub in two conformations (as shown Fig.4DE). Since such a feature was directly observed in tomograms from the other manuscript (left panels of Fig.S6AC in Klena et al.), it should be possible in this work as well.

We agree with the reviewer that the interpretation of the classification must be done with care, and share her/his interest in better understanding the structural variability between cartwheels classes in T. agilis and T. mirabilis. Although poor S/N may in theory result in erroneous joint classifications, we note that all maps in the original submission stemmed from extensive focused 3D classification, which removed defective and spurious sub-volumes, nevertheless defining distinct classes in the cases reported. Obviously, however, we cannot exclude that much larger data sets and future software advances may lead to the identification of additional features that would allow further sub-classes to be identified.

Regardless, we followed the two suggestions the reviewer offered to us and have (1) extracted and re-classified sub-tomograms belonging to the major populations and (2) undertaken a direct observation of tomograms. These two points are developed in turn below.

(1) We have performed a further round of classification of the major populations in T. agilis (55 % class) and T. mirabilis (64 % class), to assess whether additional sub-classes might be identified and thus help further improve the quality of the central cartwheel map. However, this additional round did not yield new sub-classes nor notable improvement in the map quality as judged by visual inspections. We show in Rebuttal Figure 1 a comparison in each case of the original STA and the corresponding STA upon such re-classification. Importantly, all conclusions spelled out in the original submission hold upon further re-classification, indicating that the initial classification converged to the best map quality based on the current data set and available computational resources.

(2) We have followed the suggestion of the reviewer and now show raw tomograms to confirm that the classes correspond to bona fide structures and not to processing artefacts (new Figures S1C-F). The resulting new Figure S1D for instance shows that the striking variations observed between classes in the T. agilis STA are also visible in the raw tomogram. The more subtle variations among T. mirabilis classes are more difficult to observe in the raw tomogram, but inherent variations that reflect the presence of two classes are nevertheless observed.

Furthermore, following the reviewer’s suggestion, we now mapped the distribution of the two T. mirabilis cartwheel classes onto tomograms, revealing that both classes can occur next to each other within the same centriole (new Figure S8E).

• Periodicity mismatch*

In Fig. 2CD, periodicity of CID has discrepancy from that of the stacked SAS-6 ring (8.5nm and 8.0nm). Do the authors think this is a significant difference or within an error? The same question can occur to other subtomogram averages. It would be nice to show errors as shown in their other manuscript (Fig.3C of Klena et al.) and clarify their idea. If it is systematic difference of periodicity between the stacked ring and CID, this shift will be accumulated through the entire cartwheel region - after 100nm, 8.5nm/8.0nm difference can be accumulated to ~6nm, which should change the entire view of the subtomogram - and the main factor to be classified (periodicity mismatch). This artifact (or influence) should be removed (or separately evaluated) by masking CID (out and in) and run classification separately. By clarifying this, the quality of the major subaverages (mentioned in the previous paragraph) could be improved.

The reviewer wonders whether there might be a periodicity discrepancy within one map, for instance between CID and spokes in the T. spp. cartwheel map (Fig. 2C and Fig. 2D). Here, the periodicity determined from the STA maps is 8.5 ± 0.2 nm (SD, N=4) for the CID and 8.0 ± 1.5 nm (SD, N=2) for the spokes. Based on these standard deviations, there is indeed no significant difference between the two, and thus no periodicity discrepancy. The same applies for measurements in T. agilis and T. mirabilis. The SDs were reported already in the figure legends of the original submission, and we would prefer to leave them there if possible and not mention them in the figures, which are pretty busy as is. We apologize if this was not clear enough in the initial manuscript. Likewise, one may wonder whether there might be periodicity discrepancies between structures from distinct maps, for instance between CID and A-links from T. spp. (Fig. 2C and Fig. 3D). Again, the measurements are within error, since the distance between adjacent CIDs is 8.5 ± 0.2 nm (N=4) and between adjacent A-links 8.4 ± 0.4 nm (N=6); a similar conclusion applies for the corresponding measurement comparisons in T. agilis and T. mirabilis. The figure legends have been altered in the revised manuscript to spell out that there are no significant differences between periodicities (lines 856-858).

Furthermore, we would like to stress that, by definition, STA value are average distances. For instance, in the case of T. spp., the central cartwheel STA was obtained from 511 sub-volumes, and thus the reported N=2 represents the average distance from 511 sub-volumes. Since this is an average, errors can therefore not accumulate over longer distances. This point has also been clarified in the figure legends (line 856-858).

• Periodicity*

They averaged subtomograms extracted with spacing of 252A with initial average as the first template (p.18 Line22). This means they assumed 25nm periodicity from the beginning and excluded different or larger unit size (if they take search range wide, they could detect difference periodicity, but will still be biased by initially assumed 25nm). 25nm average allowed them to see more detail than before (when they assumed 8nm periodicity), but there is still a risk of bias from references. To avoid this risk, this reviewer would propose classification of randomly extracted (but of course along the cylindrical hub or along the triplet microtubules, so one-dimensionally random picking) subtomograms. This experiment will end up with multiple sub-averages, which are 25nm (or multiple times of that) shifted from each other. Then it will prove their assumption.

We agree with the reviewer that in theory the choice of periodicity could introduce a bias. This is why we have chosen a larger step size than in our initial work, corresponding to ~3x the major periodicity of ~8.5 nm observed in the power spectrum of the sub-volumes, as mentioned above. Regardless, following the reviewer’s suggestion, we have now explored other types of periodicities by re-analyzing the dataset through extraction of non-overlapping sub-volumes along the proximal-distal centriole axis. In doing so, we randomized the starting position of the first box between tomograms, reaching the same goal as with random picking but maximizing the number of sub-volumes. We carried out this analysis for all T. spp., T. agilis and T. mirabilis cartwheel classes, and found no notable differences that would affect the conclusions of the manuscript compared to the initial overlapping sub-volume classification, albeit generally with a noisier STA due to the lower number of sub-volumes. A comparison of the two approaches is provided in Rebuttal Figure 2. Moreover, all the points regarding the choice of periodicity have been further clarified in the expanded Materials and Methods section (pages 19-21).

Minor points:

They discussed difference of stacked SAS-6 rings in the cartwheel from various species. How much is the sequence difference of SAS-6 among these species?

Unfortunately, no genomic or transcriptomic data has been published for the species investigated here, although the sparse molecular data available from small subunit rRNA sequences allows one to establish an overall molecular phylogeny. We previously identified a SAS-6 homologue in T. agilis (Guichard et al. 2013), which shares 20 % identity and 45 % similarity with C. reinhardtii SAS-6. Despite low sequence conservation, the structural conservation of SAS-6 is predicted to be high between the two organisms (Guichard et al. 2013). We apologize if these points were not expressed sufficiently clearly in the initial rendition and have adapted the wording in the revised manuscript (lines 325-332).

Are the authors sure that CID is nine-fold symmetric? It is not trivial.

We thank the reviewer for bringing up this interesting point. We have applied 9-fold symmetrization to the entire central cartwheel comprising spokes, hub and CID/ fCID, a choice guided by the apparent 9-fold symmetry of the spokes and peripheral element. We investigated the impact of symmetrization on the CID by relaxing symmetry from C9 to C1 during refinement, but did not observe a difference, and thus continued with C9 symmetry, which improves map resolution by S/N ratio enhancement and additional missing wedge compensation. In addition, we have also analyzed the CID without symmetrization, as reported in Figure S7 (previously: Fig. S6). Note that these maps were generated with larger sub-volumes centered on the spokes to comprise hub, spokes and microtubule triplets, explaining the resulting lower resolution, as the missing wedge is not compensated. Despite these limitations, however, the unsymmetrized CID shown in Figure S7A and S7E resembles the one in the symmetrized maps of Figure 2, indicating that the CID indeed exhibits 9-fold radial symmetry. That this is the case is spelled out explicitly in the revised manuscript (lines 1145-1147).

Fig.1C: Another cross-section from the distal region will be helpful. A longer scale bar is better for readers' understanding.

We understand that the reviewer is curious about the distal region, and cross-section views of resin-embedded sections from T. agilis are available and could be provided if necessary. However, given that the focus of the manuscript is strictly on the cartwheel-bearing proximal region, we felt that featuring the distal region in detail would break the narrative. Therefore, we suggest to keep Figure 1 as in the original manuscript. Following the reviewer’s suggestion, we increased the size of the scale bars from 10 nm to 20 nm in Figure 1C as well as in the corresponding Figure S8C.

Fig.S6F: It would be informative if the subclasses (25% and 20%) are distinguished in this mapping.

As per the reviewer’s request, we provide in Rebuttal Figure 3 a side-by-side comparison of the T. agilis 25 % and 20 % classes centered on the spokes, which are noisier than the composite 45 % class due to the lower number of sub-volumes in each sub-class. Given that there are no notable differences between the two maps that would affect any of the conclusions of the manuscript, we feel it is best to keep what is now Figure S7F (previously: Fig. S6F) unchanged in the revised manuscript.

A figure to explain the classification scheme will help readers understand. How many subtomograms did classification started? Were the 45% class classified into two (25% and 20%) groups by two-step classification or at once (the entire subtomograms were classified into three groups directly?

We thank the reviewer for this useful suggestion. As a result, we have generated a new Supplemental Figure S1G-J that provides a graphical overview of the classification scheme, together with sub-volume numbers for all deposited maps, thus nicely complementing Table S1.

Reviewer #1 (Significance (Required)):

Nevertheless, this work demonstrated capability of cellular cryo-ET, especially analysis of structural heterogeneity. Thus, while biological topics handled are rather specialized for cilia from flagellate, this work will attract attention of any biologist interested in molecular structure in vivo. It is worth for publication in a high journal after addressing the points above. This reviewer believes that the authors can address these points easily with additional analysis.

We reiterate our thanks to this reviewer for her/his favorable evaluation and detailed suggestions, which enabled us to generate a strengthened manuscript.

Reviewer #2 (Evidence, reproducibility and clarity (Required)):

Here, Nazarov and colleagues report sub-tomogram average (STA) maps of centrioles with 16 to 40 Å resolution from Trichonympha spp., Trichonympha agilis, and Teranympha mirabilis. Even though the authors have previously described the centriole architecture of T. spp, these STA maps of higher resolution revealed new features of centrioles, like polarized Cartwheel Inner Density (CID) and the pinhead. They also observed Filament-like structure (FLS) from T. mirabilis which seems to correspond to the CID from other species. Interestingly, they suggest that one and two SASS6 rings are stacked in an alternative fashion to make the central hub in T. mirabilis (Figure 5). The following issue should be addressed:

Major points

• Figure 4E. Authors mentioned in the manuscript that "We observed that every other double hub units in the 36% T. mirabilis class appears to exhibit a slight tilt angle relative to the vertical axis". When I see the other side, it does not seem to be tilted. Could the authors explain this?*

We apologize that this aspect was not explained in sufficient detail. The left and right sides of the hub indeed appeared different in transverse views across the cartwheel center (previous Fig. 4E). This was because the area we selected in the original submission was centered on one emanating spoke. Due to the 9-fold symmetry one spoke density was selected on the right side, while the region between two spokes was displayed on the left side (as was illustrated by the slice across the center in previous Figure 4A; dashed rectangles in 4.0 nm panel). We have now selected a larger area to include spokes from both sides of the hub and thus better visualize this offset as shown in the modified Figure 4D-E.

Reviewer #2 (Significance (Required)):

I believe these results are of interest for all centrosome researchers and would like to recommend this manuscript be published in the EMBO journal which is affiliated with the Review Commons.

We thank the reviewer for the recommendation to submit the revised manuscript to EMBO Journal, which we have followed.

Reviewer #3 (Evidence, reproducibility and clarity (Required)):

In this manuscript Nazrov et al., use cryo-electron tomography (CET) to analyse the structure of the centriole cartwheel. The Gonczy lab have previously generated a ground-breaking structure of the cartwheel from Trichonympha spp (T. spp.) (Guichard et al., Science, 2012; Guichard et al., Curr. Biol., 2013). This work is a direct continuation of those studies but using modern technology to get higher resolution images of the T. spp. cartwheel and comparing this to the cartwheel from Trichonympha agilis and from another distantly related flagellate Teranympha mirabilis.

The data is generally well presented and of high quality. I am not an expert in CET, so it would be advisable to get the opinion from a reviewer who is, but the Gonczy lab are experienced in these techniques so I would not anticipate any problems. I have to admit that the title of the paper did not excite me, and I expected this to be a very worthy, but incremental study. It was a pleasure to find out that the extra detail provided by the increased resolution has revealed several new and unexpected features that have important implications for our understanding of cartwheel assembly and function. Most important are the potential asymmetry of the cartwheel hub, apparent variations in the packing mechanism of the stacked rings (even within the same cartwheel), and the potential offsetting of ring stacking. These findings will be of great interest to the field, and so I am strongly supportive of publication in The EMBO Journal. I have only a few points that I think the authors should consider.

We thank the reviewer for this positive feedback and the recommendation to submit to EMBO Journal, which we hereby follow.

Prompted by the comment of the reviewer, we revised the title to make it more informative and appealing to readers: “Novel features of centriole polarity and cartwheel stacking revealed by cryo-tomography”.

• Nazarov et al., conclude that the cartwheel structure is intrinsically asymmetric. This is most convincingly based on the displacement of the CID within the hub, but they state that the Discussion that the potential offset between the Sas-6 double rings generates an inherently polar structure. I didn't understand why this is the case. Looking at Fig.S9A,B I can see that the offset in B could tilt to the left (as shown here) or to the right (if the structure was flipped by 180o). But I couldn't see how this makes this structure polar in the sense that a molecule coming into dock with the structure could only bind to one side of the offset structure shown in B, but to both sides of the aligned structure shown in A. I think this needs to be explained better, as it is crucial to understand where any potential polarity in the cartwheel structure comes from.*

We apologize for not having been sufficiently clear about how two SAS-6 rings with an offset could impart organelle polarity. The reviewer is correct that an offset between superimposed rings alone is not sufficient to generate polarity at a larger scale. The important point we would like to stress, however, is that we discovered concerted polarity in multiple locations, from the central hub to the peripheral elements as illustrated in Fig. S7C-D, S7G-H, S7K-L and S7O-P (previously: Fig. S6). Prompted by the reviewer’s comment, we now better emphasize the asymmetric tilt angles of merging spokes, as highlighted also in the improved Figure S7. This asymmetric spoke tilt angle allows one to discriminate the proximal and distal side of a double SAS-6 ring, which is now explained better in the text (lines 259-263 & 502-510).

• Related to this last point, in a co-submitted paper Klena et al. do not report such an asymmetry in the hub structures they have solved from several different species (neither in the tilting of the hub, or the displacement of the CID). I think it would be worth both sets of authors commenting on this point.*

We agree that comparing and contrasting the results of the two companion manuscripts is important and we have updated the text as a consequence in several places (lines 444, 467, 507, 536, 985, 1000). We know from our previous work (Guichard et al. 2013) that the asymmetry of the hub and spoke is not visible at lower resolution. In the accompanying manuscript by Klena et al., no offset in the hub or asymmetric CID localization is reported, probably due to lower resolution and differences between species.

• The authors data strongly suggests that the T. ag. and Te. mir. hubs are composed of a mixture of single and double Sas-6 rings. In contrast, the T. spp. cartwheel only has a single class of rings, but it wasn't absolutely clear if the authors think this comprises a single or double ring. In the text it is presented as though the elongation of the hub densities in the vertical direction is a new feature of the T. ag cartwheel (Fig.2H,I), but to me it looks as though this is also apparent in the T. spp. cartwheel (Fig.2C,D). The authors should address this directly and, if they believe that T. spp. has a double ring, they should comment on whether this more regular structure seems to have offset rings. If not, then the offset rings are unlikely to be the source of asymmetry that leads to the asymmetric displacement of the CID. Finally, if the authors think these are double rings, they should also be clear that they would now slightly re-interpret their original T. spp. cartwheel model (Figure 2, Guichard et al., Curr. Biol.). There is no embarrassment in this-a higher resolution structure has simply revealed more detail.*

We apologize if the conclusions drawn about T. spp. cartwheel hubs were not sufficiently clearly expressed. Like the reviewer, we think that elongated hub elements are also discernible in T. spp., something that is also illustrated by the intensity plot profile in Figure 2C (double peaks on light blue line). These points are spelled out more explicitly in the revised manuscript (lines 177-179). In addition, to emphasize the conservation of the double hub units in both Trichonympha species, we have likewise adapted the text for T. agilis (lines 198-201).

As for the offset observed within T. spp. spoke densities in Figure S10H, we interpret this as evidence for an offset of the double ring at the level of the hub, although we have not observed such offset in T. spp. for reasons that are unclear. The fact that this revises our previous interpretation based on a lower resolution map of T. spp. was already mentioned in the initial submission but is now better emphasized (lines 171-172 & 179-181).

• The authors conclude that T. mirabilis cartwheels lack a CID and instead have a filament-like structure (FLS). I wonder whether it is more likely that the FLS is really a highly derived CID that appears to be structurally distinct when analysed in this way, but that will ultimately have a similar molecular composition. This situation might be analogous to the central tube in C. elegans, which by EM appears to be distinct from the central cartwheel seen in most other species, but is of course still composed of Sas-6. This historical tube/cartwheel nomenclature is now cumbersome to deal with, so perhaps it would be better to be cautious and not give the T. mirabilis structure a completely new name-how about "unusual CID" (uCID).*

We share the view that the CID and the “FLS” –the term used in the initial submission- may have a related molecular composition and function, as we had also speculated in the discussion of the original submission. Following the reviewer’s suggestion, and in an effort to have a more uniform nomenclature, we propose to dub the T. mirabilis structure “filamentous CID” (fCID). This highlights better the similar location of these two entities and their potential shared function, while stressing the filamentous nature of the fCID. We further emphasize this point by providing the new Figure 6A to compare the presence of the two entities in select species. The discussion has also been adapted accordingly (pages 13-14).

Rebuttal Figure Legends

Rebuttal Figure 1: Re-classification of major classes

(A-D) Transverse (top) and longitudinal (bottom) views of T. agilis (A, B) and T. mirabilis (C, D) central cartwheel 3D maps. The final major classes reported in the manuscript (A: 55 % class, C: 64 % class) were subjected to re-classification, which again yielded one major class in each case, with no notable improvement (B, D).

Rebuttal Figure 2: Reclassification with non-overlapping sub-volumes

(A-F) Transverse (top) and longitudinal (bottom) views of T. spp. (A, B) T. agilis (C, D) and T. mirabilis (E, F) central cartwheel 3D maps. The final maps reported in the manuscript (A, C, E) were generated with a 25 nm step size, yielding overlapping sub-volumes, whereas the maps in (B, D, F) were generated from non-overlapping sub-volumes, with no notable differences between the two that would affect the conclusions of the manuscript.

Rebuttal Figure 3: Polar centriolar cartwheel upon sub-classification

(A-C) 3D transverse views of non-symmetrized STA centered on the spokes to jointly show the central cartwheel and peripheral elements in the T. agilis 45 % class (A), as well as separately in the 25 % class (B) and 20% class (C). No notable differences are apparent following such re-classification, apart from the output being noisier due to the lower number of sub-volumes in each sub-class.