Reviewer #3:

The manuscript "Decision making in auditory externalization perception" aims to identify cues that create/hinder an auditory externalization percept by using a template-based modeling approach. The approach as well as the findings are very interesting, and the study is thoroughly conducted. However, the manuscript adds little new knowledge to the field. Furthermore, a critical discussion is missing. The authors use a template-based model, but do not discuss the possible problems with such an approach. Particularly as each condition uses another model fit. This potentially allows the model to use cues that the auditory system cannot or does not consider. Nevertheless, the approach can still teach us which cues are potentially important for auditory externalization.

1) The title seems inappropriate as the main work seems to be on the identification and combination of cues for externalization but not on the decision making.

2) The model needs a more detailed explanation in the introduction. Otherwise the result section is not understandable without consulting the methods section.

3) Add a Discussion on template-based models and fitting conditions. The risk of mathematical inspired models is that features are exploited that the auditory system cannot access. A more sophisticated front-end than a gammatone filterbank might reduce this risk. Alternatively, the use of physiologically inspired front-ends as in Scheidiger et al. (2018) might be interesting to consider. Nevertheless, I acknowledge that some of the features used in this study are backed by physiological and psychoacoustical studies.

4) It is known that the monaural spectral shape is important for externalization, for example from the studies that you have used. Thus, I partly question the novelty of the findings.

5) I am not too familiar with template based models but I wonder if there is a problem if you use your models to fit and test with the same datasets?

Reviewer #2:

The current study compares four decision rules, factoring in seven potential acoustic cues, for predicting perceived sound externalization for single-source binaural sound with stationary interaural cues. Test stimuli included a harmonic vowel complex, noise and speech. Results show that monaural and binaural cues shape externalization. However, how listeners weighted these cues varied across the tested conditions. The authors consider the fact that some of these cues covary acoustically, by additionally testing their model on subsets of two of these cues only. No single externalization cue emerged as a clear predictor for perceived externalization. However, overall, a static cue weighting strategy tended to outperform dynamic cue weighting for predicting externalization.

Major concerns dampen enthusiasm for the current work.

1) It is unclear what neural mechanism is being tested. A premise of the current approach is that perceived sound externalization is primarily driven by acoustic cues. However, we know this not to be true. Context matters. As pointed out by the authors (l370-372), when listening to sounds processed with head related transfer functions (HRTFs) over headphones, listeners can externalize sound better when the context of the test room matches the room where HRTFs were recorded (Werner and Klein 2014).

2) Most external sounds are neither anechoic nor stationary. Therefore, any neural decision metric on externalization must have been shaped by lifelong experience with dynamic, reverberant cues for interpreting externalization. The current work mostly models stationary single source sound that was either anechoic or mildly reverberant, providing pristine spatial cues. I do not follow the author's point that this would not matter (l498-502): "While the constant reverberation and visual information may or may not have stabilized auditory externalization, they certainly did not prevent the tested signal modifications to be effective within the tested condition. In our study, we thus assumed that such differences in experimental procedures do not modulate our effects of interest." That is an untested assumption.

3) Many of the current test stimuli are perceived as ambiguous - providing 50% externalization ratings - and thus do not provide a sensitive test of brain mechanisms of sound externalization.

4) Reverberation enhances perceived externalization, but this cannot be predicted by any of the tested decision metrics which only consider stationary monaural or binaural cues.

On balance, this reviewer is unconvinced that the current work will generalize to realistic dynamic and reverberant conditions.

S. Werner and F. Klein, "Influence of Context Dependent Quality Parameters on the Perception of Externalization and Direction of an Auditory Event," presented at the AES 55th International Conference: Spatial Audio (2014 Aug.), conference paper 6-4.

Reviewer #1:

I agree with the authors that the question at the basis of this work is timely and important both from the point of view of understanding auditory perception and for informing technology. However I am not convinced that the findings here will necessarily generalize to other stimuli/listening situations.

I think the biggest limiting factor here is that the primary data on which the modelling is based are drawn from many different studies which used different stimuli, different tasks, different presentation environments and different equipment). I can see how testing the model on existing data is an important first step, but I would think that a critical next step is to form a set of (contrasting) predictions to be tested on a single stimulus set, within a single group of participants, as a way of confirming model validity. In this experiment I would also avoid using static non-reverberant environments since we know that these factors greatly affect spatial perception.

Other comments:

1) The title greatly overstates the main findings, it would be toned down.

2) Intro, line 30-33 this statement is misleading. As written it appears to claim temporal aspects of auditory perception are based on short term regularity, whilst spatial perception is based on long term effects. This is not correct see e,g Ulanovsky 2004.

3) As a reader not highly familiar with the auditory spatial processing literature I found the results section very dense and hard to follow. If you are targeting a general audience it is important to clarify concepts, avoid using abbreviations where possible etc.

4) When discussing the various decision strategies which you tested, consider explaining how they might be implemented by the auditory system, at which stage of processing etc.

5) It is very difficult to evaluate your results without more information about the stimuli and studies from which they were taken. Whilst you do provide references, I think the paper would be much clearer if you provide a more complete description of the stimuli (even in table form; paradigms etc).

Preprint Review

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Summary:

As you will see the reviewers agreed that the premise behind this manuscript is important and timely both in the context of basic auditory science and for informing technology. However, they raised largely consistent concerns about the generalizability of your observations to other auditory stimuli and to more naturalistic listening conditions.

Reviewer #3:

In the manuscript by Miné-Hattab et al the authors revisit a phenomenon that has been extensively studied for over 10 years: the subdiffusive and diffusive properties of DNA damage binding factors in repair foci (inside and outside of foci). The work is carefully done and brings a few observations of interest, but the novel insights are extremely limited. The most original aspect is that they characterize the movement of repair molecules within the focus with movement of the focus itself (the movement of foci has been done by many and turnover of factors has also been done by many). That they compare the two with one set of measurements is the key contribution of the paper, and they do find differences in diffusion coefficients. It is likely that this was not done previously. It is difficult to judge, as key papers that showed similar conclusions or datasets are not cited.

Here are a few key examples:

1) In the last year the Haber lab published a very similar study in Plos Genetics (Live cell monitoring of double strand breaks in S. cerevisiae, Waterman et al 2019 https://doi.org/10.1371/journal.pgen.1008001 ). Although they tracked Ddc2 and Rad51, they also looked at the behavior of separate foci and this paper is not even cited. The data should be compared at the very least.

2) The characteristics of 53BP1 foci have been extensively studied by many labs including those of Altmeyer, Scherthan, DeLange and others, with very similar findings as Miné-Hattab reports for Rad52 (for example, Phase separation of 53BP1 determines liquid‐like behavior of DNA repair compartments, Kilic et al., EMBO J. 2019 38(16): e101379; Live Dynamics of 53BP1 Foci Following Simultaneous Induction of Clustered and Dispersed DNA Damage in U2OS Cells Alice Sollazzo et al., Int. J. Mol. Sci. 2018, 19, 519 as well as the single molecule work of the lab of Eric Greene). Moreover both rad52 and PCNA foci were studied by Essers et al. (Kanaar and Vermeulen) MCB 2005. 25(21): 9350-9359 and EMBO J. 2002 Apr 15. Comparisons with these studies needs to be made.

3) A number of earlier studies followed Rad52 foci in budding yeast on induced double strand breaks (even using the I-Sce1-cut system used here) that are not taken into consideration. The diffusion coefficients presented here have to be compared with these earlier studies and differences should be resolved by comparing techniques and conditions of imaging. For instance, Dion et al., Nature Cell Biology 2012).

In brief, while the execution and analysis of the data shown here is very good, without direct comparison with other data sets, it is difficult to see exactly where this paper goes beyond published studies. This is especially crucial as the paper as written makes no effort to compare their data with existing datasets. Most specifically a comparison with LLPS as defined for other chromatin-foci forming proteins in the nucleus needs to be done - particularly addressing studies in mammalian cells concerning 53BP1 and other repair factors. This, plus a careful comparison with data from induced Ise1-break movement, must both be included. Finally, insufficient data are provided to draw conclusions about whether or not the authors' observations are reflective of phase separation. Additional mobility studies in conditions that disrupt LLPS are needed, both for the individual protein and for the foci. In conclusion, serious revision is needed and an effort must be made to show to the reader that this data is comparable (or not) with other data in the literature.

Reviewer #2:

Miné-Hattab et al. conduct a study focusing on the behaviour of the DNA repair protein Rad52 at sites of DNA damage in budding yeast. Several DNA repair proteins, including yeast Rad52, have been previously observed to phase separate at sites of DNA damage in a number of organisms. However, the authors here aimed to more accurately consider the potential phase separation behaviour of Rad52 by using single particle tracking (SPT) and Photo-activatable Localization Microscopy (PALM). Overall, the findings are consistent with previous studies and provide additional evidence supporting the concept that Rad52, but not the ssDNA-binding protein RPA, phase separates at the site(s) of DNA damage. The data shown also support the long-appreciated concept that different DSB sites cluster within the nucleus, albeit this study presents higher resolution data. The study falls within an important area of investigation.

1) The study does not present a novel conceptual advance.

2) What is the evidence that the biophysical properties observed are of direct relevance to DNA repair? For example, is the mobility of Rad52 within the repair focus important for repair? Is the difference in diffusion kinetics within and outside of the repair focus important for genome stability? What could the authors do to alter that diffusion profile and what would be the consequence on repair? Also, addressing this point implies the need to use a more physiologically relevant system with repairable DSBs, and not the irreparable DSB system used here. The authors describe the work of many in the field as "extremely phenomenological", yet it is not clear what the authors did to go beyond such a statement.

3) Overall, the statistical significance of most of the presented data is either lacking or unclear. This needs to be carefully addressed.

4) It is unclear if the 'absence of DNA damage' condition discussed in the first section of the results is the non-induced version of the system described in the second section of the results. Also regarding these sections, it seems that the 'absence of DNA damage' control conditions were not conducted as part of the same experiments with the I-SceI DSB.

5) Several statements made are not supported by the data and without clearly stating that the statements represent speculations. E.g. page 4, longer tail is due to Rad52 molecules diffusing slowly inside the focus; page 8, observing the 2 populations also in G1 does not necessarily mean that the 2 populations in S/G2 do not reflect replication forks at all. The authors need to carefully revise their claims/statements and consider alternative explanations. Also, the writing is often unclear or confusing and the authors should consider substantially revising it to clarify their claims, clearly indicate speculations that are not supported by the data, and make the text as accessible as possible to non-specialists.

6) How do the authors reconcile previous findings indicating that recombinant DNA repair proteins phase separate in vitro with their claim that "Rad52 acts as a client of the LLPS but does not drive its formation" on page 11?

7) How was the cell cycle stage determined?

8) Fig S1 data appear to show the existence of a partial loss of Rad52 function in the Rad52-Halo cells. This should be clearly expressed in the results and consequent limitations/caveats discussed. Also, please clarify whether Fig S1 shows the viability of Rad52-Halo cells in the presence or absence of JF646.

9) Regarding the possible categories of traces evaluated, one category is not included in the study. The surface tension that defines LLPS-dependent bodies is known to both help maintain focus integrity and partly counter LLPS body fusions. So if the foci represent true phase-separated bodies, have the authors then observed traces where Rad52 molecules interact with yet fail to enter the larger Rad52 foci?

10) The authors present no direct evidence for an "attractive potential" that drives molecules towards the centre of the focus. For example, what if the 'attractive potential' is simply the focus' boundary surface tension creating a barrier against which some of the molecules inside the focus bounce back towards the centre of the focus?

11) Consider revising the discussion to shorten it while making it more focused on conceptual advances and higher level interpretations, without re-describing the results in detail.

12) Can the authors visualize the fusion of the Rad52 foci/DSBs in live cells within their experimental systems?

13) The authors state on page 10 that "Here, we found that upon different levels of Rad52 over-expression, the background concentration increases (Figure S8) suggesting that Rad52 might not be the driving molecule responsible for the LLPS formed at the damaged site." Can the authors explain the logical transition here more clearly, it was unclear.

Reviewer #1:

In this manuscript by Mine-Hattab and colleagues, the authors use single-molecule tracking in yeast to dissect the formation of the double-stranded break response in living cells. Specifically, they try to determine the nature of Rad52 clustering at the DSB focus. The sequential recruitment pathway is well-studied in yeast (RPA --> Rad52 -->Rad51), and the inducible I-SceI break offers a controlled system for DNA damage. Moreover, yeast could be an excellent model system to elucidate if there is any conservation or function for such compartments. Overall, I found the data and the subsequent analysis to be both rigorous and nuanced. Ultimately, one is trying to distinguish whether the focus is due to a clustering of binding sites or liquid-liquid phase separation, or perhaps some combination of the two. I feel the story falls short of providing a definitive answer, as do many in this field, but the authors conclude that the preponderance of evidence points to a LLPS model for Rad52 clustering.

1) How is it possible to distinguish a cluster of binding sites from liquid-liquid phase separation? To this referee, that is the question that needs answering. In the absence of breaks, there are two Rad52 diffusion populations (D= 1.2 and 0.3 um2/s), which the authors attribute to monomers and multimers. They don't verify these multimers by alternative approaches (say number and brightness analysis), but it seems like a reasonable possibility. After a break, a third component - slower than the previous two --becomes evident. This slow population coincides with the break. In the vicinity of the break, there is now only 1 component diffusion (D=0.03 um2/s). Also, the motion is now more confined, but not absolutely so. Also, Rad52 diffuses faster than Rfa1, which is bound to ssDNA. At this point, there is no data to distinguish between two possibilities: slow diffusion or diffusion + binding. Except, if it were diffusion + binding, one might perhaps expect to still see the free diffusion component. However, I can imagine lots of different scenarios and a range of binding affinities and multimer states that would make that analysis an unholy mess.

The authors then turn to diffusion at the boundary (Fig. 5), which I agree can be a more informative measure. Here, they see changes in the diffusion estimator for trajectories which cross the boundary, using displacement which they argue is more robust for slow diffusion. The problem is that the 'boundary' is determined by the very thing they are trying to measure, not some independent marker of the compartment. In other words, Rad52 defines the compartment, unless I missed something fundamental in the experimental design. Ideally, the way such an experiment would be done to test the hypothesis that Rad52 is forming a LLPS compartment is to look at the diffusion of an inert tracer as it comes in and out of the compartment. As designed, I frankly do not see how the observation of different diffusivities in and out of the compartment distinguishes between a cluster of binding sites and an LLPS. If you accept that DNA-binding is in no way biasing the kinetics, then the authors' interpretation seems like the most sensible one. But the fact that Rad52 is involved in DNA repair makes that a hard assumption to swallow.

Furthermore, I'm not sure I entirely grasp the significance of Fig. 6. Since Rad52 can easily escape one focus and enter another, regardless of whether it is a cluster of binding sites or a phase, I don't see how the radius of confinement measurement distinguishes between these two alternatives. The observation that the foci are 2x larger in diploids but at similar density is compelling, although recent data from the Brangwynne lab point out that conserved density need not be the case (PMID: 32405004).

2) In the syntax of this paper, Rad52 is a client in the LLPS, leaving the question of the scaffold unaddressed. After all, the Rad52 focus ultimately disappears, meaning that something caused this phase to be dispersed. So is RPA the scaffold? It might be possible to address both points 1 and 2 by knowing what is responsible for forming the LLPS in the first place.

In summary, I found the paper to be balanced and rigorous when exploring possible interpretations of the data. Although the authors may feel the preponderance of their data is consistent with LLPS, I don't feel they have nailed it. It's hard to identify a smoking gun. Of their four observations in the discussion only the second is direct, and that observation may have other explanations. However, I am not sure what experiment to recommend which would be definitive. Such is the nature of this field.

Preprint Review

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This manuscript is in revision at eLife

Summary:

In this manuscript by Miné-Hattab and colleagues, the authors use single-molecule imaging approaches to investigate local dynamics of Rad52 foci at DSBs in budding yeast, which is an important area of investigation. They show that the dynamics of Rad52 molecules inside foci are consistent with protein movement within LLPS domains, while Rfa1 dynamics are not. Their data also provide supporting evidence to previous observations that repair sites cluster within the nuclei, and suggest that clustered foci behave as larger phase separated structures. While the idea that Rad52 and other repair proteins form phase separated domains is not novel, this study presents higher resolution data in support of this model. The reviewers generally agree that the study is interesting and well conducted, but the conceptual advancement is limited. Specifically, more convincing experiments demonstrating that the observed Rad52 dynamics reflect LLPS are required. Evidence that the dynamics are relevant for DNA repair and genome stability should also be provided. Additionally, the study should be better integrated with previous studies, statistical analyses need to be more rigorous/better presented, and the text should include a clearer separation between observations and speculations.

Reviewer #3:

This study uses Bayesian inference to estimate the probability of detecting a malaria case and distribution of malaria cases using different surveillance methods in a district in Palawan, Philippines. The authors show that detection of malaria cases depends on household location and cannot be explained by distance to the health centre alone. They also argue that in low endemic settings it is economical to screen health care attendees stratified by their environmental risk (here, 100m proximity to closed canopy forest). The integration of unique high-quality spatial and molecular datasets is compelling. The authors argue that integrating remote sensing into triage for enhanced molecular detection of malaria could be economical in these settings.

Major comments:

1) The explanation of the modelling framework is, as written, hard to follow and reproduce. Examples of where authors could improve clarity: the equations throughout use the same notation to mean very different things (si = patent infection (L380) or diagnostic sensitivity (L394)). The statement '𝑿𝑖𝜿 represents a vector of covariate effects' L383 does not make sense. Is X a specific location and 𝜿 the covariate estimate? It is difficult to understand how models were created and evaluated. The level of detail in the spatial data (Table S1) is insufficient for reproducibility, but could be easily amended to do so. Table 1- can authors list the actual range of these covariates before they are mean-centered and scale. Contextualizing the fixed effect estimates (i.e. distance to a closed canopy forest) is difficult to interpret given that no mean or sd of these distances are given (at least not that I could find).

2) Terminology changes throughout the manuscript, making things difficult to follow. For example, surveillance method 1 is referred to as passive case detection (Line 126), existing passive surveillance systems (Line 131), standard PCD (Line 137). Although one can assume these are all the same, it would help to use consistent terminology for this throughout. Convenience sampling is used throughout, but it's unclear if this is distinct from enhanced surveillance.

3) This is mentioned in the limitation section, but I don't think it gives a sufficient explanation. One benefit of the R-INLA framework is that it can account for spatio-temporal data - why was time of year and temporally relevant environmental characteristics not examined?

4) The authors don't provide convincing evidence that integrating remote sensing into this setting would actually add value. Could health care workers not ask residents if they live next to a big, closed forest? Wouldn't this achieve the same outcome? Wasn't it already known that frontier malaria was a problem here?

Reviewer #2:

This is an interesting analysis and it is great to see a modelling analysis that has the potential to directly influence programmatic decisions. The idea of using remotely sensing data to stratify surveillance or diagnostic practices is interesting and scalable. The analyses are clearly described, and I found the use of the probability of detection metric particularly relevant to the types of decisions being made in pre-elimination settings. I have a few minor comments and would be curious if some discussion could be added to how this may be applicable to settings outside of SE Asia.

Reviewer #1:

In 'Disentangling fine-scale effects of environment on malaria detection and infection to design risk-based surveillance' the authors analyze data from the Philippines to investigate the utility of landscape data to inform risk-based surveillance programs. The authors use occupancy modeling, a common approach in ecological studies, with health facility data (that combine both passive case detection via microscopy and RDTs with molecular approaches) to analyze the effectiveness of surveillance systems to detect malaria cases. Using cross-sectional surveys based at health facilities and the residence location of sampled individuals, the authors work to develop a method to detect locations with malaria infections. They find that in highly forested areas, there is a higher proportion of infections only detectable by molecular methods.

In general, the authors provide a fine analysis. However, the novel aspects or new insights of this approach are unclear. The authors use a common standard statistical approach, although less common in epidemiology it is very common in ecology, to analyze fairly commonplace data. Their findings are in line with our existing knowledge of issues with enhanced (i.e. molecular) versus standard (RDT, PCR) and ability for ecological/landscape data to help improve surveillance systems. For example, it is not novel that enhanced surveillance would identify a wider spatial distribution than passive case detection since this method should identify more infections. Further, integrating landscape or geographic data to inform risk-prediction is commonly used for malaria or other vector-borne diseases that have an environmental component.

Major comments:

The authors do not provide adequate background on the setting, biases in the data used, and impact of health seeking behavior on their results. The authors find that the detection probability was negatively associated with travel time to the health facility. However, they do not elaborate upon whether this might be true or if health seeking biases from individuals who are from more forested areas and traveling to health clinics. In addition, the authors only analyze a single year of data which prevents any temporal trends to be analyzed or more robust analyses to be performed.

One of the key findings is that the cost per infection detected is less expensive using a risk-based surveillance. However, how do the authors suggest this would be actionable? What strategies would be done to follow-up these infections? Since these results are not about incidence or prevalence, just the presence or absence of at least one case of malaria in a location, how would this be translated into practice? In addition, is it reasonable to assume that molecular diagnostics would be deployed to these types of health facilities? It is already well known that passive case detection is less costly than molecular detection.

The authors do not elaborate on the implications of identifying additional locations where there is a larger proportion of sub-patent infections. Although the overall finding that infections only detected via molecular approaches are more common in forested areas, it is not clear how this would help the program. In addition, the primary outcome measure is the presence or absence of a malaria infection in a location. This is not a common outcome measure and further analyses of how this type of measure would be used and interpreted are needed.

Preprint Review

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Reviewer #3:

The authors have used a number of different experimental approaches to investigate the actions of LPS (as a model for inflammation) on modifying GABAergic inhibition in the medial prefrontal cortex (mPFC). They conclude that the inhibition of pyramidical neurons is selectively enhanced by the subsequent upregulated levels of GABAAR subunits, glutamine synthetase (GS) and vGAT, and downregulated BDNF and pTrkB levels as a result of microglia activation. Unfortunately the authors use a number of different approaches that preclude comparing results because of the different experimental conditions. For example, IP injection of LPS 2 hours before recording from acutely prepared brain slices is not necessarily comparable to a 20 min bath application of LPS directly onto brain slices. The entry of LPS directly into the brain is likely to be minimal and is not equivalent to the bath application of LPS. In addition, the attenuation of the "sickness behavior" after LPS injection and the attenuation by minocycline (Fig 7) is a fairly old story well studied by Dantzer's group (e.g. PMCID: PMC2683474) and previously shown to be blocked by minocycline (Henry et al 2008 PMID: 18477398).

There are discrepancies in the methods descriptions and details about the conditions. Technically some of the recordings aren't whole cell patch recordings because the pipettes contain gramicidin indicating that these were perforated patch recordings. However it is uncertain which recordings are obtained using perforated patch approach. The authors don't provide enough information on the evaluations of the perforated patch recordings to ensure there were no access resistance problems. In addition there are two different pipette solutions described in the methods. This has to be clarified. The authors also do not provide information on when the animals were sacrificed after the LPS injections and slices were obtained.

Finally the authors describe the actions of BDNF on LPS application on brain slices not on the LPS injection into the animals. They also mention two different concentrations. I am not certain the effects of LPS injection IP in the awake animal are equivalent to the LPS application for 20 min prior to BDNF. Page 6- I don't think the acute application of LPS onto inhibitory interneurons is equivalent to the effects of LPS injection in the whole animal and the preparation of slices leading to recordings from pyramidal neurons. These experiments are unconvincing and would have to be conducted under similar conditions for comparisons to be made.

The authors puff supernatant extracted from PFCs and compare +- LPS. They find a higher amplitude current from the LPS treated mice and interpret this as indicating a higher GABA content. This is insufficient evidence as there are other components in extracts such as this and the authors have no evidence using GABA antagonists that these currents truly are due to GABA-A Cl- channels.

Reviewer #2:

The manuscript by Tang et al 2020 entitled "Microglia activation leads to neuron-type-specific increase in mPFC GABAergic transmission and abnormal behavior in mice" investigates how changes in inflammation acutely modify GABAergic neurotransmission in the medial prefrontal cortex. The authors provide evidence that 2h-post LPS systemic injection (i.p.) leads to enhanced mIPSC amplitude and frequency and upregulation of GABAaR, vGAT, and GS protein levels. In addition, BDNF application or pre-treatment with minocycline prevents aberrant GABAergic transmission following LPS exposure. They conclude that microglia are responsible for these changes in neurotransmission. The experiments are generally well-done and the manuscript was nicely written and easy to follow. However, there are significant concerns related to the interpretation that this is a microglial effect. Above all, LPS and minocycline are very blunt and not specific to microglia. Besides their effects on the peripheral immune system, which could also affect the brain, they can also directly affect other cell types in the brain (neurons, glia, vasculature, etc.) in addition to microglia. Therefore, it cannot be concluded, without more cell-specific manipulations, that the effects are attributed to microglia. Other concerns are detailed below:

1) Are changes in neurotransmission restricted and specific to the mPFC or is this a more global disruption in neurotransmission due to full body systemic inflammation?

2) The indicators of microglial activation by immunostaining for Iba-1 and measuring soma size are fairly superficial. More in-depth molecular analyses with more microglia-specific markers would be more informative.

3) GFAP does not label all reactive astrocytes and is therefore not the best indicator of changes in reactive astrogliosis. The authors should include additional markers in their analysis outlined in Liddelow et al. Nature 2017.

4) Behavioral changes, which are largely locomotor, within 2 h post-LPS are more likely a sickness behavior rather than a specific effect of changes in neurotransmission in the mPFC.

5) It is unclear what specific pyramidal neuron population are being recorded in the mPFC. Specifying the layer would be informative.

6) The authors attempt to link the results with BDNF application with a microglial affect. This link is not particularly strong. While there are studies demonstrating microglial BDNF can affect circuits, the majority of BDNF is made by other cell types in the brain, not microglia. Without cell-specific manipulations, the authors should tone down this link.

7) Experiments displayed in Figure 4 should include a minocycline-only condition.

8) It would be informative to perform electrophysiological recordings on organotypic slices treated with minocycline followed by +/- acute LPS treatment.

9) The authors use an interesting method whereby they puff lysate from control and LPS brains to assess the impact on e-phys recordings. Due to the increased inhibitory transmission, the authors conclude that there is increased GABA content. However, it seems there could be other explanations such as other neuroactive factors, including cytokines, that could potentiate GABA transmission. Measuring GABA by, for example, immunohistochemistry could help to address this concern.

10) In several western blot panels the bands are saturated and are, thus, not ideal for use in quantifications.

11) The increase in GABAaR, vGAT, and GS at the protein level within 2 h-post LPS treatment is quite rapid and more typical of immediate early genes (e.g. c-FOS, Arc, etc.). Could the authors comment on this in the manuscript?

Reviewer #1:

In this manuscript, Drs Tang and colleagues study how inhibitory synapses are modulated upon intraperitoneal injection of LPS or upon direct application of LPS onto acute slices. The manuscript could certainly be strengthened by addressing the following points, which are all related:

1) The authors seem to consider that microglial "activation" identified by a morphological modification and enhanced Iba1 signal is an homogeneous all-or-none state that can be reached or blocked by different stimuli. Therefore, they compare the result of an "activation" by a 2h intraperitoneal (ip) injection of LPS with a direct 10 min application of LPS onto acute brain slices. However, it is now acknowledged that different stimuli induce different microglial phenotypes (Perry et al. Nat Rev Neurol 2010, 6:193) that may not be comparable. LPS binds to TLR4 protein which is expressed by microglia in the brain, but also by peripheral immune cells such as macrophages. The effects of ip injection of LPS might thus be due to microglia (if LPS pass the blood brain barrier), and / or to an indirect effect of peripheral immune cells activation. The effect of LPS application on acute slices is directly due to the binding to microglial TLR4. At this stage, it seems not possible to rule out the possibility that a signaling molecule coming from the periphery could both activate microglia and modulate inhibitory synapses (see point 2). It is therefore not possible to claim (as in the title) that activation of microglia results in the increase of GABAergic transmission.

2) The authors propose a role for BDNF based on the decrease of BDNF in 2h LPS mice observed by WB (figure 4D). However, they have focussed their WB analysis on this protein and have not examined any other signaling molecules. In figure S3, they showed that LPS increases the mRNAs encoding TNFα, IL1b and IL6. How can they exclude that these proteins are involved in the activation of microglia of microglia and upregulation of GABAR?

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. Gary L Westbrook (Oregon Health and Science University) served as the Reviewing Editor.

Summary:

The impact of neuroinflammation on brain circuits is an important topic. However, all reviewers had significant and overlapping concerns and were not convinced that the data adequately supported the authors’ conclusions.

Reviewer #2:

The manuscript lacks a clear hypothesis/message. It is ultimately descriptive and adds very little to our understanding of the role of immune mechanisms in the development of tissue fibrosis (including pulmonary fibrosis). Detailed profiling of the immune populations in the context of the bleomycin-induced fibrosis model has been reported previously (Tighe et al., AJRCMB, 2011, PMID 21330464). Similarly, results of the spatial analysis are also not surprising: the authors used the lung injury model and found an accumulation of the recruited immune cells in the areas of injury/fibrosis. Moreover, spatial methods are lacking appropriate rigor necessary for quantitative assessment (i.e. stereology, see Hsia et al., AJRCCM, 2010, PMID 20130146). As a machine learning methods paper, it also lacks novelty (several dimensionality reduction techniques plus random forest classifier) and not validated using external datasets.

Reviewer #1:

This paper uses multiple approaches to study the cellular dynamics of murine bleomycin lung injury as a model for human IPF. Multiple techniques are used for this purpose including multi-parameter flow, histology, data reduction technique, comparative analysis between BAL and lung, non-linear mixed modeling and immunohistochemistry. The results are interesting and propose a staged inflammatory response leading to IPF like pathology. However, the data is very descriptive and does not test a specific hypothesis. In particular, the results do not suggest a particular therapeutic strategy. Addition of a targeted intervention to the experiments would enhance the impact of the work.

Preprint Review

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Summary:

The manuscript uses a large temporal immuno-phenotyping dataset in the broncho-alveolar fluid and lungs of mice given bleomycin, so as to enable the modelling of the localised progression from innate to adaptive inflammation and subsequent fibrosis. While this is an immense amount of work and the analysis is interesting, the concerns regarding rigor in spatial quantification and the primarily descriptive nature of the work make the resultant insights, mechanistic or translational, somewhat too limited for a cross-disciplinary readership.

Reviewer #3:

Luyten et al's study examines the phenomenon of drug-induced post-retrieval amnesia for auditory fear memories in rats, and report that after several experiments using Propranolol, Rapamycin, Anisomycin or Cycloheximide that they essentially observe no disruption of reconsolidation, (i.e., no amnesia). This is a well-executed, written and meticulous study examining an important phenomenon. The author's lack of observing amnesia using these "reconsolidation blockers" highlights an important fact that systemic administration of these drugs at the time of memory retrieval may not robustly influence reconsolidation processes despite what the existing literature may collectively indicate. The author's data clearly indicate this point and it is important the scientific community be made aware of these difficulties in blocking reconsolidation using systemic administration of these drugs.

This group has previously published similar studies disputing similar phenomena. First highlighting a lack of amnesia following the reconsolidation-extinction paradigm and then more recently demonstrating a lack of amnesia attempting to block the reconsolidation of context fear memories. This is now their third installment focusing on Cued fear memories. Certainly, these findings are important, but arguably the novelty of such findings may be diminished a bit. In one of the "control" experiments where the experimenters administer anisomycin immediately post training, they observe a paradoxical result - they observe memory strengthening instead of the expected blockade of consolidation and amnesia. This result highlights a number of things to consider when we interpret these overall results. For one protein synthesis inhibitors(PSIs) are toxic and when administered systemically usually result in inducing the animals to have diarrhea and generally just makes them sick. This of course will make the animals stressed and agitated and result in increasing their stress and likely amygdala activity. All of this could likely be the reason why the animals exhibited memory strengthening or no impairment in consolidation even with a PSI on board. See PMCID: PMC7147976. Figure 6. In this study, they could rescue the impairment of PSI on consolidation by increasing BLA principal neuron firing. Thus an important take away is something like this could easily be happening in the reconsolidation experiments - that there is no blockade because the animals are stressed either due to PSI on board or because some issues with experimenter/animal interactions, etc lead to higher BLA neural activity and rescue of the reconsolidation process.

I don't think the authors go far enough articulating the important differences between systemic and intra-cranial administration of these drugs. Time is a potential factor. Immediate administration of the drug at high concentration in the target brain region (BLA) versus many minutes until the drug gets to the target region with uncertain concentration levels that may not mirror levels reached with intracranial administration. It's unfortunate the authors were not able to include intra-BLA administration of these drugs in this study. I do not necessarily expect them to do such experiments, since they have already done so much and it is not clear the laboratory has the appropriate expertise to conduct such experiments, but this comparison would be helpful.

I think it is important that the authors make some statement of training conditions on cannulated versus cannulated rats. For example, every animal in Nader's 2000 study was bilaterally cannulated targeting the BLA. In contrast every animal in this study underwent no such surgery. I think this is relevant. In my experience non cannulated animals are a bit smarter than cannulated animals and the training conditions across these two differing groups may not equate to the same level of learning. And of course, differences in learning levels can lead to differences in the ability of the retrieved memory to destabilize. The authors mention possibly examining markers of memory destabilization. GluR1 phosphorylation, Glur2 surface levels, protein degradation/ubiquitination have all been used to assess if destabilization has occurred. I do not fully agree with their reasons for not performing such experiments. They could examine some or one of these phenomena across differing training conditions between retrieval, no-retrieval animals. This likely could be informative. However, the authors may not possess the necessary expertise to conduct such experiments, so I'm not stating these experiments need to be completed, but certainly the study could be strengthened with such data.

Experiment 3E - Propranolol without reactivation. I don't see any data for this on the graphs. Am I missing something?

The authors should probably cite this paper too, PMID: 21688892. The authors in this study find no evidence that propranolol inhibits cued fear memory reconsolidation.

Reviewer #2:

General assessment:

In this study, Luyten et al. aimed to replicate post-retrieval amnesia of auditory fear memories reported numerous times in the literature. They used a variety of behavioural approaches combined with systemic pharmacological treatments (propranolol, rapamycin, anisomycin, cycloheximide) after reactivation of fear memories. Interestingly, none of the treatments induced a significant decrease of freezing responses during subsequent retrieval tests. Authors strengthened their null results by using Bayesian statistics, confirming the absence of drug-induced amnesia.

Overall, the study is really interesting. Experiments and analyses are very well designed and bring some important findings to the debated topic of post-retrieval amnesia and its clinical relevance.

I have nevertheless several comments for the authors to consider.

-Despite being very detailed, the authors should clarify and uniformize their Methods section and Supplemental information (e.g. number of CS, contexts used...) to improve the understanding of the different approaches. Similarly, methods for the reinstatement protocol (Exp 2) are missing.

-In exp 5, tests 1 and 2 are supposed to have 12 CS each. However, only 8 dots are represented on the graph. Did the authors average some freezing values after the initial 4 first CS presentations?

-There is an obvious difference in baseline freezing response before the test in Exp 7 (Figure 5A-B). Discussion of these differences is an important point and was thoroughly discussed by the authors in the Supplement.

-Ln 384-387: "... additional Bayesian analyses were carried out that collectively suggested substantial evidence for the absence of an amnestic effect". Despite the "substantial effect" given by the meta-analysis, I am a bit confused by the meaning of an "anecdotal evidence against drug < control" reported in half of the experiments. How do the authors interpret these results?

-The effect of cycloheximide on memory consolidation is indeed unexpected. Even if beyond the scope of the current study, what is the authors' hypothesis to explain that cycloheximide in their conditions induced a pro-mnesic effects on the consolidation of fear memories but altered the consolidation of extinction?

-Cycloheximide seemed to induced post reconsolidation amnesia of fear memory after extinction training (Exp 8, Fig 3G) but not after single CS reactivation. Can the authors please develop this point? Is it possible that several presentations of the CS is required to destabilise the initial memory trace?

Reviewer #1:

This manuscript provides evidence that drug administration during a reconsolidation window does not necessarily prevent memory recall, as has been shown by many groups. The authors attempted to replicate several published experiments and despite demonstrating that the drugs had other effects on the animals' behavior and physiology (e.g. weight gain), no effects on memory were observed.

The paper is nicely prepared.

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 all found this thorough report of the failure to replicate drug-induced post-retrieval amnesia to be interesting and the work was viewed as scientifically sound. But they were all concerned that the extent of the advance is not to the level that would be expected. They also raised substantive concerns regarding the reasons for the failures to replicate.

Reviewer #2:

This manuscript concerns the application of a narrowed mass window DIA method for simultaneous detection of modified (methylated, succinylated, acetylated Arg and Lys) and unmodified peptides in the same MS run. The authors use a combination of synthetic peptide libraries and immunoaffinity enriched samples to compare the performance of several mass windows, ultimately showing improved separation of modified and unmodified (precursor) peptidoforms using a 4 Da separation window. They apply this method with a modified site localization algorithm to identify modification sites that are differentially affected by hypo- and hypermethylation potential in mouse NASH models. These studies reveal potential connections between SAM levels and methylation potential with mRNA translation and acetylation levels. Overall, this work presents a new methodology for simultaneous detection and quantitation of modified proteoforms without requiring parallel runs for enriched and unmodified protein detection. This methodology should be of interest to the proteomics community. Several of the mechanistic connections made in the NASH model are preliminary. There are several other aspects of the method presentation that should be addressed in the comments below.

Major Concerns/Comments:

1) The mechanistic jump from moderate alteration of methylation in three ribosomal proteins to causing decreased mRNA levels is not supported. The authors would need to add significantly more detail on where these modifications are and what quantitative changes are observed, as well as how these changes can affect the function of the protein of interest. Additionally, the claim that using the 4 Da DIA acquisition aids in understanding this mechanism should be expanded.

2) Similarly, the connections listed in the acetylation section are very tenuous. Specific proteins and deacetylases are listed and connected, but other relevant proteins that play redundant or counteracting roles are not considered. A more holistic presentation of sirtuins and hdacs should be included as they will collectively control the acetylation status. Finally, what is the conclusion of this section? That acetylation is lowered due to a series of effects leading to sirt3 mediated deacetylation? This should be supported experimentally if these claims are to be made.

3) Overall, the causal, rather than corrective relationships discussed on the sections focused on quantifying differential methylation/modification present in hypo/hypermethylated mouse models should be changed. For example, the authors make statements like "to determine the role that differential methylation potential plays in NASH...". The altered prevalence of sites is correlated with altered methylation potential, but these data do confirm they are playing a role in NASH. Statements like these should be adjusted.

4) Do the authors integrate information about cleaved peptides? This co-isolation issue is primarily an issue when exactly the same peptide +/- modification is close in chromatographic space. Yet the unmodified version of many of these target peptides will be cleaved by trypsin, creating a completely different peptide. How is this accounted for in data analysis?

5) The authors include a section on modifying the localization algorithm Thesaurus for the modifications studied here. Can the authors discuss these changes so the readers can assess whether these changes are appropriate and how they affect the altered performance?

Reviewer #1:

The manuscript by Robinson et al describes improvements to the DIA technique that are focused on enabling the quantitation of peptides bearing subtly different PTMs on lysine and arginine residues. The technique utilizes small DIA isolation windows to avoid co-isolation of precursor peptides whose m/z's are close (i.e. unmethylated vrs monomethylated or mono- vrs di-methylated, etc). The authors demonstrate that it can be utilized on unenriched samples which permits simultaneous assessment of changes to whole protein levels. Furthermore, they extend their localization algorithm (Thesaurus) to utilize these data and show POC by characterizing changes to PTMs in two mouse models of NASH.

The study represents quite a lot of work and it shows a high level of methodological sophistication, however it is quite narrow in scope. It will be of interest to mass-spectrometrists that utilize DIA, but not to a general audience.

Specific concerns:

1) The paper barely acknowledges the fact that peptides modified on lysine and arginine typically don't cleave efficiently with trypsin thereby resulting in missed cleavages. Thus most of the time it's quite simple to distinguish modified from unmodified without the need for narrow isolation windows.

2) DIA can be quite useful, but this reviewer cannot help but think that PRM might be more well-suited to detailed studies of peptidoforms with subtly different PTMs. If PRM is utilized, isolation windows can be as narrow as 1Da so the techniques employed in this manuscript are unnecessary.

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:

While the Reviewers were in agreement that your paper reports a useful method, they also felt that it was narrow in biological focus and of primary interest to those within the mass spectrometry-based proteomics community. The Reviewers also question whether the method offers substantial advantages over alternative approaches for analyzing Lys/Arg PTMs by MS-based proteomics.

Reviewer #3:

PREreview of "Analysis of receptor-ligand pairings and distribution of myeloid subpopulations across the animal kingdom reveals neutrophil evolution was facilitated by colony-stimulating factors" Authored by Damilola Pinheiro et al. and posted on bioRxiv DOI: 10.1101/2020.06.19.161059

Review authors in alphabetical order: Monica Granados and Katrina Murphy

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 8 people in total, including researchers from several regions of the world, a preprint author, and the event organizing team.

Overview and take-home message: Pinheiro et al. have made advances in understanding neutrophil evolution and receptor-ligand participation by using a wide range of relational taxonomic data to show how CSF1/CSF1R and CSF3/CSF3R pairings evolved and contribute to granulocyte adaptations. Neutrophils are the most prolific granulocytes of the mammalian myeloid cells involved in the immune response. The research team bridged the gap in our knowledge on how the receptor-ligand pairing signals of CSF1R/CSF1 helped with bone marrow development, where these short-lived cells are generated, and CSF3R/CSF3 signaled the maximum production volume of the neutrophils and their movement as both a cell population and a single cell for distribution. Although this work is of significant importance in the field, below we outlined some concerns that could be addressed in the next version of this manuscript.

Positive feedback:

-(The findings were) Super novel! I love the breadth of taxa that are covered.

-The intersection of cell biology and evolution is quite interesting!

-This preprint could be a great model for future research/analysis.

-The bolded subtitles for the different results sections were clear and helpful!

-Increased understanding in neutrophils is important because children with immature neutrophils end up with recurrent early-onset life-threatening infections, e.g. severe congenital neutropenia. The more we can learn about neutrophils the more we can take steps to fight this type of infection.

-I believe there is sufficient information in the materials and methods section to allow for the reproduction of the experiment.

-The format made sense and the flow could be followed.

-Cells have a tendency to call out domestic and evolutionary elements which are beneficial, so learning how receptor and ligand interactions evolve in different taxa is relevant.

-It's interesting that gene complexes are associated with specific morphological aspects (e.g. exotherms and endotherms); the gene expression is obvious.

-Figure 1 was cool to see. An expansion of Figure 1 might be of interest, where the phylogenetic tree changes over time to show the loss and gain of specific granulocytes.

-Gene sequencing data was pulled from NCBI Gene and Ensembl databases to create Figure 2a. This is a great example of having a very specific question/hypothesis that can be answered with existing data.

Can other types of physiology be tracked similarly in future research, e.g. scales, breathing - anything that could be mapped?

Are there other groups that could relate to metabolism e.g. brain studies?

It would be interesting to see the level of degradation, e.g. for fish - mapping physiology to a specific gene or brain size (the brain is more developed in different taxa).

-The preprint can be relevant for myeloid phagocyte development and across species geometric morphology/computational anatomy particularly as it can relate to brain structure and sizes. More genetic data across species and homologous brain areas is helpful.

-Overall there was a connection between the results and the research questions, yes, I would say the conclusions were supported by the data.

-Even though we don't have this specific field expertise, as a group, we recommend this manuscript to both others and further peer review.

Major concerns:

-Since this is a large selection of taxa groups, can specification (of a subset) be divided into more detail?

-Please note, taxonomy is not a field I am familiar with. It would be helpful to check the sequence conservation of the receptors across these taxa families and see whether there are any minor evolution instances where they mutated. If the receptors have mutated, do they have a particular residue that mutated?

Acknowledgments:

We thank all participants for attending the live-streamed preprint journal club. We are especially grateful for both the first author's contributions to the discussion and for those that engaged in providing constructive feedback.

Reviewer #2:

The article is well written.

1) Please provide a supplementary file containing all the references used for Figure 1b (complete blood count data; CBC). This would be a useful source of data for researchers interested in other blood cell types.

2) Regarding the CBC data - the authors should mention in the text if all the samples were obtained from adults. Whilst I appreciate that n are low for some species, do you obtain the same result if you analyse males and females separately? This may be worth mentioning given that neutrophil numbers have been reported to be higher in women.

3) Please provide a supplementary file containing all the NCBI gene and Ensembl accession numbers for each gene, in each species (Figure 2a).

4) The authors may want to mention that there are other receptors for IL-34 which may explain its expression (in fish, Fig2a) in the absence of Csf1r.

5) Please provide a supplementary file containing all the NCBI protein accession numbers used for Fig3a.

6) Please include isotype controls on histogram in Supplementary figure 1a, 1c and 1d.

7) Please include the full gating strategy for Supplementary figure 1a.

8) Why was 72h chosen for the mobility assays (Supplementary Fig 1b)? At this point, monocytes cultured in CSF1 would begin differentiating into macrophages, and this may affect their mobility.

9) Supplementary Fig 1c - please include the antibodies in the Lin cocktail for flow cytometry in the figure legend.

10) Please mention in text and figure legend that human blood was used (there is no mention of it within text).

11) Was a dead cell exclusion dye used for flow cytometry of human blood and neutrophils? And did you look at FSC-A v FSC-H to exclude doublets? If not, how can you exclude the possibility that the Cxcr4 hi neutrophils are not dying or doublets?

Reviewer #1:

Pinheiro and colleagues have described a fascinating view on the evolution of neutrophils and other myeloid cells. This is a very original and potentially important piece of work. To follow neutrophil evolution in the evolutionary tree through co-analysis of the expression of G-CSF/G-CSFR and M-CSF/M-CSFR in the same tree is smart and interesting. The article is not easy to read and some issues need some more clarification(s). So the article would benefit when (random order):

1) At several locations in the article the authors imply that G-CSF is inducing differentiation fitting with an inductive model (eg. introduction lines 41-51). At the same time the authors rightly mention the presence of mature neutrophils in G-CSF-/- mice (as well as mature eosinophils in IL5R-/- mice) more pointing at a stochastic model. This latter model assumes that expression of CSF-R's is more random, and only committed progenitors expressing these receptors will proliferate rather than differentiate in response to these CSF. Please provide sufficient arguments for the inductive model or change part of the interpretations when a stochastic model is more likely.

2) In the whole article data are provided on numbers in peripheral blood. Only a minority of myeloid cells reside in the blood, the majority is in the tissues. The situation with neutrophils is uncertain. Please discuss.

3) The part on C-EBP transcription factors is difficult to follow. Please help the reader understand why they are so important (based on KO strategies) while there is no clear picture in evolution as the genes are sometimes present, sometimes not. Some species have many, some only one. Simply stating redundancy in the system does not really fit the knock-out studies.

4) The part described in lines 372-409/Supplemental figure 1 is not adding much to the article. It is only human with no evolutionary perspective. Consider removing.

5) Please provide some more insight into the issue of eosinophils versus neutrophils. Now it is implied that the co-evolution with endothermia is relevant. Many articles suggest that eosinophils are more specialized in killing large targets (extracellular killing/e.g. parasites) vs neutrophils small targets (intracellular killing/e,g, bacteria). Can the authors provide their ideas about the functional difference of the cells in the evolutionary perspective.

6) line 466: it is stated that neutrophils comprise the largest population of myeloid cells in mammals. This needs supportive evidence, as macrophages are thought to be the largest population at least in the tissues.

7) lines 582 - 585. Although the issue of the lamins is well taken formal proof that the segmented nuclear morphology of neutrophils is important for movement and trans-cellular migration is yet to be determined (e.g. J Immunol January 1, 2019, 202 (1) 207-217; DOI: https://doi.org/10.4049/jimmunol.1801255 ).

8) Lines 61-64 young children with SCN often have mutations in the ELANE gene rather than the GSF-R gene. Can the authors discuss how ELANE fits with the model they are presenting?

9) Please provide the definitions of neutrophils and heterophils as they can be present as different cells in the same species.

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:

Pinheiro and colleagues have described a fascinating view on the evolution of neutrophils and other myeloid cells. The authors used a wide range of relational taxonomic data to show how CSF1/CSF1R and CSF3/CSF3R pairings evolved and contributed to granulocyte adaptations. This is a very original and potentially important piece of work that sheds light into the evolution of mammalian neutrophils.

Reviewer #3:

I like this paper. It clearly and succinctly presents an interesting and (to my knowledge) novel mechanism for proofreading that is distinct from typical formulations, that decouples the enzyme itself from the proofreading functionality (essentially modularizing the proofreading mechanism). The derivations and figures explore its possibilities and physical limits in a fairly convincing fashion (subject to several minor quibbles I detail below), supporting the conclusions. This mechanism significantly broadens the scope of systems that could enact proofreading, and allows tuning of the proofreading by regulating activity or concentration of gradient maintainers or enzyme, thus promising significant implications.

My two main suggestions are to give more context about (1) the effect of enzymatic catalysis on the resulting spatial distributions and (2) the relative costs of the two most prominent energy-consuming processes needed for this scheme. Specifically:

1) The entire manuscript assumes that catalysis is negligible and thus need not be explicitly modeled in solving for the steady-state distributions. How would incorporating a boundary condition at the right that involves non-negligible catalysis change (even qualitatively) your findings?

2) When quantifying the energetic costs, the main text solely focuses on the cost of counteracting the enzyme binding substrate, diffusing, and releasing. The SI explores some theory for the other cost of maintaining the substrate gradients, but without reporting any absolute numbers. For the biologically plausible kinase/phosphatase substrate-maintenance mechanism explored in the main text, how does its cost compare to the cost that you study quantitatively in the main text?

Reviewer #2:

In the manuscript by Galstyn et al on "Proofreading through spatial gradients", the authors proposed and studied a new kinetic proofreading (KP) model/scheme based on having a spatial gradient of the substrate (both "correct" and "wrong" ones) and the diffusive transport of the substrate-bound enzyme molecules to a spatially localized production site. The authors did an excellent job in explaining their new model and its connection and difference w.r.t. the classical Hopfield-Ninos KP mechanism. The key insight is that with spatial inhomogeneity, e.g., in the presence of a persistent spatial gradient for the enzyme or the substrate, one can consider spatial location as a state-variable. By having the substrate and product (or production site) at different spatial locations, these spatial degrees of freedom of the enzyme, i.e., enzymes at different physical location, can be considered as the intermediate states that are necessary for kinetic proofreading - each intermediate state contributes a certain probability for error-correction. In the original Hopfield-Ninos KP scheme, the intermediate state is provided by additional enzyme(s), whereas in this new KP scheme, it depends on having a spatial gradient, which the authors argue is more tunable. I like the theory for its simplicity and elegance. I have only a few mostly technical questions/comments.

My main concern for this study, however, is about how relevant this mechanism is for realistic biological systems. The original Hopfield-Ninos KP mechanism was motivated by specific and important biological problems (puzzles), namely the unusually high fidelity in biochemical synthesis process (in comparison with its equilibrium value). In this MS, the theory is developed without a specific biological system or specific biological question in mind. It is true that spatial gradient exists across biological systems and the authors also showed that typical kinetic rates may fall in the functional range of this new gradient-dependent KP mechanism. But, what is the function of the original system that such a kinetic proofreading process can help improve? Is it biochemical synthesis? Do the authors envision "correct" and "wrong" biomolecules being produced at the production site (x=L) like in the original setting of Hopfield-Ninos? Or is it signaling like in the T-cell signaling case? If so, do the authors envision that both the correct signaling molecule and the incorrect signaling molecule have a spatial gradient and they can both be carried by the same enzyme to their functional sites? I am not asking for a detailed comparison with a specific system, but I think a known but unsolved biological phenomenon that may be explained by this new mechanism would really help motivate a biologist audience. Furthermore, a connection to a specific biological system could also lead to testable predictions that would ultimately verify (or falsify) the existence of this mechanism.

Questions related to the model/theory:

1) In this study, there is a production r for the enzymatic reaction at x=L where the enzyme is active. However, the effect of this reaction, which change ES-->E+P, is not considered in the model equations (1-3). Is it because r is considered to be small? If so, smaller than what? Since speed is directly related to r, how does the value of r affect the speed and the speed-accuracy trade-off?

2) The nonmonotonic dependence of fidelity on the diffusion time for finite gradient as shown in Fig. 3c is intriguing. What determines the optimal diffusion constant (or diffusion time) when the fidelity is maximum for a given gradient length scale?

3) The study of trade-off among energy dissipation, speed, and fidelity is quite nice and adds to a growing list of study on performance trade-off's in nonequilibrium systems. For example, a similar energy-speed-accuracy (ESA) trade-off was studied systematically in the context of adaptation in bacterial chemotaxis (Lan et al, Nature Physics 8, 422-428, 2012) and chemosensory adaptation in eukaryotic cells (Lan and Tu, J R Soc Interface 10 (87), 2013). In particular, the exponential dependence of the fidelity on power consumption (energy dissipation) shown in Fig. 4 in this MS agrees well with results in these earlier studies (see Fig. 3c and Eq. 5 in Lan et al, 2012; Fig. 4 in Lan&Tu, 2103). It would be informative to discuss the trade-off found here for the gradient-dependent KP scheme in comparison with similar trade-off relations in other systems.

4) The power dissipation P is computed by Eq.8 in this MS. Where does Eq. 8 come from? What's the physical meaning of P? The standard way to compute energy dissipation is by computing the entropy production rate S', which is well defined. Then by assuming the internal energy does not change with time in steady state, we equate energy dissipation with kT*S'. The form of entropy production rate is known and can be found in text book (such as those from T. Hill) and papers (e.g., those from H. Qian and collaborators; and from U. Seifert and collaborators), and the formula given in Eq. 8 does not seem to be consistent with the known form of entropy production. In particular, for a given reaction with forward flux J+ and backward flux J-, the entropy production rate is: (J+-J-)ln(J+/J-), which can be easily shown to be positive definite and only =0 when detailed balance J+=J- is satisfied.

Overall, the MS provided a new gradient-dependent scheme for error correction in chemical systems. The study of trade-off among energy dissipation, speed, and fidelity (accuracy) in this new mechanism is also valuable for the general study of cost-performance relation in non-equilibrium systems. My main concern is the lack of examples of specific biological systems where this gradient-dependent error correction mechanism could be at work to enhance the specific biological functions of these systems.

Reviewer #1:

The authors proposed a new theoretical mechanism of kinetic proofreading based on spatially distributed biochemical systems. This concept is novel and distinctive from existing models of proofreading, although it is not yet proved experimentally. The writing is clear, concise and elegant. There are no logical flaws, and I really enjoyed reading this manuscript. Yet, I have a number of comments to be addressed, which will substantially increase the quality of this manuscript.

1) P. 1. The same concentration profiles are assumed for the right substrate R and the wrong substrate W. This is a strong assumption, could the authors consider the case where the concentration gradient length of the wrong substrate profile is larger than this length for the right substrate but still smaller that the distance L? They may calculate a series of the fidelity curves with increasing Lambda_W and the same Lambda_R. How will proofreading change?

2) P. 2. "The scheme proposed here does not rely on any proofreading-specific structural features in the enzyme; indeed, any 'equilibrium' enzyme with a localized effector can proofread using our scheme if appropriate concentration gradients of the substrates or enzymes can be set up. As a result, spatial proofreading is easy to overlook in experiments and suggests another explanation for why reconstitution of reactions in vitro can be of lower fidelity than in vivo." The key is the difference in the off rates for the right substrate R and the wrong substrate W, k^W_off >k ^R_off because W & R compete for E. This has to be mentioned in the above statement.

3) P. 2. "To demonstrate the proofreading capacity of the model, we first analyze the limiting case where substrates are highly localized to the left end of the compartment, lambda S << L." However, Eq. 5 is derived assuming that not only lambda s << L, but also lambda S << lambda ES (see Appendix).

4) P. 3. "... a red curve on the plot, is reached in the limit of ideal sequestration, ... " The word sequestration has a different meaning in biochemistry, e.g., it is used to describe 'sequestration' of an enzyme by the substrate/product or an inhibitor, which is not what the authors have in mind. They use 'sequestration' to describe the ideal substrate localization, Lambda_S -> 0. Put aside that this use of 'sequestration' is not the best choice, the authors need, at least, to explicitly define what they mean under 'sequestration'.

5) Fig. 3. Please explicitly define Veq speed (when k^W_off = k^R_off). In addition, how a black dotted curve is obtained is not explained, and the corresponding parameters are not given.

6) P. 5. "an enzyme E that acts on active forms of cognate (R) and non-cognate (W) substrates which have off rates 0.1 s−1 and 1 s−1, respectively (hence, theta eq = 10)." This implies a large difference in the free energy of binding of more than 1kcal/mol. In the absence of ATP/GTP hydrolysis, the difference in the binding energies is usually small. Can the authors give a specific example for an enzyme system where the difference in the free energy of binding is more than 1kcal/mol with no ATP/GTP hydrolysis?

7) Pp 5- 6. "As expected, proofreading by these gradients is most effective when the enzyme-substrate binding is very slow, in which case the exponential substrate profile is maintained and the system attains the fidelity predicted by our earlier explanatory model (Fig. 5b). .... If the binding rate constant (kon) or the enzyme's expression level (r_E) is any higher, then enzymatic reactions overwhelm the ability of the kinase/phosphatase system to keep the active forms of substrates sufficiently localized (Fig. 5c) and proofreading is lost." This is not entirely clear because the gradients depend on the phosphatase activity, whereas the authors did not mention that they likely assumed that when the substrate is bound to the enzyme, it is protected against the phosphatase.

8) Appendix D. The authors have to also consider or at least discuss the different diffusivities for phosphorylated and unphosphorylated substrates, a feature of many spatially distributed system and cite [FEBS Letters 583 (2009) 4006-4012] where this case was considered for dynamically stable spatial gradients.

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. Ahmet Yildiz (University of California) served as the Reviewing Editor.

Summary:

In the manuscript by Galstyn et al on "Proofreading through spatial gradients", the authors proposed and studied a new kinetic proofreading (KP) model/scheme based on having a spatial gradient of the substrate (both "correct" and "wrong" ones) and the diffusive transport of the substrate-bound enzyme molecules to a spatially localized production site. The authors did an excellent job in explaining their new model and its connection and difference w.r.t. the classical Hopfield-Ninos KP mechanism. The key insight is that with spatial inhomogeneity, e.g., in the presence of a persistent spatial gradient for the enzyme or the substrate, one can consider spatial location as a state-variable. By having the substrate and product (or production site) at different spatial locations, these spatial degrees of freedom of the enzyme, i.e., enzymes at different physical location, can be considered as the intermediate states that are necessary for kinetic proofreading - each intermediate state contributes a certain probability for error-correction. In the original Hopfield-Ninos KP scheme, the intermediate state is provided by additional enzyme(s), whereas in this new KP scheme, it depends on having a spatial gradient, which the authors argue is more tunable. The reviewers were enthusiastic about the theoretical model presented in this study because of its simplicity and elegance. However, the reviewers have also raised serious concerns that need to be addressed. In summary, the panel feels that discussion of possible biological example(s) where this novel type of proofreading may be occurring would significantly improve the manuscript's appeal to a broad audience. In addition, the reviewers ask for more explicit explanation of the effect of enzymatic catalysis rates, and discussion of the full dissipation cost.

Reviewer #3:

In their manuscript 'The adaptive architecture is shaped by population ancestry and not by selection regime,' Otte and colleagues use an evolve and resequence strategy to examine the response of a Portugal population of D. simulans responds to cold temperature. The authors identify putative targets of selection and compare the number of targets, their location, and the distribution of selection coefficients to previous work on the same population exposed to hot temperatures as well as a different population exposed to hot temperatures. The topic is of general interest, the work is sound and the writing is clear and concise.

1) It is not clear what the novel contribution of this manuscript is. The title indicates that the key finding is that population of origin mediates response to selection rather than the selection regime. However, the authors fail to provide compelling data to support that. The data are from 1 population under two selection regimes and a second population under one of those regimes. There simply aren't enough comparisons to infer that population ancestry plays a bigger role than selection regime in adaptive evolution.

2) The authors also seem to argue that a contribution of this paper is that it illustrates that temperature adaptation is not a single trait. This was the major finding of a 2014 paper from the same group in D. melanogaster- a single founder population was exposed to hot and cold temperatures and the authors found almost no overlap between the putatively selected variants in the two different temperature regimes.

3) Beyond the limited impact of the current work, there are some additional specific issues. The authors note that it was 'remarkable' that the distribution of selection coefficients and the number of inferred selection targets between the hot and cold experiments was 'highly similar.' What is the null expectation? Where does the null come from?

4) The discussion is somewhat unsatisfying and largely speculative. The 'different trait optima' section reads as straw man; this could be reframed to better guide the reader. There is little support for the 'differences in adaptive variation' hypothesis. The section on LD was interesting, but the simulation findings should reside in the results section.

Reviewer #2:

Overall Review: This is another commendable study from the Schloterer lab that features next generation genome-wide sequencing of multiple evolving populations. It compares results obtained with two different selection regimes, one hot and one cold, and two different founding populations of Drosophila simulans, one from Portugal and one from Florida. The results reveal a lack of consistency among selection regimes and founding populations. Temperature-dependent adaptation is shown to be "local" or "contingent," rather than globally consistent. My chief recommendations concern the experimental and theoretical contexts within which this study should be interpreted.

Major points:

1) I do not require any additional data collection or statistical revision. My comments are organized in terms of experimental paradigm (A) and theoretical significance (B).

A.

2) The typical paradigm for experimental evolution in this and many other labs is the use of hybrid populations created from isofemale lines. This method for founding experimental populations can be expected to generate some degree of random "historicity" as the isofemale lines approach fixation of specific genotypes with high stochasticity. Then there are further stochastic and historical effects which arise when such lines are hybridized. The strengths and limitations of this paradigm should be addressed. Most importantly, such stochastic historical effects might be the source of the discrepancy between the replicate lines derived from Portugal and Florida.

3) As the authors themselves point out, there is a comparative difficulty arising from the different scales of replication used for the Florida versus Portugal experiments. A further question for large-scale experimentation is whether a larger and uniform level of replication might produce more similar results, such as 20 evolving populations from each source. Or indeed, three sets of ten evolving populations from three distinct founders from the two sources, with a total of 60 evolving experimental lineages. The authors should discuss whether they believe that their findings would hold up with such an expanded experimental protocol.

4) The authors themselves point out at one point that their experiments might have benefitted from some phenotypic characterization of the presumed temperature adaptation. That raises the more general question of how the field of experimental evolution can progress with some labs just doing phenotypes and other labs just doing genome-wide sequencing. Surely this and other studies would be strengthened by combining the two types of assay. Furthermore, genomic evolution might be usefully analyzed in terms of the degree to which specific genomic changes can be associated with specific phenotypic changes, as that is the foundation for adaptation itself.

B.

5) This is yet another study that finds difficulties with the invocation of noroptimal selection along a one-dimensional functional gradient. Such models have been long-standing favorites of evolutionary theorists, such as Kimura and Lande. But that preference may arise more from the ease with which these models can be formulated and analyzed by theoreticians. Actual evolving populations don't seem to embody the precepts of such theory, whether the issue is the maintenance of genetic variation (see the work of Turelli, for example) or the evolution of closely studied populations, as illustrated by this study. An alternative point of view that the authors should discuss is that such models are indeed NOT usually correct.

6) There are alternative theoretical frameworks that address the maintenance of genetic variation and the response to selection. Among these are schemes of protected polymorphism arising from overdominance, epistasis, and frequency-dependent selection. If the thrust of the preceding point 4 is accepted, then it would be theoretically salient for the authors to suggest what type of underlying population genetic machinery would best account for their findings, in place of the noroptimal selection-mutation balance model.

Reviewer #1:

Otte et al. used an evolve and re-sequence strategy to explore "the genetic architecture of adaptive phenotypes". The authors previously found different genetic architectures across different founder populations evolving in a common hot environment. The authors chose one of these founder populations for replicated experimental evolution (5 replicate populations) in a cold environment for 50 generations. The authors were surprised to discover the same number of loci evolve under strong selection between the hot-evolved and cold-evolved replicate populations, though the 20-ish loci are largely non-overlapping. The distribution of selection coefficients was also similar. They interpret this commonality as evidence that the founder population history has a larger effect on adaptive architecture than the selection regime.

The study demonstrates a comprehensive effort to discover the number of genome regions and distribution of selection coefficients that emerge from a highly controlled experimental evolution project. The experienced team applies a sophisticated toolkit to this powerful experimental design - a toolkit that grows ever more sophisticated with each new experimental run that they perform. However, the authors set me up to learn why such different adaptive architectures emerge from different founder populations. Ultimately, the researchers acknowledge that they "cannot pinpoint the cause for the differences in the inferred adaptive architecture..." Some results simply recapitulated the previous Portugal E&R study and other results recapitulated a D. melanogaster E&R study. I did not find the "common adaptive architecture" across different selection regimes to be a particularly compelling discovery of sufficiently broad interest. Other concerns and questions can be found below:

Major concerns:

1) Pg. 4: It is my understanding that the power of multiple populations from a single founder evolving in parallel allows for more rigorous identification of loci targeted by selection. I found it surprising to discover that if a lack of replication emerges from an experimental evolution study, this outcome is interpreted as "genetic redundancy." First, genetic redundancy has a precise definition in genetics that muddles the author's meaning. And second this interpretation seems rather post-hoc.

2) To "shed more light on the different selection responses" is a weak motivation. The introduction sets me up to understand why selection responses are so different but no major insights into the "why" emerge from the cold-adaptation experiment.

3) More explanation of figure 1 in the main text is needed. Does each point correspond to a SNP that consistently changes across all five populations? Or is this the union?

4) Line 210: How did the researchers define "stress" and determine that the degree of stress is equivalent across two temperature regimes? The absence of these data undermine the potency of the comparison.

5) How can the authors be sure that the only difference between the hot and cold populations was temperature? Was competition/population size/etc held constant? Might the lack of overlap between hot and cold adapted loci stem from one such regime selecting for a different phenotype? (i.e., not temperature tolerance)

6) Line 237: The authors assert that most alleles show a temperature-specific response - a discovery with precedent in the literature, including from this team of researchers. The authors attribute the absence of common loci between temperature regimes to the high number of generations (50) compared to the number across seasons cited in Bergland et al. The researcher could easily look for common targets at earlier time points of experimental evolution to test this idea.

7) Line 292-293: This section reads as disingenuous - the researchers could have explored overlap between Portugal and Florida founders using only the selected loci coordinates and look for non-random overlap using simulations/resampling tests.

8) Discussion: The speculation about why such different architectures emerged across Portugal and Florida was diluted by the absence of initial fitness estimation upon subjection to a cold environment (which would have offered evidence for different initial "optima" across founder populations) as well as the change in fitness from generation 0 to generation 50.

9) The simulations and corresponding discussion would make for an interesting review/opinion piece but not as new results for this manuscript.

Minor Comments:

1) Pg. 3. The recurrent citation of Barghi et al. in the Introduction undermined the reader's impression that fundamental questions are being addressed in this article

2) Lines 33-39: The argument that parallel signatures of selection across distinct natural populations are insufficient to address the polygenic basis of adaptive phenotypes, and so comparatively more contrived E&R studies are required, was unconvincing.

3) Line 158: Confusing. Should "among" actually be "within"?

4) Line 486: I believe that the authors would be hard-pressed to find in the literature a paper declaring that "single population...[is] sufficient to understand the genetic basis of adaptive traits".

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 reviewers agreed that the study was well-executed and offered important insight into how decisions around experimental set up affect the outcome of experimental evolution studies. Ultimately, however, there was consensus that the results failed to support the broadest conclusion that ancestry is more important than selection regime. Moreover, given previously published reports on experimental evolution from your group and others, the current study lacked sufficient novelty.

Reviewer #3:

The paper from Itoh is a thorough and interesting analysis of a mechanistic dissection of the underlying cause of Dupuytren's Disease (DD). One exonic SNP is associated with the disease and this mutation changes a residue in helix C of MMP14, a major collagenase, from Asp to Asn. Interestingly, helix C is distant to the catalytic center and the authors show not unexpectedly that recombinant mutant forms of the protease bearing the mutation have identical gelatinolytic and collagenolytic activity in solution. However, in the cell membrane bound form, collagenolysis is markedly reduced. The authors discuss several possibilities for this centering on the potential impaired ability to form dimers. Dimerization and collagen binding has been shown by many groups (please cite some other groups and not just your labs work) to be important for collagen triple helicase activity. This is then suggested to be the underlying cause of the defect in collagenolysis (that then leads to impaired collagen turnover and hence the build up of collagen at several locations in these patients with DD).

As always there are several points that need addressing to make this a truly nice piece of analysis and data. The major criticism resides in the very nice patient data presented in figure 5. This is key to the whole paper but sadly the authors actually ignore what is shown and drive forward with their own interpretation of the underlying mechanism.

Major comments:

1) It is quite clear from a variety of approaches used in the detailed analyses in Fig 5 that there is a strong difference in the degree of enzyme activation occurring in the patient and normal cells comparing AA, which shows the predominant fully active ~51k form vs GG very low amounts perhaps 5% of the mutant when on the cell surface. (the gels are poor quality and so the estimate of MW is difficult to be sure). Thus, the simplest explanation for the reduced collagenolytic activity of the patient is that there is less active protease, without invoking alternate mechanisms. Nonetheless, I understand why the authors investigated dimerization and hemopexin domain interactions and that is fair enough. BUT, those data and interpretations need to be placed in context with fig 5. The interpretation is that other effects occur that alter the activation of MMP14 buy furin or in its cell surface protein protein interactions or with the plasma membrane

2) Relatively few analyses have been performed of the critical residues in collagenases for collagenolysis. In MMP8 re the S3' site reveals the importance of specific residues in contacting collagen for cleavage (Pelman) that apparently is not important for the mutation under study in the present paper as 237 is distant from the active site on Helix C. Notably, 237 lies in an interesting sequence: DDDRR in which one of the Asp couples to the active site in triple salt bridge relay commencing from the NH2 of the F/Y at the start of the catalytic domain after correct activation, and this is needed to fully activate MMPs. This work by Stoecker should be referenced (though it is not in relation to MMP14 it is a general principle for all MMPs). Please discuss this D as it may affect the electrostatic environment of the 273 position and so reduce catalytic potential. While evidence presented does not indicate this (for collagen and gelatin) there are no kcat/km determinations which are needed to quantify the effect of the mutation.

3) However, the 273 position is potentially close to the top (blade I) of the adjacent hemopexin domain that the authors know very well is key for collagenolytic activity. The authors posit quite correctly that the mutation may affect the interaction with the hemopexin domain and I totally agree. Collagenolytic activity is difficult and precision in protein contacts is likely needed for catalysis to occur. A model of the catalytic domain contacting the hemopexin domain in blade I is needed to help interpret this. See Zhao et al 2014 (http://dx.doi.org/10.1016/j.str.2014.11.021 ). With the Xray scattering data this appears to be a potential mechanism for disruption, not just dimerization. Please include in Fig 1 a model of the full length MT1-MMP and the site of 273 in relation to the top B strand of blade I for the potential interaction by modelling. Arg 360 by eye might be a potential interactor. Though there are two other Arg that may be involved perhaps R 330, R343 and R345? Please investigate this as it will be interesting.

4) In this regard, a major oversight has been the lack of reference to the very good analyses of MT1-MMP membrane association by Marcinket al (2019) Structure 27: 281-292.e6. This reveals the membrane binding associations of blade III and IV of the Hx domain which differentially orients the protease on the surface and hence to collagen. An earlier paper by the same group (http://dx.doi.org/10.1016/j.str.2014.11.021 ) also has been ignored (above). These analyses are extremely detailed with amino acid resolution and much could be gained by interpreting these contact residues between collagen and the hemopexin domain and the domain and lipids and hence how it interacts with the catalytic domain where the mutation resides. This must be done in depth to be fair to other work and also for deeper biological insight to the mechanism of collagenolysis in general and in these patients in particular. The membrane association may also drive or supplement dimerization.

5) I have a serious issue with the fusion construct used in Fig 6. "The Fc part of these chimera molecules enforces the ectodomain of the enzymes to form a disulfide bonds-mediated stable homodimer (Figure 6B), thus allowing the determination of the molecular shape of the MT1-MMP homodimer". How can the authors conclude this? A dimer certainly is formed but its orientation may be totally different from the natural situation where no SS bridge occurs and potentially is in a different orientation. This is a serious caveat that must be clarified to interpret the nice data otherwise in Fig 6.

6) Only indirect evidence presented that the mutation does not affect dimerization. Please show gel filtration of the complexes or other means to clarify the dimer vs monomeric forms of the WT, mutant and 1/1 heterodimers as this is an obvious and important likely mechanism to explain the phenotype.

7) It is amazing that the allelic frequency is 0.20. So why does the heterozygous phenotype that the authors investigate in the recombinant experiments show up more in the population?

Reviewer #2:

The work contains interesting features, but several aspects of the work are more perplexing than insightful. The authors identify a SNP in MMP14 that occurs in 30% of the population that negatively affects the collagenolytic activity of the encoded gene product, i.e., MT1-MMP. They then propose that the resulting D-to-N mutation may play a role in the pathogenesis of Dupuytren's disease (DD). First, while the title states the the SNP variant causes " .. a defect in collagenolytic activity (that) confers the fibrotic phenotype of DD" , the findings are more appropriately described as having established a correlation between defects in collagenolytic activity and the fibrotic phenotype of DD. However, no data have been presented that document a defect in collagenolytic activity in DD pts harboring the SNP. Indeed, it remains unclear as to whether type I collagen is the key substrate in DD. Given that MT1-MMP can hydrolyze an almost bewildering array of non-collagenous substrates (both cell-surface, secreted and plasma-derived), it is difficult to rule out the possibility that that the D-to-N mutation does not more profoundly affect the hydrolysis of an alternate target. It would be interesting to know if there are changes in gene expression when COS cells are transfected with wt vs the SNP variant of MT1-MMP and cultured on plastic (or even with an E-to-A mutation in the catalytic domain). Second, these concerns notwithstanding, if one were to assume that type I collagen is the critical target, the underlying mechanisms that impact collagenolytic activity are unclear. The authors document complex changes in MT1-MMP processing and cell surface expression in combination with structural changes in the soluble homodimer. Yet, when the soluble variant was shown to express normal type I collagenolytic activity, a conclusion was reached that enzyme activity is likely affected "only when the proteinase is expressed on the cell surface." Possibly, but how do we rule out effects on MT1-MMP exocytosis, endocytosis,trafficking or post-translational modifications in the tail, hinge region, etc - or as mentioned above, hydrolysis of an alternate - and potentially more important - target?

Reviewer #1:

In this paper the authors focus on a mutation of MT1-MMP that seems to be associated with Dupuytren's Disease (DD). Using overexpression systems and cells isolated from patients they provide evidence that a major defect of the mutant form of MT1-MMP is it’s reduced ability to activate MMP-2 activation and in turn collagen degradation. Although interesting, the paper presents major shortcomings.

-All the results obtained are based on in vitro experiments and most of the studies are dependent on overexpression systems.

-The effects of mutant MT1-MMP on MMP2 activation are not as impressive as the authors claim. No statistical analysis is provided for Fig. 2B (MMP2 activation in cells expressing WT or mutated form of MT1-MMP) and it is not clear if the changes in MMP2 activation observed in Figure 3B (pro-MMP2 activation in cells from patients) are indeed significant. From the graph presented it does not seem to be the case. If this is the case, then the major point of the paper is indeed not corroborated by strong evidence.

-The authors propose that WT and mutated MT-MMP might form a dimer and the mutated form might act as dominant negative. IP is shown only with anti-FLAG antibodies. Reciprocal IP with anti-myc should also be shown. Also different stringency conditions should be employed to determine the 'strength' of this potential heterodimerization. Importantly advanced FRET-based techniques should be used to study and evaluate heterodimers in the plasma membrane.

-The title of the paper is misleading as these only in vitro based studies do not allow the authors to conclude that the An SNP variant MT1-MMP with a defect in its collagenolytic activity confers the fibrotic phenotype of Dupuytren's Disease. To answer this key question a vertebrate animal model needs to be provided.

-Figure 5 needs better controls and/or quantification. The IF provided is not convincing and the authors need to provide loading controls of 'surface' proteins. Importantly statistical analysis needs to be provided to determine whether the changes observed are significant and important.

In conclusion it is felt that the major conclusions of this paper are not based on convincing data and more analysis needs to be done in order to determine how exactly the mutated form of MT1-MMP might lead to DD.

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 recognize that the paper contains interesting features, they also addressed major concerns and pitfalls with the study, including: 1) the overall significance; 2) lack of in depth mechanism whereby MT1-MMP variants might alter collagenolytic activity; 3) lack of functional studies with cells isolated from DD patients; 4) the importance of type I collagen as a key substrate in DD remains unclear; and 6) lack of solid evidence that MT1-MMP itself plays a key role in DD.

Reviewer #3:

This study provides experimental evidence that, in contrast to a currently accepted view, some sensor histidine kinases exist in more than one oligomerization state and that a monomer-to-dimer transition might play a role in signal transduction. Such transition is well documented for eukaryotic signal transduction systems, but not in prokaryotes. Thus, the findings reported here open an avenue to a broader investigation of this phenomenon and its potential generalization.

My only major comment is the inexpert level of bioinformatics analysis. While all specific concerns seem minor (listed in the corresponding section below), taken together they amount to a bigger problem, particularly with presentation. On the other hand, none of the shortcomings with the bioinformatics part seriously affect major conclusions of this study.

Reviewer #2:

Manuscript Summary:

The manuscript by Dikiy et al. extends previous investigations from the Gardner lab on the oligomeric states of histidine kinases containing photosensing LOV domains (LOV-HKs). The Gardner lab had previously characterized two dimeric and one monomeric LOV-HK from Erythrobacter litoralis. In the present study, they perform sequence analyses to identify soluble LOV- and PAS-domain containing HKs similar to the previously characterized monomeric LOV-HK EL346. They characterize the photocycle, oligomeric state, and autophosphorylation activity of several of these HKs. Finally, noting that one dimeric LOV-HK (RH376) has three small regions of sequence that are absent from the monomeric EL346, they delete these regions individually and in combination to generate a set of mutated RH376 proteins that they characterize.

General Assessment:

The results of this study are consistent with previous studies from the Gardner laboratory, indicating that functional LOV-HKs can exist as monomers, dimers, or mixtures of both. Perhaps unsurprisingly, the effects of deletions engineered to identify determinants of dimerization do not clearly align with any simple hypotheses and limited insights are gained. Overall, the study would benefit from greater precision in the writing of the manuscript, greater rigor in experimental design and analyses of data, and restraint in tempering conclusions to better align with the data.

Major Comments:

1) The introduction could be improved by more precise language (see details in Minor Comments).

2) Details about the autophosphorylation assay should be provided. Specifically, the concentrations of proteins used in the assays need to be specified, unless the stated concentrations are the final concentrations in the assay, in which case this needs to be more clearly indicated. The extremely low concentration of ATP (3.6 uM) is problematic. Even for initial rate determinations, ADP generated during the reaction will likely inhibit phosphorylation under these conditions.

3) Figure 1. Given the substantial domain rearrangements that are known to occur during signaling, it would be helpful to specify the signaling states depicted in the schematic structures.

4) Line 231 subtitle and lines 257-258. This conclusion seems to be somewhat overstated given the small number of proteins examined. Within Table 2, one of three EL346-like LOV-HKs is monomeric and the same is true for the three LOV-HKs examined. This ratio of 4:2 dimers to monomers does not seem sufficient to conclude that LOV-HKs are generally dimeric.

5) Lines 270-274 and Fig. 3b. How do you know that the plateau is indicative of phosphatase activity rather than a simple equilibrium due to the presence of ADP in the reaction mixture (either as a contaminant in the ATP or generated during the reaction)? A minimum of 3 replicates should be shown with error bars. Which data from the two-trials were used to reach the conclusion of a 1.5-fold difference in activity? More rigorous statistics should be employed.

6) Lines 274-279 and Fig. 3b. It is not clear from the description of the assay in the Methods section what concentrations of HKs were used in the assays. If concentrations were not similar for all proteins assayed, differences in rates are likely to result from different amounts of ADP generated during the reaction.

7) Lines 278-279. It is a big leap to conclude that monomer-dimer transitions may be a regulatory strategy based on the observation of different rates of autophosphorylation. What concentrations of monomer and dimer proteins were used in the assays? And if the oligomeric state is used as a regulatory strategy, how? Do you envision some mechanism that regulates the oligomeric state and this in turn regulates autophosphorylation? (This is eventually addressed in the discussion. Perhaps the statement about a regulatory strategy should be withheld until the Discussion>)

8) The sequence of the loop in DHp and CA domains of HKs has been used to predict cis- vs. trans- mechanisms of autophosphorylation. Please comment on the loops in the LOV-HKs. Presumably all monomeric HKs would have loops consistent with a cis- autophosphorylation mechanism. Are they similar in monomeric and dimeric LOV-HKs?

9) Fig. 4. What are "monomer-1/dimer-1" and "monomer-2/dimer-2"? Why is there such a large difference in the activities observed for -1 and -2? Also, the y-axis in the graph in Fig. 4b appears to be mislabeled as "Concentration".

10) Fig. 6. A minimum of 3 independent activity assays should be shown and statistical tests should be applied to determine the significance of the observed differences, especially given the large variations in the data.

11) Lines 330-332 and Fig. S4. The absorbance profiles clearly differ between the proteins. How much variation would be necessary to claim that a protein was non-functional? Indeed, in the next sentence, it is acknowledged that flavin binding is adversely affected. If so, then what is meant by "the deletions do not perturb the folding and function of the LOV domain"?

12) Lines 368-369. What experiments address the sufficiency of either RH1 or RH3 for dimerization? The rationale for this statement is not clear.

13) Fig. S6. It is not conventional to introduce new data within the Discussion. Perhaps this figure should be moved to the Results.

Reviewer #1:

The main objective of this study was to investigate a possible relationship between oligomerization and regulation in histidine kinases. To this end the authors identified novel LOV and PAS sensor kinases based on sequence homology searches with HK EL346, a soluble monomeric HK that senses blue light through a LOV domain. To study the monomer-dimer transition as a possible regulatory mechanism they try to "monomerize" a dimeric LOVHK, named RH376, by deleting three regions that could be determinants of the oligomeric state. Nevertheless, the authors found that none of these deletions disrupt the dimeric state of the protein. The conclusion of the work appears to be that multiple domains contribute to dimerization and function of HKs.

This manuscript is experimentally well done and well written. First the authors show that Non-Lov PAS-HKs show a mix of monomers and dimers, both of which are active. Then, the study is focused in the LOV HKRH376 and in deletions RH1-RH3 and a double mutant RH1+3. RH1 and RH2 are active dimers while RH3 remains largely dimeric and is inactive. Finally, the double mutant is an inactive monomer. The major conclusions of this manuscript are that multiple regions determine oligomerization in this family of HKs and light-induced conformational changes have a complex relationship with autophosporylation and do not appear to be restricted to the oligomerization state. In summary, I found that the data, although technically sound, don´t provide mechanistic insights in the regulatory mechanism(s) of sensor kinases.

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. Michael T Laub (Massachusetts Institute of Technology) served as the Reviewing Editor.

Summary:

This study provides evidence that some sensor histidine kinases may exist in more than one oligomerization state and that a monomer-to-dimer transition might play a role in signal transduction. The results are consistent with and extend prior work from this lab and will be of interest to those studying two-component signal transduction.

Reviewer #3:

Bissett and colleagues provide an in-depth assessment of the stop signal task implementation in the ABCD protocol. Given the importance of the data set itself, as well as current trends in research funding, there are several important lessons to be learned here, both regarding this specific task implementation, as well as with respect to task designs in large-scale data collections in general.

Reviewer #2:

This paper reports a thorough critique of the ABCD stop-signal data set. It identifies a set of eight problems that severely limits the utility of the ABCD stopping data. In particular, the first two (which are essentially the same problem) invalidate estimates of SSRT based on the independent race model because of violations of the context independence assumption of that model. The remaining issues are more minor in the sense that while potentially problematic they either affect a very small percentage of the data and so can be dealt with by removing the affected trials or participants, or do not appear to be problematic in practice.

The authors have provided a valuable service to the research community in systematically and thoroughly cataloguing these issues, although we think it is fair to say that a number of people (including the present reviewers) have been aware of the key design issue caused by the stop signal replacing the go signal for quite some time and have been working on solutions.

Below we have a few suggestions for clarifications, but overall the paper is very clear and well written.

Although the paper mentions that "new models for stopping must be developed to accommodate context dependence (Bissett et al., 2019), the latter of which we consider to be of utmost importance to advancing the stop-signal literature", it does not discuss such models and neither does it show the potentially severe consequences of context independence violations in the ABCD data set.

All our more substantive comments relate to "Retroactive Suggestions For Issue 1". First, the authors write: "Given the above, if analyzing or disseminating existing ABCD stopping data, we would recommend caution in drawing any strong conclusions from the stopping data, and any results should be clearly presented with the limitation that the task design encourages context dependence and therefore stopping behavior (e.g., SSRT) and neuroimaging contrasts may be contaminated".

We feel that this recommendation is too lenient and would suggest the following alternative: Unless the ABCD community conclusively shows that the design flaw does not distort conclusions based on SSRT estimates (or any other stop-signal measure), researchers should not use the ABCD data set to estimate SSRTs at all.

Second, the authors suggest removing subjects who have severe violations as evidenced by mean stop-failure RT > mean no-stop-signal RT. We are concerned that this recommendation impacts on the representativeness of the sample. Also, this recommendation ignores the fact that violations are not an all-or-none phenomenon but are a matter of degree and can come in varying shapes and sizes.

Third, the authors recommend that "any results be verified when only longer SSDs are used, perhaps only SSDs > 200ms". Figure 3 does not seem to support the recommended cut-off of 200ms: at 200ms accuracy is still far from asymptotic.

In general, we feel that recommendations based on removing participants and trials are not sufficient. Such practices will affect the representativeness of the sample and will increase estimation uncertainty and hence decrease power. We believe that the only way to solve Issue 1 is by developing measurement models that can account for the dependence of the go and the stop process.

Reviewer #1:

General assessment:

The paper points out eight design issues observed in the stop signal task of the longitudinal Adolescent Brain Cognitive Development (ABCD) study by Casey et al. (2018). The issues are ordered by importance and are partially interrelated. The paper is written in a very clear and non-redundant style and makes a number of suggestions on how to deal with the various issues. The points made in the paper are well-taken. Moreover, the preprint of this paper has already elicited a reply by authors from the ABCD study leading to some partial adjustments of the design of the stop task.

Major comments:

1) As the authors suggest, the most important issue is the potential violation of the context invariance assumption due to the variability of the go stimulus duration across different stop signal delays (SSDs). This is a plausible concern even if the number of "clear" violations is relatively small (447 out of 7231 subjects). Nevertheless, the authors' point would be made even more convincing if they could point to some (simulation?) results showing the effect of a weaker go signal at short SSDs on the estimate of the stop signal response time (SSRT).

2) I suggest using the term "context invariance" instead of "context independence" , in order not to confound the assumptions of 'context' and 'stochastic' independence in the Logan-Cowan race model. It should be pointed out that the prediction of the race model concerning faster stop failures than go responses is conditional on both context invariance AND stochastic independence between go and stop signal processing being true (see Colonius & Diederich, 2018, Psych. Review).

3) I have no further major comments but would like to suggest a further analysis: Let us suppose, as the authors point out, that the RT distribution of responses to the go signal is indeed affected by the duration of the go signal. As a first approximation, let us assume that the observed RT distribution is a binary mixture of responses: slow RTs to a weak/short go stimulus and fast RTs to a strong/long gos stimulus. Without making specific assumptions about the two components of the mixture, one could employ a mixture distribution test first suggested by Falmagne (1968, British J. Math. Statist. Psychology): The RT ("density") distributions, plotted separately for each SSD and go signal trials, should all cross at one and the same point in time. Of course, this is not a foolproof test but if some evidence in favor of this prediction is found it would strengthen the authors' point.

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 4 of the manuscript. Birte Forstmann (University of Amsterdam) served as the Reviewing Editor.

Summary:

This paper focuses on one of the benchmark magnetic resonance imaging (MRI) datasets, the so-called Adolescent Brain Cognitive Development (ABCD). In total, eight design issues observed in the stop signal task of the longitudinal ABCD study by Casey et al. (2018) are pointed out. The design issues are described in detail, ordered by importance, and a number of suggestions are given on how to overcome potential limitations. Given the importance and prominence of the ABCD study in the field of cognitive neurosciences, both the reviewers and editors believe this paper to highlight essential issues in a constructive way. Finally, we believe this paper will elicit a fruitful discussion including the adjustments of the design of the stop signal task.

Overall, this manuscript is well written, interesting, timely and will help resolve the debate in the field. We have the following suggestions to improve the manuscript.

Reviewer #3:

The work by the group of Andries Bergman investigates the heterogeneity of macrophages in prostate cancer. They identified three macrophage subsets in tumorigenic tissue, which were also present in adjacent areas. All three subpopulations were clearly distinct on the molecular level, however, none of these subsets had a clear M1 or M2 phenotype. Accordingly a gene signature could be extracted that correlates with metastasis-free survival of patients and might have prognostic value.

Even though the manuscript is interesting, well written and the finding that no clear difference in macrophage composition is evident between adjacent and tumorigenic areas is surprising and new, the paper is not sufficient in its current form to fully support the presented messages.

Main points:

1) The authors state that they identified three distinct populations of tissue resident macrophages in prostate tissue, independent of the localisation. This finding is surprising, since an accumulation of monocyte-derived tumor(-associated) macrophages can be observed in almost all tumors. According to the material and methods section, the authors did not digest their tissue. What is the impact of digestion vs. non-digestion on macrophage recovery from human prostate tissue? Is it possible that especially tissue-resident macrophage subsets embedded in the parenchyma were missed? A detailed flow cytometry experiment needs to be performed in order to identify the most sensitive but at the same time most efficient isolation procedure that captures all possible macrophage subsets. Advanced flow cytometry with a broader antibody spectrum (e.g. CX3CR1, CD11c, CD14, CD16....) needs to be used to characterise the myeloid composition in more detail. Maybe even more sophisticated methods like CyTOF are advisable and recommended (See et al., 2017).

2) The authors call the identified cells "tissue resident macrophages". However, a closer examination of the genes in the identified clusters suggest, that cluster 0 might refer to (monocyte-derived) macrophages (identified by Cx3cr1, Ms4a7, Trem2, C1q; Chakarov et al., 2019), cluster 1 to cDC1 dendritic cells (identified by Flt3, Cd207, Fcer1a, Clec10a; Heger et al., 2018; Dutertre et al., 2019) and cluster 2 likely to extravasated monocytes (high levels of S100A genes, Ifi30 and Lyz; Kapellos et al., 2019). Therefore, maybe only cluster 0 reflects true (interstitial?) tissue resident macrophages. Accordingly, the bioinformatic analysis has to be strongly intensified and the data needs to be compared to other recently published work in order to identify for instance the signatures of tissue-resident macrophages, interstitial macrophages, monocyte-derived cells and monocytes. The authors have to familiarise themselves with the common nomenclature and the state-of-the-art identification of human mononuclear phagocytes (including cDCs) based on their transcriptomic signatures.

3) The authors speculate in the discussion part that the tumor influences distant macrophages through tumorigenic factors, which might be of prognostic value. In order to make such a statement, the authors have to show the transcriptome signature of macrophages isolated from tumor-free patients. Only a direct comparison between 'healthy' and 'tumorigenic' tissue can uncover tumor-dependent effects on macrophage transcriptomes and composition.

4) Close histological examination with subset specific markers needs to be performed to show that indeed no cellular difference exists between the localisation of macrophages in adjacent and tumorigenic areas. This should be compared to 'healthy' tissue (see previous point).

Reviewer #2:

The manuscript is a single-cell RNA-seq approach to macrophages (CD3- and CD14/CD11b+) from prostatic adenocarcinoma tissue as well as adjacent non-tumorous prostate tissue. The authors find that three RNA-seq-defined macrophage subset clusters were found in both tumour and adjacent prostate in varying proportions in their patient series. These clusters show only weak associations of expression of genes related to the 'M1' and 'M2' macrophage activation status. They also show no differential association of expression of genes involved in T cell response regulation. One cluster appears to show evidence of NF-kappaB and WNT signalling but little interferon signalling, while another shows strong interferon signalling but poor WNT signalling, and the third cluster ('cluster 1') appears likely to consist of cells in cycle. These are intriguing populations for further work.

The authors then derive a differentially expressed gene signature, and show that it correlates with clinically relevant parameters in publicly available data sets. These correlations are very interesting from a translational perspective.

The data are substantive, and provide a valuable resource database for the transcriptional landscape of prostatic monocytic cells. However, the findings remain primarily empirical correlations at this stage, with very limited mechanistic implications.

1) The patient numbers analysed are very small. There are only four clinical samples (with three biopsies each) from which both tumour and non-tumour tissue has been used. There are no prostate samples without tumours similarly analysed to provide any indications about the 'normal' (and perhaps true 'tissue-resident') macrophage populations of the human prostate. It is thus difficult to interpret the monocytic cells analysed as blood-derived or of tissue-resident origin, limiting mechanistic speculation. It is also not clear if the observed patterns of monocytic lineage subsets are generated in patients prior to or after initiation of malignancy.

2) The cell numbers analysed are quite small as well. From four patient samples analysed, a total of 641 cells have been used for the RNA-seq-based analysis. This means an average of about 160 cells per patient sample, including both tumour and non-tumour tissue (an average of eighty cells from each location, perhaps). This seems a relatively thin basis for major interpretations.

3) Further to the above concern, there is no indication of the immune cell infiltrate density, especially monocytic cell density, in the various individual tumour samples, nor any analysis of the landscape of the immune cell infiltrate, for correlation with the monocytic lineage transcriptional groups for further mechanistic speculations. This is, again, compounded by the availability of only four patient samples.

4) There is no independent validation that there are indeed three monocytic subsets in prostatic tumours with clustered differential protein expression of interferon, WNT and cell cycle pathways, leaving the functional assumptions without rigorous support.

5) There is no clarity regarding the macrophage gene signature derived from the integrated dataset. As a result, while there is translational value to its associations with clinically relevant parameters, the biological interpretation remains unclear, since it is not clear that these genes are not expressed in non-monocytic cells in prostatic tumour biopsies, especially given that the differential expression consists of genes in the NF-kappaB, WNT and interferon pathways.

Reviewer #1:

In this manuscript Siefert et al., profile human prostate cancer-associated macrophage subtypes by single-cell RNA-seq. This analysis identified three major sub-population of macrophage (cluster-0, 1, and 2) in human prostate cancer and adjacent normal tissue. Next, the authors investigate the association of macrophage subtypes with recurrence and metastasis in independent prostate cancer cohorts. This leads to the identification of CSF1R+ (cluster-0) macrophage as a cell type associated with early recurrence and metastasis in prostate cancer. Overall this is an interesting study, however, in the absence of specific presence and/or enrichment of cluster-0 in tumor tissue it is not clear why these macrophages lead to early relapse or metastasis in prostate cancer. Moreover, the absence of any validation and/or functional analysis further diminish the broader implication of this observation.

1) Overall, the authors have employed very good QC parameters to filter superior quality cells. However, they detected batch effects in data (patient-specific clustering) and therefore employed batch correction methods. Unfortunately, after batch correction, they fail to detect tumor-specific macrophage populations in prostate cancer. The authors' reason that this could be due to the broader effect of 'tumor' on the adjacent normal ecosystem. However, in the absence of a comparison between macrophages from normal prostate and prostate tumor, it's difficult to conclude that tumors influence the macrophage in adjacent normal tissue. Given the well established phenomenon of tumor-associated macrophage this observation is surprising and an alternative explanation could be possible artifacts induced during the batch correction (i.e. integration) leading to the removal of subtle differences between tumor vs adjacent normal macrophages.

2) This study identifies three major sub-population of macrophages in prostate cancer. Authors discuss the limitation of M1/M2 nomenclature to define macrophage spectrum, which is evident from their analysis as well. However, they also don't provide a marker-based nomenclature of these macrophage clusters. It will be beneficial for the community to know the specific markers of these macrophage sub-populations which will be important for flow-cytometer or imaging-based validation of these populations. It is really important to validate the identity of single-cell RNA-seq clusters by flow or imaging analysis. However, the lack of validation remains one of the major limitations of this study. Not sure given the COVID situation it is possible but it will be very beneficial for the community.

3) It's not clear how cluster-0 macrophage leads to early relapse or metastasis. Given the higher expression of TNFa and IFN-g in cluster-0, it will be beneficial if authors can provide some discussion on this. Moreover, since cluster-0 is not unique to the tumor, does the frequency of these cells changes in the tumor ecosystem when compared to adjacent normal tissue? This quantification will be important to understand the possible implication of these cells in early relapse or metastasis.

4) A recent study by Huang et al., (Cell Death and Disease 2020) demonstrates the role of CCL5+ TAMs in promoting prostate cancer stem cells and metastatic phenotype. Do cluster-0 macrophages express CCL5 or any other marker which may facilitate replacement and metastasis.

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:

While we all considered the value of the dataset as a useful resource for the community, providing a transcriptional landscape of prostatic monocytic cells, we all agreed that the study remains too descriptive and primarily empirical correlations at this stage, with very limited mechanistic implications and validation. In addition, the lack of healthy control, an incomplete bioinformatical analysis (batch effects, other MPS cell clusters like cDCs), missing validation, and a limited number of cells/patients dampened the enthusiasm of all the reviewers.

Reviewer #3:

General assessment:

The work presented is a major scientific achievement. This is the first functional reconstitution of any CO2 concentrating mechanism. 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.

The writing is generally clear. The claims are well-supported by multiple lines of evidence. The engineered Rubisco-dependent E. coli showed clear improvements in growth phenotypes after introduction of H. neapolitanus CCM genes, which were then confirmed using thorough genetic and biochemical analyses.

Major comment:

The control EM images in Figure 5 should be present in the main figure, not a supplement. It is concerning that the positive control failed. It should be repeated, or, if possible, it would really help to show TEMs of WT H. neapolitanus. This would allow comparison of the putative carboxysomes to a native carboxysome and would greatly improve the quality and value of this figure.

Reviewer #2:

The manuscript by Flamholz et al. is a significant and excellent piece of work that is very novel and would have wide appeal to a range of microbiologists and general biologists. The manuscript is well written and represents a very interesting and largely complete set of data.

It was an ambitious goal to convert a model bacterium such as E. coli into a system that is able to grow with dependence on the CO2-fixing enzyme Rubisco, and a basic Calvin Cycle. The authors have achieved that, and as expected these engineered cells required a very high 10% CO2 for optimal growth. No LB media was required except for addition of some minimal salts and glycerol. Without added CO2 growth does not proceed with glycerol alone. Next, and Importantly, they then asked if they could add a basic CO2 concentrating mechanism (CCM) from a sulphur bacterium (Halothiobacillus) so that the E. coli cells could scavenge and accumulate enough inorganic carbon (CO2 /bicarbonate) to grow at air levels of CO2 (namely 0.04% CO2). Some 20 genes were required to make up this basic CCM work, namely a complete carboxysome operon, genes for a Ci pump (DabBA2), Rubisco genes, phosphoribulokinase, and engineered removal of both carbonic anhydrase genes from E.coli as well as riboseP-isomerase. The growth rate of cells at air was relatively slow, but shown to be at an expected rate based on modelling. Ultimately this work has implications towards the question of whether a basic CCM could function in a plant chloroplast and provides a boost to photosynthetic CO2 fixation. It seems to support this goal.

Curiously, the complete 20-gene system did not initially allow growth at air CO2 levels, but did work after a series of directed evolution experiments in bioreactors that led to some minor mutations. It is noted that one of these changes was the transfer of a the high copy number origin from one plasmid to the other, while some were 'regulatory' elements within the pCCM and pCB plasmids, then designated as pCCM' and pCB' plasmids after mutations. The authors should provide more detail on the net result of these mutations, as to whether expression was altered upwards or downwards for the two key plasmids? QPCR would be adequate.

One of the remarkable achievements in this manuscript is to mark out the necessary changes to convert an enteric bacterium into an organism that is dependent on Rubisco for CO2 fixation/carbon gain at limited CO2 levels (and glycerol as an initial carbon backbone). No more than 20 genes are required, possibly less, and clearly all the primary genes to assemble one example of a functional alpha-type carboxysome is now proven because of this experiment. Though there are likely to be some general chaperones required that the host provides.

Reviewer #1:

The photosynthetic efficiency of C3 plants is largely limited by the catalytic inefficiency of rubisco, the CO2 fixing enzyme in the Calvin-Benson-Bassham cycle of photosynthesis. Since rubisco can also react with O2, bacteria, algae and C4 plants have evolved CO2 concentrating mechanisms (CCMs) to increase the concentration of CO2 around rubisco. The CCM promotes carboxylation and inhibits the competitive oxygenation reaction of rubisco. Transplanting CCMs into C3 crop plants is considered a promising strategy to improve rubisco's photosynthetic performance. Bacterial CCMs consist of two essential components: inorganic carbon transporters at the membrane and the proteinaceous shell organelle, carboxysomes. Reconstitution of carboxysomes in E. coli and tobacco have been previously reported, however, there is no report of a functioning reconstituted CCM.

In this paper, the authors introduced 20 CCM-related genes from the proteobacterium H. neapolitanus into E. coli cells which have been engineered to be dependent on rubisco function for growth. Their results show that at most 20 genes are sufficient to generate a bacterial CCM which enables E. coli to grow at ambient CO2 concentration due to efficient fixation of CO2 by rubisco. This manuscript provides a useful platform for future investigations to establish the minimal number of genes required for transplanting the cyanobacterial CCM into non-native autotrophic hosts to improve their CO2 assimilation and growth.

Major comments:

1) 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.

2) In Figure 3-figure supplement 1A, the authors should discuss why the gene csos1D is present in both pCB and pCCM.

3) 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.

4) The negative control in Figure 5-figure supplement 1 is too dark and difficult to compare with the other micrographs. Moreover, to observe recombinant carboxysomes in the positive control (WT:pHnCB10), the authors should have induced the cells using a lower concentration of IPTG as reported previously by Bonacci et. al. (PNAS 2012).

Reviewer #3:

In this manuscript, Peng et al. report three cryo-EM structures of the yeast V-ATPase holoenzyme, two without VopQ and one bound to the bacterial effector VopQ at 3-3.5A resolution. These structures reveal different functional states of the complex, with the ATPase sites adopting either closed or open conformations, supporting a rotary catalytic mechanism proposed previously. Compared to published structures of V1 or V0 subcomplexes and of the rat holoenzyme, the novelty of the authors' study lies in resolving the regulatory subunit H bound to the yeast holoenzyme at near-atomic resolution. Surprisingly, however, little mechanistic insight is provided by the authors into how this key regulator controls V-ATPase activity. For example, what is the structural explanation for why subunit H is essential for holoenzyme activity? How does subunit H inhibit ATP hydrolysis in the V1 subcomplex?

Major comments:

1) The authors refer to states 1, 2 and 3 throughout their manuscript, without ever introducing these states or explaining the differences. While experts in the V-ATPase and F-ATPase field may be familiar with these states, the manuscript in its current form is not well accessible for non-experts.

2) It is unclear why the V0V1 sample without VopQ was prepared with AMPNP, but the one with VopQ contained an equimolar mixture of AMPNP and ADP. For better comparison of both structures, it seems it would have been more appropriate to use the same nucleotide conditions. Related to that, the authors state that VopQ locks the holoenzyme in state 2. How can the authors exclude that the addition of ADP caused this effect, especially since VopQ seems substoichiometric (see below)? If VopQ stabilizes state 2, how is this achieved?

3) The density for VopQ in the authors’ structure is extremely weak, indicating only a subpopulation of particles actually contains VopQ. The authors should try focused classification to better separate VopQ-bound and -free holoenzyme.

4) Page 6: "Therefore, our data also suggests that subunit H is present in possible disassembled V1 subcomplex and in the holocomplex, ..." It is unclear how the authors' structures or ATPase data allows this conclusion. The authors should explain.

5) The authors identify specific interaction pairs between subunit H and subunits in V0 and V1. How do mutations at these interfaces affect V-ATPase holoenzyme stability and activity? Mutational analyses would provide an important validation of the structures and insights into the mechanism by which subunit H regulates V-ATPase activity.

6) The authors mention differences in the stator subunits between the rat and yeast holoenzymes. It would be worthwhile including a figure of this comparison.

7) The atomic models for the three related cryo-EM structures are poorly refined, with clash scores of >40, ~1.5% Ramachandran outliers and 16-17% rotamer outliers. The proteins and ligands in the various models also have unusually low B-factors for the reported resolutions. The authors must properly refine their atomic coordinates. It is also unclear why three different map sharpening factors are listed for each EM map.

Reviewer #2:

In this manuscript, the authors describe cryo-EM structures of the assembled yeast V-ATPase in the presence of the inhibitory nucleotide AMP-PNP and in the presence of VopQ, an inhibitor recently shown to bind to the Vo sector. The structure is reported to be of higher resolution than previous cryo-EM structures of the same yeast enzyme in three rotational states (2015) and the yeast V-ATPase containing the Stv1 isoform (2019), both reported by the Rubinstein lab. As in those structures, there are areas of lower resolution, and the catalytic hexamer shows the highest resolution. Three distinct conformations were observed in the Rubinstein Vph1-V-ATPase cryo-EM structure, potentially corresponding to three rotational states. Here only two states are observed, possibly as a result of the presence of the inhibitory nucleotide. VopQ inhibition of the intact V-ATPase only occurs in the absence of ATP hydrolysis, and the VopQ-V-ATPase structure, obtained in the presence of AMP-PNP and ADP, appears to enrich the State 2 conformation. However, the VopQ itself is very poorly resolved. Overall, AMP-PNP-bound and VopQ-containing V-ATPase structures do provide some new information, particularly the side-chain interactions with subunit H, but several claims are overstated.

The following issues should be addressed:

1) The authors do not give sufficient credit to previous work. The statement on lines 50 and 51, "We describe the cryo-EM structures of the first intact eukaryotic holoenzyme V-ATPase complex (V1Vo)..." is simply not true given the previous yeast structures from the Rubinstein lab. The main advance here is in improved resolution (from 6-8 A to 3.1-3.5 A) for two of three rotational states. Overall, the authors need to do a better job of highlighting what is really novel in their study, starting in the Abstract, which does not highlight the new information in the structures here.

2) The absence of the third rotational state (State 3) is attributed to disassembly of the V-ATPase (lines 64-66). However, this does not make sense given the fact that all three structures were found in the previous studies, and that V-ATPase disassembly is actually inhibited when ATPase activity is inhibited. Instead the absence of this state (which is consistently the least represented) must be associated with either the AMP-PNP inhibition or the number of particles visualized.

3) From their recent structures showing VopQ binding to the membrane Vo subcomplex, it was expected that VopQ would bind to State 2 of the holoenzyme. Unfortunately, the inhibitor could not be visualized well in the context of the intact enzyme, but there appears to be an enrichment and/or stabilization of State 2 of the V1Vo. However, the VopQ-V-ATPase samples also contain both AMP-PNP and ADP, so the authors should at least discuss whether it is the ADP or the VopQ that led to the stabilization of State 2 (especially given apparent low occupancy of VopQ). This structure did allow more detailed view of the subunit side chain interactions with subunit H than was possible previously. However, the suggestion that this structure was the first demonstration that subunit H was present in the holoenzyme (lines 107-109) is not correct, as this subunit co-purifies with intact V-ATPases and was present in previous structures.

4) The suggestion in lines 214-217 that this is the "first direct observation of various conformations of subunit pairs in a V-ATPase holoenzyme" is overstated. Conformational changes due to nucleotide binding have been visualized in even higher resolution crystal structures of the conserved bacterial (E. hirae) V1 (ref. 14).

Reviewer #1:

Structures are reported of yeast V-ATPase. They are similar to previously reported structures of rat and human V-ATPase, and are consistent with previously established mechanistic models. The major advance is that the new structures include subunit H, which is required for activity of the holoenzyme but inhibits ATPase activity in the isolated V1 component. Unfortunately, the structures do not indicate a mechanistic basis for subunit H activity. Another new feature of the current structures is inclusion of the bacterial effector VopQ, which was previously visualized binding to two sites on the isolated V0 subcomplex. Unfortunately, the density of VopQ in the current structures appears to be extremely poor. In summary, although the visualization of subunit H is an advance, the relative lack of new mechanistic insight from the current study diminishes my enthusiasm.

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.

Author Response

Reviewer #1:

Major comments:

1) The title and the conclusion that SON and SRRM2 form nuclear speckles are not supported by the data. The data show that SON and SRRM2 are necessary for nuclear speckle formation. They do not rule out that another factor is necessary, such as SRRM1, which interacts with SRRM2 and itself harbors an intrinsically-disordered domain. That is, the authors have not shown that SON and SRRM2 are also sufficient for nuclear speckle formation. Such a test is necessary to draw the strong conclusion the authors make, and precedence for such a test has been established in the study of Cajal bodies. Specifically, central factors to Cajal body formation were shown to nucleate Cajal body formation at a specific site in chromatin when such central factors were localized to that site. The authors either need to perform such a sufficiency experiment or moderate their conclusions (and title).

2) In principle, in the immunofluorescence studies, the disappearance of mAb SC35 signal on depletion of SRRM2 does not alone prove that SRRM2 is what is visualized by the mAb SC35 in such assays. Given that this paper seeks to establish rigorously that mAb SC35 marks nuclear speckles by recognition of SRRM2, given that SRSF7 is recognized by the antibody on blots, and given that SRSF2 has been traditionally presumed the target of mAb SC35 in nuclear speckles, the rigor of this study demands that SRFS7 and SRSF2 be visualized in cells in the presence of an SRRM2 truncation to rule out that either SRSF7 or SRSF2 phenocopy SRRM2 in this assay.

This is a valid concern and we have thought of the same principal that is if any strongly speckle-associated intrinsically disordered domain containing protein, such as SRRM1 or RBM25, two proteins that are also frequently used as NS markes, would have a similar impact on NS formation as SRRM2 has. To this end, we performed a co-depletion of SON and SRRM1 (shown in Supplementary Figure 10) in a cell line that has a TagGFP2 inserted into SRRM2 gene locus. As it can be seen from the imaging presented in this figure for 4 individual cells (but also more generally on 10 independent field imaged, (data not shown)) we did not score a reduction in the GFP intensity, or dissolution of the spherical bodies as is the case in SON-SRRM2 co-depleted cells. We observed the nuclear speckles have the round-up morphology, that is seen upon SON-KD, but are not dissolved shown with PNN staining and SRRM2-TagGFP signals. Moreover, we performed a co-depletion of RBM25 (another strongly NS-associated protein also used as a NS-marker) and SON which did not result in the dissolution of nuclear speckles (Supplementary Figure 10). Therefore, we have reached to the conclusion that SON and SRRM2 form nuclear speckles with the contribution of SON being more important for the formation and titled our study accordingly.

Traditionally, because of the Fu & Maniatis 1992 paper, as pointed out by the reviewer, it is assumed that SC-35 recognizes SRSF2 in immunofluorescence experiments and potentially multiple SR-proteins in immunoblots. The former point, to the best of our knowledge, has never really been proven in any type of rigorous experiment. Fu lab. has generated SRSF2 K/O mice, but never provided an immunofluorescence image that shows that SC-35 signal disappears in K/O cells.

Just to summarize our line of reasoning here:

1) We do an unbiased IP-MS experiment, which shows that SRRM2 is the top candidate protein, at least an order of magnitude away from any other protein in the dataset by any measure. This strongly suggest that SRRM2 is the primary target of this antibody, although doesn’t prove it due to technical reasons i.e. no input normalization, some proteins produce more ‘mass-specable’ peptides than others, and larger proteins tend to produce more peptides.

2) We carry out a biased screen of 12 SR-proteins and find that SRSF7 is strongly recognized by mAb SC-35

3) We do IP-western blotting experiments, which correct for input and are not affected by relative ‘mass-specable’ peptide issues or protein sizes, which reveal a strong enrichment of SRRM2 (>10% of input), some enrichment for SRSF7 (~2% of input) and no enrichment for SRSF2, SRSF1 or other proteins that we have tested.

4) Since the “35kDa” protein is so engrained with the history of this antibody and our results were most consistent with the idea that this protein is SRSF7 rather than anything else, we insert a degron tag to SRSF7. If the hypothesis is true, then we expect a shift of the SC-35 band, concomitant to the shift in SRSF7, which is indeed the case. This is not proof that SC-35 doesn’t recognize any other protein but it does provide very strong evidence (combined with the other two experiments) that the 35kDa band detected by SC-35 in immunoblots is in fact SRSF7.

5) We then show, by TagGFP2 insertion into the SRRM2 locus, that SC-35 mAb can recognize SRRM2 specifically on immunoblots, and furthermore truncations beyond a certain point completely eliminates this signal. We also show later that siRNA mediated KD of SRRM2 also leads to the elimination of the signal from immunoblots (Supplementary Figure 9).

6) Combining the results so far, we address the issue of immunofluorescence, i.e. which protein or proteins are responsible for this signal. We think there are two possible scenarios that could both be true based on the presented evidence so far:

a. This signal is mainly, if not entirely, originates from SRRM2. b. The signal is a combination of SRRM2, SRSF7 and/or other SR-proteins that the SC-35 might be cross-reacting.

7) We then take advantage of our cell lines with SRRM2 truncations. These truncated SRRM2 version are not recognized by SC-35 mAb on immunoblots, therefore it is reasonable to suspect that they will not be recognized by SC-35 mAb in immunofluorescence as well.

8) If scenario (b) is correct and nuclear speckles are still intact in these cells (which we show that they are indeed intact, judged by SON, RBM25 and SRRM1 stainings Fig. 3A-B), then we would expect either no change in SC-35 signal, or a somewhat reduced signal. We see a complete loss of signal.

9) Being extra careful with this result, we also mix the control cell line and SRRM2-truncated cells and image them side-by-side to address any issues related to imaging settings etc. There is no detectable SC-35 signal in truncated cells.

10) We also show that the 35kDa band is still unchanged in SRRM2 truncated cells (Figure 2E), showing that SRSF7 itself is not affected in these cells.

These results, combined together, show that SC-35 signal in immunofluorescence originates from SRRM2, and any other signal potentially contributed by other proteins are below the detection of immunofluorescence microscopy.

Reviewer #2:

This study reports important evidence that the widely-used SC-35 antibody primarily recognizes SRRM2 rather than the assumed SRSF2. The manuscript provides several lines of evidence supporting this conclusion, and the work has broad impact on the field of nuclear structure and function as this antibody is the most common marker for the major nuclear component, nuclear speckles.

The one concern with the manuscript is the interpretation of some of the previous literature and understanding in the field.

First, since the 1990s it has been widely known that the SC-35 mAb has very limited specificity for denatured proteins and was not suitable for immunoblots (see abcam page for ab11826). Indeed, the assumption has always been that it recognizes a folded epitope. Therefore, the use of western blots to conclude anything about the specificity of this antibody is inappropriate.

Secondly, it has also been previously documented that this antibody has cross-reactivity with SRSF7 (i.e. 9G8; Lynch and Maniatis Genes Dev 1996).

Third, most SR proteins are not abundantly observed in tryptic MS due to high cleavage of RS domains. This is particularly true of SRSF2, which has a highly "pure" RS domain (i.e. all RS repeats) that encompasses almost half of the total protein. SRRM2, on the other hand, has much more complex and degenerate RS domains that encompass a much smaller percentage of the total protein. SRRM2 is also 10x the size of SRSF2. Thus, given equal molar amounts of SRSF2 and SRRM2, one would expect at least 20x the number of peptides and much more complete coverage of SRRM2 vs. SRSF2. Therefore, while the subsequent immunoblot in Figure 1C is compelling evidence that SRRM2 is precipitated with the SC-35 antibody, while SRSF2 is not, the IP-MS data alone is not strong proof that the SC35 mAb primarily recognizes SRRM2 rather than SRSF2. The text should be revised accordingly.

Finally, the abstract implies that the demonstration of SON as a central component of speckles is new ("elusive core"). As appropriately referenced in the text, this is not the case, rather SON is often used as a marker for nuclear speckles, and SON has long been considered to be part of the core of speckles, as knock-down has been documented by several groups to disrupt speckles. The wording in the abstract should therefore be more parsimonious.

With all due respect to all previous researchers that have used mAb SC35 and published their results, we think that the specificity issue has become unnecessarily convoluted due to the initial inaccurate characterization. Abcam’s recommendations highlight the issue in an interesting way. In the old marketing images, abcam shows a single band in a total lysate prepared from HEK293 cells: https://www.abcam.com/ps/products/11/ab11826/reviews/images/ab11826_49518.jpg

However, producing such an image, in our experience as we have also reported in the manuscript, is only possible under non-ideal western-blotting conditions i.e. when the transfer is not adequate to reveal proteins with large molecular weights. Intriguingly, a customer (not us) complains about an improper WB result obtained with this antibody (with a 2-star rating):

https://www.abcam.com/sc35-antibody-sc-35-nuclear-speckle-marker-ab11826/reviews/68414?productWallTab=ShowAll

It looks like an unexplainable high-molecular smear without the information that we provide in our manuscript, but in light of it, it’s clear that protein stained here is SRRM2.

In our experience the antibody works perfectly fine for western blotting, and very specifically and robustly reveals SRRM2 at ~300kDa, as long as the immunoblotting conditions are optimized for large proteins. We also show that bulk of the signal around 35kDa originates from SRSF7, however as indicated by the other reviewer’s comments, and also previous research, the antibody probably cross-reacts with other proteins as well with varying degree.

In this sense, the antibody can be used for immunoblotting, but pretty much any result obtained from such an experiment must be verified with an independent antibody or independent methods, which we did in this manuscript.

The SC35 mAb is actually suitable for western blotting if the gel running and transfer conditions are carefully performed to have SRRM2: a) enter the gel and b) transferred properly to the membrane. Under conditions where SRRM2 is just not entering the gel (due to high percentage gels, or gels with too much bis-acrylamide), or doesn’t get transferred to a membrane (non-ideal buffer conditions, protein stuck in stacking part and cut away etc.), we have seen the unspecific bands, but we had to use the most sensitive detection reagents at hand to see those, so they are rather weak. We have provided a detailed explanation to what these conditions are in the methods section of our manuscript, but briefly: running the gel slowly allowing the protein to enter in the gel and transferring overnight with CAPS buffer were key to get the western blot working. As we have shown in Figure 2C and 2E, the majority of signal detected comes from SRRM2. The unspecific binding of SC35 mAb could only be scored if the above-mentioned conditions were not met.

We believe what made matters historically worse has been the use Mg++ precipitation that enriches many SR proteins, but actually completely depletes SRRM2 (Blencowe et al. 1994 DOI: 10.1083/jcb.127.3.593, Figure 5, https://pubmed.ncbi.nlm.nih.gov/7962048/ ). When we’re sure that SRRM2 is in the gel though, it just shines as a single band. So in conclusion, SC-35 is reasonably specific to SRRM2, especially in immunofluorescence, but it certainly cross-reacts with other SR-proteins, especially when SRRM2 is missing for technical or biochemical reasons.

We will update in the manuscript for the corresponding section by citing earlier studies reporting the specificity issues of mAb SC35.

We absolutely agree that IP-MS data alone is not enough to conclude that SC-35 recognizes SRRM2, or whether it is the primary target or not. The overwhelming amount of SRRM2 peptides detected, in addition to the overwhelming amount of total peptide counts from SRRM2 does strongly suggest that it is the case, which we then followed up by IP-western blotting which controls for relative input, and the various experiments shown in later figures.

We have looked at our MS results and found out that:

SRSF2 was detected with 4 unique peptides with an MS/MS count of 5 and a sequence coverage of 29% (intensity 3E+07), whereas SRRM2 was detected with 227 unique peptides with an MS/MS count of 3317 and a sequence coverage of 61.9% (intensity 2E+11).

These numbers show a 6600 times higher intensity for SRRM2 (not normalized). As the identification and abundance of different peptides/proteins can by dramatically different in MS, it is indeed correct that one should be careful with such comparisons. The only way would be to use peptide standards for both proteins and record standard curves, then a real quantitative comparison would give the true numbers. Hence, we will revise the wording of that section.

Finally, as the reviewer has pointed out, we have not shown that speckles can be reformed by introducing ectopically expressed SON/SRRM2 into cells which now appear not to have nuclear speckles. This would indeed be the formal proof showing that SON/SRRM2 are not just necessary but also sufficient to form nuclear speckles. Such an experiment is quite challenging due to the length of these proteins and difficulty in establishing conditions where one can express these proteins, but not overexpress them which leads to round-up speckles (as shown and discussed by Belmonte lab). Therefore, we will change the title to “SON and SRRM2 are essential for the formation of nuclear speckles” to better reflect our conclusions.

We really did try to be clear and just about the previous literature around SON. Indeed, it is clear that SON is a crucial part of NS, likely the most important component for the integrity of speckles. However, in all of these previous studies, RNAi-mediated depletion of SON, without exception, leaves behind spherical bodies that are strongly stained with mAb SC35, that also harbor other NS-markers (which we also show). This is of course not new, as we also appropriately cited previous work, however being able to dissolve these “left-over” speckles by co-depletion of SRRM2, and perhaps more importantly by deletion of the SRRM2’s C-terminal region is indeed novel.

In essence, our results show that in the absence of SON, as shown by previous work as well, NS-associated proteins are still able to organize themselves into nuclear bodies, indicating that either all other SR-proteins without the need of another organizer clump together, or another factor (or factors) is still acting as an organizer. When we remove the C-terminus of SRRM2, which we show is the primary target of SC-35, which strongly stains these left-over nuclear bodies in the absence of SON, then deplete SON, all NS markers that we could find become diffuse, indicating that nuclear speckles no longer exist, or become too small to be detected or classified as “nuclear bodies”. Co-depletion of SON and SRRM2 leads to the same phenotype, but co-depletion of SON and SRRM1 (or RBM25) doesn’t, leaving behind spherical nuclear speckles that harbor SRRM2 which are no different than SON KD cells.

Reviewer #3:

Nuclear speckles in the last several years have attracted significant attention for their association with transcriptionally active chromosome regions (after largely being ignored by most for the previous 20 years). Overwhelmingly, a single monoclonal antibody has been used as a marker for nuclear speckles for several decades.

This manuscript now argues convincingly that the main target that is recognized by this monoclonal antibody is not SRSF2 (SC35) as long thought, but rather SRRM2. The authors thus clarify a vast literature, while also focusing attention on the very large protein SRRM2 that in many ways resembles another nuclear speckle protein, SON. Both have huge IDRs and unusual RS repeats, while SON has been proposed to act as a scaffold for many SR-containing proteins, which is likely also true for SRRM2, by extension. Moreover, the manuscript provides a convincing explanation for why the target of this antibody was previously misidentified, by showing a lesser cross-reaction with SRSF7, of similar MW to SC35.

Finally, the manuscript suggests that SON and SRRM2 together help nucleate nuclear speckles, as a double KD, or a SON KD in a background of a truncated SRRM2, leads to loss of nuclear speckle-like staining of other proteins normally enriched in nuclear speckles (RBM25, SRRM1, PNN). The authors go on to suggest that this double KD approach will now provide an important means of disrupting nuclear speckles to aid in functional studies.

Interestingly, some of the results of this manuscript actually are already confirmed or consistent with previous literature. For example, a cited paper describes changes in Hi-C compartmentalization patterns after "elimination" of nuclear speckles- actually, they performed a SRRM2 KD and showed loss of SC35 staining, which is now explained as simply due to the KD that they performed. More recently, a new proteomics study of nuclear speckles (Dopie et al, JCB, 2020: https://doi.org/10.1083/jcb.201910207) reported both SON and SRRM2 as the two most highly enriched nuclear speckle proteins, with enrichment scores similar to each other but more than twice that of all other speckle proteins. Moreover, this same paper also did a SRRM2 KD and observed loss of anti-SC35 staining but not SON staining.

Overall, I found this manuscript of significant interest for people in the nuclear cell biology field and technically thorough and well done. I just had one issue and one point to make in my main comments, plus some minor points.

1) The evidence that nuclear speckles are nucleated by SON and SRRM2 is based on the dispersion of staining of nuclear speckle proteins RMB25, SRRM1, and PNN. However, an alternative explanation is that some other protein(s) nucleates nuclear speckles, while these other nuclear speckle proteins bind to SON and SRRM2, and are therefore enriched in nuclear speckles. To eliminate this concern, the authors could show that SON and/or SRRM2 do not bind to these proteins- for instance using co-IP or other methods. Of course, it could be that such binding or scaffolding of nuclear speckle proteins is how they form nuclear speckles. But just one protein that is not bound by SON and SRRM2 but still stains nuclear speckles after the double KD would be inconsistent with their hypothesis. Therefore, if they do find that all these proteins bind SON and/or SRRM2 they could simply discuss this as a scaffolding mechanism but qualify their conclusion based on the alternative explanation described above.

2) In our lab we have not been comfortable using the kinase manipulations, discussed in this paper, to eliminate nuclear speckles for experimental purposes because the cells appear very sick after these manipulations. For other reasons, we also tried a double SON and SRRM2 KD. Our experience is that the cells after this double KD were also not very normal. If the authors are suggesting the SON and SRRM2 double KD as an experimental tool to disrupt nuclear speckles in order to access nuclear speckle function, then it would be valuable for them to indicate cell toxicity, etc. Many SR-protein KDs for example do not allow selection of stable cells. What about this double KD?

The first point of Reviewer #3 has been addressed above in response to the Reviewer #2.

We have stated that our work identifying SON and SRRM2 as the elusive core of nuclear speckles paves the way to study the nuclear speckles under physiological conditions. Here, we have used the cells 24 hours after transfection (~18 hours of knock-down) as the primary reason being that SON-KD caused a mitotic arrest if the cells were kept longer in culture. This was reported earlier in Sharma et al MBC 2010. There was no additional severity in the phenotype when the SON-KD was combined with SRRM2-KD, therefore we believe the arrest phenotype we scored is mainly due to depletion SON. In this sense, double-depletion of SON and SRRM2 can be used to study the effects of loss of NS (transcription, post-transcriptional, topological), but certainly within a time-frame of around 24 hours in cells that haven’t gone through mitosis. We will clarify this statement in the revised manuscript to avoid any misunderstanding as pointed by the reviewer. Faster depletion strategies, and/or a system where cells are mitotically arrested would be required to observe long term effects more reliably.

Reviewer #3:

Nuclear speckles in the last several years have attracted significant attention for their association with transcriptionally active chromosome regions (after largely being ignored by most for the previous 20 years). Overwhelmingly, a single monoclonal antibody has been used as a marker for nuclear speckles for several decades.

This manuscript now argues convincingly that the main target that is recognized by this monoclonal antibody is not SRSF2 (SC35) as long thought, but rather SRRM2. The authors thus clarify a vast literature, while also focusing attention on the very large protein SRRM2 that in many ways resembles another nuclear speckle protein, SON. Both have huge IDRs and unusual RS repeats, while SON has been proposed to act as a scaffold for many SR-containing proteins, which is likely also true for SRRM2, by extension. Moreover, the manuscript provides a convincing explanation for why the target of this antibody was previously misidentified, by showing a lesser cross-reaction with SRSF7, of similar MW to SC35.

Finally, the manuscript suggests that SON and SRRM2 together help nucleate nuclear speckles, as a double KD, or a SON KD in a background of a truncated SRRM2, leads to loss of nuclear speckle-like staining of other proteins normally enriched in nuclear speckles (RBM25, SRRM1, PNN). The authors go on to suggest that this double KD approach will now provide an important means of disrupting nuclear speckles to aid in functional studies.

Interestingly, some of the results of this manuscript actually are already confirmed or consistent with previous literature. For example, a cited paper describes changes in Hi-C compartmentalization patterns after "elimination" of nuclear speckles- actually, they performed a SRRM2 KD and showed loss of SC35 staining, which is now explained as simply due to the KD that they performed. More recently, a new proteomics study of nuclear speckles (Dopie et al, JCB, 2020: https://doi.org/10.1083/jcb.201910207 ) reported both SON and SRRM2 as the two most highly enriched nuclear speckle proteins, with enrichment scores similar to each other but more than twice that of all other speckle proteins. Moreover, this same paper also did a SRRM2 KD and observed loss of anti-SC35 staining but not SON staining.

Overall, I found this manuscript of significant interest for people in the nuclear cell biology field and technically thorough and well done. I just had one issue and one point to make in my main comments, plus some minor points.

1) The evidence that nuclear speckles are nucleated by SON and SRRM2 is based on the dispersion of staining of nuclear speckle proteins RMB25, SRRM1, and PNN. However, an alternative explanation is that some other protein(s) nucleates nuclear speckles, while these other nuclear speckle proteins bind to SON and SRRM2, and are therefore enriched in nuclear speckles. To eliminate this concern, the authors could show that SON and/or SRRM2 do not bind to these proteins- for instance using co-IP or other methods. Of course, it could be that such binding or scaffolding of nuclear speckle proteins is how they form nuclear speckles. But just one protein that is not bound by SON and SRRM2 but still stains nuclear speckles after the double KD would be inconsistent with their hypothesis. Therefore, if they do find that all these proteins bind SON and/or SRRM2 they could simply discuss this as a scaffolding mechanism but qualify their conclusion based on the alternative explanation described above.

2) In our lab we have not been comfortable using the kinase manipulations, discussed in this paper, to eliminate nuclear speckles for experimental purposes because the cells appear very sick after these manipulations. For other reasons, we also tried a double SON and SRRM2 KD. Our experience is that the cells after this double KD were also not very normal. If the authors are suggesting the SON and SRRM2 double KD as an experimental tool to disrupt nuclear speckles in order to access nuclear speckle function, then it would be valuable for them to indicate cell toxicity, etc. Many SR-protein KDs for example do not allow selection of stable cells. What about this double KD?

Reviewer #2:

This study reports important evidence that the widely-used SC-35 antibody primarily recognizes SRRM2 rather than the assumed SRSF2. The manuscript provides several lines of evidence supporting this conclusion, and the work has broad impact on the field of nuclear structure and function as this antibody is the most common marker for the major nuclear component, nuclear speckles.

The one concern with the manuscript is the interpretation of some of the previous literature and understanding in the field.

First, since the 1990s it has been widely known that the SC-35 mAb has very limited specificity for denatured proteins and was not suitable for immunoblots (see abcam page for ab11826). Indeed, the assumption has always been that it recognizes a folded epitope. Therefore, the use of western blots to conclude anything about the specificity of this antibody is inappropriate.

Secondly, it has also been previously documented that this antibody has cross-reactivity with SRSF7 (i.e. 9G8; Lynch and Maniatis Genes Dev 1996).

Third, most SR proteins are not abundantly observed in tryptic MS due to high cleavage of RS domains. This is particularly true of SRSF2, which has a highly "pure" RS domain (i.e. all RS repeats) that encompasses almost half of the total protein. SRRM2, on the other hand, has much more complex and degenerate RS domains that encompass a much smaller percentage of the total protein. SRRM2 is also 10x the size of SRSF2. Thus, given equal molar amounts of SRSF2 and SRRM2, one would expect at least 20x the number of peptides and much more complete coverage of SRRM2 vs. SRSF2. Therefore, while the subsequent immunoblot in Figure 1C is compelling evidence that SRRM2 is precipitated with the SC-35 antibody, while SRSF2 is not, the IP-MS data alone is not strong proof that the SC35 mAb primarily recognizes SRRM2 rather than SRSF2. The text should be revised accordingly.

Finally, the abstract implies that the demonstration of SON as a central component of speckles is new ("elusive core"). As appropriately referenced in the text, this is not the case, rather SON is often used as a marker for nuclear speckles, and SON has long been considered to be part of the core of speckles, as knock-down has been documented by several groups to disrupt speckles. The wording in the abstract should therefore be more parsimonious.

Reviewer #1:

Major comments:

1) The title and the conclusion that SON and SRRM2 form nuclear speckles are not supported by the data. The data show that SON and SRRM2 are necessary for nuclear speckle formation. They do not rule out that another factor is necessary, such as SRRM1, which interacts with SRRM2 and itself harbors an intrinsically-disordered domain. That is, the authors have not shown that SON and SRRM2 are also sufficient for nuclear speckle formation. Such a test is necessary to draw the strong conclusion the authors make, and precedence for such a test has been established in the study of Cajal bodies. Specifically, central factors to Cajal body formation were shown to nucleate Cajal body formation at a specific site in chromatin when such central factors were localized to that site. The authors either need to perform such a sufficiency experiment or moderate their conclusions (and title).

2) In principle, in the immunofluorescence studies, the disappearance of mAb SC35 signal on depletion of SRRM2 does not alone prove that SRRM2 is what is visualized by the mAb SC35 in such assays. Given that this paper seeks to establish rigorously that mAb SC35 marks nuclear speckles by recognition of SRRM2, given that SRSF7 is recognized by the antibody on blots, and given that SRSF2 has been traditionally presumed the target of mAb SC35 in nuclear speckles, the rigor of this study demands that SRFS7 and SRSF2 be visualized in cells in the presence of an SRRM2 truncation to rule out that either SRSF7 or SRSF2 phenocopy SRRM2 in this assay.

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 has yielded two significant contributions. First, the study recharacterized a widely used antibody, mAb SC35, which was initially raised against the spliceosome and characterized both as targeting the 35 kDa protein, SRSF2, an intensely studied splicing regulatory factor, and as marking nuclear speckles, which in the last several years have attracted significant attention for their association with transcriptionally active chromosome regions (after largely being ignored by most for the previous 20 years). The authors present a series of rigorously designed and carefully carried out experiments demonstrating that the 35 kDa factor that mAb recognizes is instead SRSF7. Moreover, the authors present compelling evidence that the primary target of mAb SC35 is a ~300 kDa protein, SRRM2, a spliceosomal factor originally discovered as a nuclear matrix factor and later defined as a nuclear speckle component. In the most convincing experiments establishing these targets the authors show that mAb SC35 signals shift, when the molecular weight of SRSF7 or SRRM2 is varied, and that the signal disappears when SRSF7 is depleted. Given the use of mAb SC35 for nearly three decades, these results suggest that tens if not hundreds of papers require re-interpretation. This study reminds us again of the necessity of rigorous validation of antibodies.

Second, the authors investigate the role of SRRM2 in the formation of nuclear speckles. Previous studies have shown that knock down of the nuclear speckle factor SON leads to a compaction of nuclear speckles but not their entire dissolution, implicating a role for at least one additional factor in nuclear speckle formation; other studies have implicated an array of factors as being required for nuclear speckle formation. Here, the authors show that truncation or knock down of SRRM2, in contrast to several other nuclear speckles factors, also reduce nuclear speckle number, although more modestly than SON, and the truncation or knockdown of SRRM2 in combination with the depletion of SON reduces nuclear speckles more than SON depletion alone. The authors interpret these findings to indicate that SON and SRRM2, both of which harbor intrinsically-disordered domains, form nuclear speckles in human cells, as the title indicates. Further, the authors suggest that the double knockdown provides a new tool to study nuclear speckle function. Overall, this study provides surprising and important insight into a commonly used mAb and valuable new perspectives on nuclear speckles, which have the potential to transform future studies. The study will be of broad interest to those interested in splicing, nuclear speckles, antibody specificity, and more generally, liquid-liquid phase separation.

Reviewer #3:

Serra-Marques and co-authors use CRISPR/Cas9 gene editing and live-cell imaging to dissect the roles of kinesin-1 (KIF5) and kinesin-3 (KIF13) in the transport of Rab6-positive vesicles. They find that both kinesins contribute to the movement of Rab6 vesicles. In the context of recent studies on the effect of MAP7 and doublecortin on kinesin motility, the authors show that MAP7 is enriched on central microtubules corresponding to the preferred localization of constitutively-active KIF5B-560-GFP. In contrast, KIF13 is enriched on dynamic, peripheral microtubules marked by EB3.

The manuscript provides needed insight into how multiple types of kinesin motors coordinate their function to transport vesicles. However, I outline several concerns about the analysis of vesicle and kinesin motility and its interpretation below.

Major concerns:

1) The metrics used to quantify motility are sensitive to tracking errors and uncertainty. The authors quantify the number of runs (Fig. 2D,F; 7C) and the average speed (Fig. 3A,B,D,E,H). The number of runs is sensitive to linking errors in tracking. A single, long trajectory is often misrepresented as multiple shorter trajectories. These linking errors are sensitive to small differences in the signal-to-noise ratio between experiments and conditions, and the set of tracking parameters used. The average speed is reported only for the long, processive runs (tracks>20 frames, segments<6 frames with velocity vector correlation >0.6). For many vesicular cargoes, these long runs represent <10% of the total motility. In the 4X-KO cells, it is expected there is very little processive motility, yet the average speed is higher than in control cells. Frame-to-frame velocities are often over-estimated due to the tracking uncertainty. Metrics like mean-squared displacement are less sensitive to tracking errors, and the velocity of the processive segments can be determined from the mean-squared displacement (see for example Chugh et al., 2018, Biophys. J.). The authors should also report either the average velocity of the entire run (including pauses), or the fraction of time represented by the processive segments to aid in interpreting the velocity data.

2) The authors show that transient expression of either KIF13B or KIF5B partially rescues Rab6 motility in 4X-KO cells and that knock-out of KIF13B and KIF5B have an additive effect. They also analyze two vesicles where KIF13B and KIF5B co-localize on the same vesicle. The authors conclude that KIF13B and KIF5B cooperate to transport Rab6 vesicles. However, the nature of this cooperation is unclear. Are the motors recruited sequentially to the vesicles, or at the same time? Is there a subset of vesicles enriched for KIF13B and a subset enriched for KIF5B? Is motor recruitment dependent on localization in the cell? These open questions should be addressed in the discussion.

3) The authors suggest that KIF5B transports Rab6 vesicles along centrally-located microtubules while KIF13B drives transport on peripheral microtubules. Is the velocity of Rab6 vesicles different on central and peripheral microtubules in control cells?

4) The imaging and tracking of fluorescently-labeled kinesins in cells as shown in Fig. 4 is impressive. This is often challenging as kinesin-3 forms bright accumulations at the cell periphery and there is a large soluble pool of motors, making it difficult to image individual vesicles. The authors should provide additional details on how they addressed these challenges. Control experiments to assess crosstalk between fluorescence images would increase confidence in the colocalization results.

Reviewer #2:

The manuscript by Serra-Marques, Martin, et al provides a tour de force in the analysis of vesicle transport by different kinesin motor proteins. The authors generate cell lines lacking a specific kinesin or combination of kinesins. They analyze the distribution and transport of Rab6 as a marker of most, if not all, secretory vesicles and show that both KIF5B and KIF13B localize to these vesicles and describe the contribution of each motor to vesicle transport. They show that the motors localize to the front of the vesicle when driving transport whereas KIF5B localizes to the back of the vesicle when opposing dynein. They find that KIF5B is the major motor and its action on "old" microtubules is facilitated by MAP7 whereas KIF13B facilitates transport on "new" microtubules to bring vesicles to the cell periphery. The manuscript is well-written, the data are properly controlled and analyzed, and the results are nicely presented. There are a few things the authors could do to tie up loose ends but these would not change the conclusions or impact of the work and I only have a couple of clarifying questions.

In Figure 2E, it seems like about half of the KIF5B events start at or near the Golgi whereas most of the KIF13B events are away from the Golgi? Did the authors find this to be generally true or just apparent in these example images?

In Figure 8G, the tracks for KIF13B-380 motility are difficult to see, which is surprising as KIF13B has been shown to be a superprocessive motor. Is this construct a dimer? If not, do the authors interpret the data as a high binding affinity of the monomer for new microtubules and if so, do they have any speculation on what could be the molecular mechanism? It appears as if KIF13B-380 and EB3 colocalize at the plus ends for a period of time before both are lost but then quickly replenished. Is this common?

Reviewer #1:

In their manuscript, Serra-Marques, Martin, et al. investigate the individual and cooperative roles of specific kinesins in transporting Rab6 vesicles in HeLa cells using CRISPR and live-cell imaging. They find that both KIF5B and KIF13B cooperate in transporting Rab6 vesicles, but KIF5B is the main driver of transport. In these cells, Eg5 and other kinesin-3s (KIF1B and KIF1C) are dispensable for Rab6 vesicle transport. They find that both KIF5B and KIF13B are present on these vesicles and coordinate their activities such that KIF5B is the main driver of the cargos on older, MAP7-decorated MTs, and KIF13B takes over as the main transporter on freshly-polymerized MT ends that are largely devoid of MAP7. Interestingly, their data also indicate that KIF5B is important for controlling Rab6 vesicle size, which KIF13B cannot rescue. Upon cargo switching from anterograde to retrograde transport, KIF5B, but not KIF13B, engages in mechanical competition with dynein. Overall, this paper provides substantial insight into motor cooperation of cargo transport and clarifies the contribution of these distinct classes of motors during Rab6 vesicle transport. The experiments are well-performed and the data are of very high quality.

Major Comments:

1) In Figure 5, it is very interesting that only KIF5B opposes dynein. It would be informative to determine which kinesin was engaged on the Rab6 vesicle before the switch to the retrograde direction. Can the authors analyze the velocity of the run right before the switch to the retrograde direction? If the velocity corresponds with KIF5B (the one example provided seems to show a slow run prior to the switch), this could indicate that KIF5B opposes dynein more actively because KIF5B was the motor that was engaged at the time of the switch. Or if the velocity corresponds with KIF13B, this could indicate that KIF5B becomes specifically engaged upon a direction reversal. In any case, an analysis of the speed distributions before the switch would provide insight into vesicle movement and motor engagement before the change in direction.

2) One of the most interesting aspects of this paper is the different lattice preferences for KIF5B, which shows runs predominantly on "older" polymerized MTs decorated by MAP7, and for KIF13B, whose runs are predominantly restricted to newly polymerized MTs that lack MAP7. The results in Figure 8 suggest a potential switch from KIF5B to KIF13B motor engagement upon a change in lattice/MAP7 distribution. In general, do the authors observe the fastest runs at the cell periphery, where there should be a larger population of freshly polymerized MTs? For Figure 4E, are example 1 and example 2 in different regions of the cell? Do the authors think the intermediate speeds are a result of the motors switching roles? Additional discussion would help the reader interpret the 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 2 of the manuscript. Kassandra M Ori-McKenney (University of California) served as the Reviewing Editor.

Summary:

Serra-Marques, Martin et al. investigate the individual and cooperative roles of specific kinesins in transporting Rab6 secretory vesicles in HeLa cells using CRISPR and live-cell imaging. They find that both KIF5B and KIF13B cooperate in transporting Rab6 vesicles, but Eg5 and other kinesin-3s (KIF1B and KIF1C) are dispensable for Rab6 vesicle transport. They show that both KIF5B and KIF13B localize to these vesicles and coordinate their activities such that KIF5B is the main driver of the cargos on older, MAP7-decorated microtubules, and KIF13B takes over as the main transporter on freshly-polymerized microtubule ends that are largely devoid of MAP7. Interestingly, their data also indicate that KIF5B is important for controlling Rab6 vesicle size, which KIF13B cannot rescue. By analyzing subpixel localization of the motors, they find that the motors localize to the front of the vesicle when driving transport, but upon directional cargo switching, KIF5B localizes to the back of the vesicle when opposing dynein. Overall, this paper provides substantial insight into motor cooperation of cargo transport and clarifies the contribution of these distinct classes of motors during Rab6 vesicle transport.

Reviewer #3:

General assessment:

In this research article, authors claim that HIP1 plays an important role in promoting the proliferative ability of prostate cancer cells by HIP1-STAT3-GDF15 signaling axis activation. HIP1 overexpression increased STAT3 signaling in response to FGF2 receptor activation and increased GDF15 transcription. The increase in GDF15 protein secretion was dependent on HIP1 and STAT3 expression and was shown to have paracrine growth-promoting effects. Although some of the information is new, the relevance and importance of this information is inconclusive and not supported from the data presented in this article.

Major Comments:

This paper needs a substantial amount of revision, as indicated below.

A. Novelty:

HIP-1 has been extensively studied in cancer including prostate cancer (Rao et al., 2002). Its role in STAT3 signaling has also been demonstrated (Hsu et al, 2015). This study is not very novel.

B. Major comments:

1) Figures 1A, S1: Changes in p-AMPK1α, and p-Akt are very profound in this array, however, the authors indicate that "By contrast to our validation of STAT3 phosphorylation by Western blotting, it was not possible to detect increased levels of p-AMPK1α (T174), p-Akt (S473) or p-PLC-γ1 when we attempted to validate these by blotting (Supplementary Figure S1D-F)." Why do the authors think this is happening? Did the authors use the same experimental conditions for the array and validation experiments? These apparent discrepancies need further clarification.

2) Figure 1E: the authors show that shHIP1#2 caused a modest knockdown of HIP1, while shHIP1#1 induced a dramatic reduction in HIP1 protein level, however, both the shRNAs significantly inhibited pSTAT3 to the same extent. This indicates that total knockdown (KD) of HIP1 is not necessary to completely shut-down the activity of pSTAT3. How does this translate to the biological functions of HIP1?

3) How come DMSO treatment blocks the phosphorylation of ERK1/2 in lane 2 of Fig 1(F)?

4) Figure S1F: pSTAT3 western blot: the authors should indicate which band they considered positive for p-STAT3; if it's the lower band why was there no activity in lane 4?

5) Fig 2A and 2B should be repeated in HIP1 knockout cells.

6) What is the endogenous level of HIP1 and GDF15 in prostate cancer cell lines vs. normal prostate epithelial cells? Why was HIP1 overexpressed in LNCaP cells? Was the level of HIP1 expression low in LNCaP and PNT1A, when compared in a panel of prostate cancer cell lines? Did the authors observe any differential expression of HIP1 and GDF15 in hormone sensitive vs. hormone resistant prostate cancer cells?

7) GDF15 is a very ambiguous biomarker of cancer as its levels are even higher in the case of mental disorders including psychosis (for reference https://www.ncbi.nlm.nih.gov/pmc/articles/PMC5554200/ ). And from this study, it is not even clear that the GDF15 upregulation is just one of the several outcomes of the activation of this signaling axis or if it is the only consequence of this signaling axis to promote the growth of cancer cells by increasing paracrine signaling. An experiment in GDF15 knockout cells/mice can document the role of this axis in a more precise manner.

8) It has been shown that wt p53 significantly reduces STAT3 tyrosine phosphorylation and inhibits STAT3 DNA binding activity in prostate cancer cell lines that express both constitutively active STAT3 and mutant p53 protein. The authors have claimed that the increase in STAT3 phosphorylation is due to HIP1 expression. All three of the cell lines evaluated in this paper have different p53 status and show differences in expression of activated STAT3. Is the expression of HIP1 independent of the status of p53?

9) Figure 3: Does STAT3 silencing (siRNA/stattic) downregulate HIP1, and does this decrease STAT3 activation over time? Also, does STAT3 silencing or treatment with WP1066 inhibit HIP1-induced tumor growth in vivo?

10) The role of GDF15 in prostate cancer is likely stage specific. It may promote early stages of tumorigenesis, but suppress the progression of advanced prostate cancers. The authors claim that HIP1 overexpression is mediated by stat3 activation, which leads to increased secretion of GDF15. Does expression of HIP1 correlate with the expression of GDF15 and does this also associate with stage-specific progression of prostate cancer?

11) How was cellular transformation studied and confirmed? Did HIP1 cause transformation of normal prostate cells?

12) Fig 1B: HIP1 western blot is not clear, please quantify 1C, 1D, 1E.

13) Most of the studies are done only in one cell line which is not adequate.

14) What is the clinical relevance of this study? The authors should study clinical samples along with multiple cell lines.

15) Several of the Western blot figures need better quality blots; Figs 1E (FGFR), S2C (all).

Reviewer #2:

The paper describes a novel signaling pathway which links HIP1 and STAT3. HIP1 is an oncolgene which should be targeted in prostate cancer. In previous studies the role of HIP1 in prostate cancer was established. The paper is well-written and the experiments needed to make appropriate conclusions are performed. The paper is also important because of identification of the role of GDF15 in prostate cancer. In my opinion, the paper may benefit from clarification whether HIP1 treatment leads to up-regulation of cytokines such as interleukin-6. This is possible because the effect of HIP1 could also be indirect, i.e. mediated by interleukin-6. No other major revisions are suggested. In general, the paper is an important contribution to understanding of signaling pathways of STAT3 in prostate cancer.

Reviewer #1:

In this manuscript by Rao et al, the authors use an immortalized prostate cancer epithelial cell line, PNT1A, to identify the effects of HIP1 overexpression. The authors show in a series of well-controlled experiments the positive relationship between HIP1, phosphorylation of STAT3, and expression of FGFR4. Phenotypically, this relationship is also associated with pro-tumorigenic events such as in vitro migration and invasion, and development of tumor xenografts. Finally, the authors demonstrate that HIP1 results in increased expression of the GDF15 cytokine to exert its effects on tumor cells in a paracrine fashion.

There are no major concerns with this manuscript.

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 by Rao et al, the authors use an immortalized prostate cancer epithelial cell line, PNT1A, to identify the effects of HIP1 overexpression. The authors define a positive relationship between HIP1, phosphorylation of STAT3, and expression and activation of the FGF2 receptor, FGFR4. Phenotypically, this relationship is also associated with pro-tumorigenic events such as in vitro migration and invasion, and growth of tumor xenografts. Finally, the authors make the case that HIP1 results in increased expression of the GDF15 cytokine to exert its effects on tumor cells in a paracrine fashion.

In general, the paper is well-written, and the results clearly presented. The authors have previously extensively studied HIP1 in cancer, including prostate cancer (Rao et al., 2002). A role for HIP1 in STAT3 signaling has also been demonstrated (Hsu et al, 2015). Hence, the primary novelty and importance of the study is because of identification of role of GDF15 in prostate cancer, and delineation of a tumor-promoting, paracrine HIP1-STAT3-GDF15 signaling axis. While this was viewed as a strength of the study, there were significant weaknesses. Most prominent of the weaknesses was the fact that the bulk of the experiments were performed only in a single cell model, PNT1A, which reduces confidence that the results are generalizable, as opposed to reflecting idiosyncratic signaling response in this model. The consensus of the reviewers was that the key findings of the studies should be further validated in additional cell line models, and/or the relationships proposed should be validated in clinical specimens for prostate cancer. Ideally, both additional cell lines and clinical samples would be used, but at least one is essential to support conclusions. In addition to this important global critique, the reviewers made several specific criticisms of the experiments presented in the study, which should be addressed.

Reviewer #2:

In this paper, the authors describe a web-app that can create, customized, and labeled volcano plots. Technically, from three columns of a CSV file (log fold change, log p-value, and gene name), it displays a scatter plot, with labeled dots. The app (made with shinyR) can be used online or run locally with R/Rstudio. In itself, the app is well done, easy to use, and reactive. Compared to similar existing tools (VolcanoR, Genavi, msVolcano), it is an improvement: it is more intuitive and more "interactive". All that said, it's still a single-use plotting tool, with limited applications, as it avoids doing any statistical analysis on the data.

1) It's not possible to interact directly with the spreadsheet inside the web-app or to select a subset of it, or do simple arithmetic operations on the columns (replacing a log fold-change by a log2 for example).

2) The x-axis cannot be put in log-scale.

3) Being able to export the R code that generates such a plot would be a nice functionality, for those who want to be able to easily use the general look of the plot inside their own pipelines.

4) It would be nice to be able to get q-value from p-values or to measure a false discovery rate.

Reviewer #1:

Goedhart and Luijsterburg developed a R-based web application VolcaNoseR for plotting a kind of scatter plot widely used in transcriptomics/proteomics research(significance vs log fold change), also known as a volcano plot. Using VolcaNoseR it is very easy to create nice-looking, annotated volcano plots, as the GUI provides control of most of the parameters of the plot, such as labels, the significance threshold, the colour schemes etc. Importantly, VolcaNoseR plots are also interactive, which can be used to explore the data and get easy access to any particular gene/protein.

1) As the authors indicated in the very beginning of their paper, volcano plots are used for visualization of large amounts of data. Making scatter plots is possible with almost all existing plotting tools: from MS Excel to specialized packages in R (https://www.bioconductor.org/packages/release/bioc/vignettes/EnhancedVolcano/inst/doc/EnhancedVolcano.html ) and plotly (for interactive plots). The authors make the point that VolcanoseR is unlike all these softwares because it does not require the user to have any programming skills, since it has a custom-tailored GUI. However, producing and correctly interpreting the underlying big data already requires computational/coding skills that far exceed making a scatter plot (especially with many tutorials for the latter available online (https://huntsmancancerinstitute.github.io/hciR/volcano.html )).

2) One of the main features of VolcaNoseR is the ability to make publication ready plots. Yet one will need many more visualisations for any manuscript, than volcano plots. And to do other visualisations (e.g. heatmaps, violin plots and others) potential users will still need to use other plotting tools (and even be proficient in it to match the style of other visualisations in the manuscript with the volcano plot produced by the VolcaNoseR web app).

3) In the part data re-use authors provide a nice example of previously published data, where data points that were not annotated in the source study could be of special interest (Fig. 3). However, I doubt that investigating labels of hundreds of data points one by one on the interactive plot with the cursor is easier, than just filtering underlying source data tables for significant results and searching for genes of interest in the resulting table.

Reviewer #3:

The connection between core transcriptional regulation and tumor metabolism is an area of current interest. The reciprocal regulation of ZBTB18 and CTBP2 has potential value in understanding the functional regulation of lipid biology. However, there are substantial concerns with the studies that limit its rigor and value.

Major concerns:

1) It is advised that the authors consider referencing the International Cell Line Authentication Committee's Register of Misidentified Cell Lines before investing in experiments. The vast majority of critical experiments used only SNB19 (SNB-19). This is a contaminated line and should not be used for studies. The following is from the ATCC:

“SNB-19 (ATCC CRL-2219) and U-373 MG (ATCC HTB-17) - STR analysis at ATCC revealed that SNB-19, a human glioblastoma cell line has a STR pattern identical to that for U-373 MG (ATCC HTB-17). SNB-19 and U-373 MG also share derivative chromosomes. These observations were confirmed with the original stock available to ATCC. Since then distribution of SNB-19 was discontinued. U-373 MG (ATCC HTB-17) - As a result of sequencing, the authenticity of ATCC HTB-17 has been questioned by R.F. Petersson in Stockholm and collaborator E.G. Van Meir in Atlanta (personal communication and see Ishii, N., et al. Brain Pathol 9: 469-79, 1999). They report similarities between U-373 MG (ATCC HTB-17) and another glioblastoma, U-251. The cell line U-373 MG, obtained from the original lab in Uppsala has differing genetic properties from the ATCC HTB-17 (U-373 MG). Following further investigations, ATCC stopped distribution of this cell line.”

It is not only a concern about the naming of the line. The use of a single cell line grown in metabolically artifactual conditions for most of the studies weakens the ability to connect the results to the disease being studied. It also raises concern about global rigor overall. It would have been much better to consider using the BTSC cells for most of these studies. The validation efforts were minimal (sometimes even missing loading controls).

2) Figure 1A, C, D, F: I assume that EV really was with FLAG alone. If not, the comparison should be between FLAG-ZBTB18 and FLAG alone. In each of these studies, there were no replicates and only a single cell line.

3) Figure 1B: Why were CTBP1 and CTBP2 prioritized, instead of other molecules with more peptides?

4) Co-IP of endogenous proteins ZBTB18 and CTBP2 in a panel of cells would be important.

5) The shRNA experiments are poorly controlled. There is a single shRNA used and no rescue studies to address potential off-target effects. All experiments should include better controls.

6) As the authors note, ZBTB18 is expressed at different levels in different glioblastomas, with greater expression in mesenchymal tumors. I would suggest that the authors better consider defining the putative reciprocal function of ZBTB18 and CTBP2 with both loss-of-function and gain-of-function studies.

7) The in vivo studies are limited in scope. There is a single replicate of a single cell line (SNB-19, with the caveats above) with a single shRNA and no rescue studies.

8) It is not surprising that ZBTB18 and CTBP2 have differences in gene regulation, but the current studies make it difficult to fully support the overall model. There are no rescue studies that show the rescue of proliferation or other defects, which would be important for the molecular model.

9) MTOB is a regulator of the methionine salvage pathway, not simply CTBPs. Why wasn't methionine signaling investigated? The rescue efforts for MTOB with ZBTB18 failed, but it would be important to at least validate CTBP rescues.

10) It wasn't clear to me why SREBP signaling was not studied in rescue studies? There is largely an effort to show changes in transcription, but few functional studies to show rescue of metabolism, proliferation, and tumor growth.

11) Figure 4 should include endogenous ZBTB18 IP, as well, with better cells.

12) Figures 4-7 show that the media used for most studies is not really appropriate to study ZBTB18 and CTBP2 function. These efforts should include more consideration of serum-free conditions and in vivo studies, especially as many studies have shown that standard serum conditions with excess oxygen cause artifacts of metabolism.

13) The findings of changes in lipid metabolism are interesting, but quite preliminary. Lipid droplets have been strongly linked to aggressiveness in gliomas. The quantification does not show very strong differences. It would be important to show that the differences in lipid biology explain the effects of ZBTB18 and CTBP2 on tumor cell metabolism and proliferation. Are these findings the driver or passenger of effects?

14) I would suggest that the authors consider deeper in silico efforts to examine target expression and patient outcome or genetic events.

Reviewer #2:

In this manuscript, the authors claim that ZBTB18 interacts with CTBP2 and represses SREBP target genes to inhibit fatty acid synthesis in glioblastoma. However, the mechanisms presented in the manuscript are not convincing. This is because there are several major concerns for their conclusions as described below.

1) It looks that Figure 1D shows almost no endogenous interaction between CTBP2 and ZBTB18 when α-CTBP2 was used. This is perhaps because their cell lines may express very low ZBTB18 levels. Moreover, in reciprocal IP experiments using cells with FLAG-ZBTB-18 overexpression, α-ZBTB18 IP shows weak CTBP2 band that is inconsistent with the CTBP2 band in Figure 1C. In addition, this manuscript relies too much on results that were generated from overexpression for the tumor suppressor candidate gene ZBTB18.Therefore, it is possible that many results in this manuscript may represent artificial results based on FLAG-ZBTB18 overexpression. Of note, knockdown or loss-of-function experiments are generally better for a tumor suppressor genes.

2) ZBTB18 is a transcriptional repressor. CTBP2 is a transcriptional corepressor that interacts with LSD1 and other repressive proteins, although it may act as a transcriptional activator via the association with certain factors. If ZBTB18 interacts with CTBP2, it is reasonable to think that they would cooperate for gene repression and is also worthy to compare the effect of ZBTB18 knockdown with that of CTBP2 knockdown on gene expression. However, without a good rationale, authors compared the effect of ZBTB18 overexpression with that of CTBP2 silencing on gene expression. In this regard, they should have also compared the effect of ZBTB18 knockdown with that of CTBP2 knockdown on gene expression. If ZBTB18 knockdown is not suitable because of its low expression in their cell lines, they may have to use a different cell line.

3) LSD1's role: LSD1 can demethylate H3K4me2 and H3K4me1 but not H3K4me3. It may demethylate H3K9me2 in certain contexts (for example, upon the interaction with AR). Authors said "H3K9me2 is a well-established target of LSD1 demethylase activity" and then examined the effect of ZBTB18 overexpression on LSD1, H3K9me2, and H3K4me3 (but not H3K4me2) using quantitative ChIP. Authors should have checked H3K4me2 as well. Nevertheless, their results showed that ZBTB18 overexpression increased LSD1 and H3K9me2 but decreased H3K4me3. Authors then mentioned "a possible explanation is that the recruitment of CTBP2 complex by ZBTB18 to its target sites inhibits LSD1 demethylase activity and might be employed by ZBTB18 to counteract CTBP2-mediated activation.” However, another possibility would be that increased recruitment of ZBTB18 and LSD1, maybe along with CTBP2, would increase the repressive mark H3K9me2 but decrease the active mark H3K4me3. Perhaps, consistent with the latter possibility, authors mentioned that CTBP2 has been linked to the inhibition of cholesterol synthesis in breast cancer cells through direct repression of SREBF2 expression. To clarify this issue, authors need to show the effect of LSD1 knockdown on expression of SREBP target genes as well as on HDAC1/2, H3K4me2 and H3K9me2 levels at these genes.

Note: authors measured the LSD1 activity in nuclear lysates using a commercial kit. This assay is based on LSD1-mediated H3K4 demethylation but not H3K9 methylation. However, the purpose of this experiment appeared to show the effect of ZBTB18 on LSD1 activity for H3K9me2 demethylation. It is not clear that this was an appropriate use of this assay.

4) Some results are not entirely novel. For example, previous studies from authors and other groups showed that ZBTB18 negatively affected proliferation of cancer cells (Figure S2). In addition, other previous studies have reported that CTBP2 promotes tumorigenesis for hepatoma and may be a glioma prognostic marker (PMID: 27698809) (Figures 2I & 2J). LSD1-interacting proteins (Figures 4A-4C) have been known.

5) Many labels and legends for the figures should have been better described as they are often confusing and difficult to read. Along with this, many figures should have been better presented. Some examples are as follows:

• What is the protein number in Figure 1B?

• For multiple figures (Figures 2H, 3H, 3G & 3H, 4D-4I, 5C, etc), there are no statistical analysis.

• Authors should have better labelled to present their figures. For example, to present transfection and ChIP in Figure 3G, authors may want to use the labels as follows: EV + IgG; EV + α-FLAG; FLAG-ZBTB18 + IgG; FLAG-ZBTB18 + α-FLAG (instead of IgG_EV; FLAGEV; IgG ZBTB18; FLAG_ ZBTB18, respectively).

• In Figure 7E, SREBP target genes would be better than SREBP genes

Reviewer #1:

This manuscript explores the mechanism by which ZBTB18 regulates the expression of SREBP genes in glioblastomas. The authors use IP and MS experiments to identify CTBP2 as a new ZBTB18 binding protein. ChIP-seq shows some overlaps of CTBP2 with ZBTB18 largely on gene promoters. CTBP2 activates, while ZBTB represses the expression of some SREBP genes. ZBTB18 disrupts the CTBP2/LSD1 complex leading to increased H3K9me2, decreased H3K4me3, and gene silencing. SREBP proteins are transcription factors that control the expression of enzymes involved in fatty acids and cholesterol biosynthesis. Consequently, ZBTB18 expression leads to reduction of several phospholipid species. Overall, although this manuscript demonstrates the role of ZBTB18 in suppressing lipid synthesis and storage and a potential oncogenic role of CTBP2 in glioblastoma cells, the mechanism underlying its regulation of gene expression is still not clear.

1) According to the model, CTBP2 binds at SREBP gene promoters to maintain active transcription; expression of ZBTB18 enhances its binding to other LSD1 complex components and their chromatin association, however, on the contrary, ZBTB18 inhibits the enzymatic activity of LSD1 thus to repress gene expression. This model itself is seemingly paradoxical. Why does CTBTP18 recruit a corepressor (such as LSD1) and then inhibits its repressive function? Does LSD1 indeed function as a co-repressor or co-activator? Is its enzymatic function required?

2) LSD1 is well-known for its demethylation activity against H3K4 mono- and di-methylation; its demethylase activity on H3K9 is far from clear. The data as presented does not rule out the possibility that LSD1 is a co-repressor of ZBTB18.

3) The enzymatic assay in Figure 4J is preliminary. In vitro enzymatic assays using pure proteins with proper controls are necessary.

4) The analysis of ChIP-seq data is preliminary. In Figure 3B, there are close to 12K peaks of CTBP2 binding sites (EV-CTBP2 only) that are lost upon co-expression of ZBTB18, and these peaks are not bound by ZBTB18. How does this happen? Also, there are close to 10K of gained CTBP2 binding sites upon coexpression of ZBTB18, half of which are bound by ZBTB18. What are these peaks? I did not find information on how many repeats are done for each ChIP. If only once, this may simply reflect huge variations between experiments. Basic analysis to access the quality of ChIP-seq is also not shown.

5) Supplementary Figure 6A does not tell whether there is a good overlap between ZBTB18 bound peaks and the bindings of CTBP2 interactors (NCOR1, ZNF217 and LSD1). Vann diagrams need to be used to show overlaps with P-values.

6) The entire study relies on overexpression of ZBTB18. Complementary knockouts using CRISPR in cells expressing ZBTB18 are needed.

7) All Western blots miss protein standard markers. Percentage of input is also not labelled making it difficult to judge how strong the ZBTB18 and CTBP2 protein-protein interaction is.

Author Response

This paper analyzes the evolution of the KRAB-containing zinc finger protein (KZFP) family of proteins. While the reviewers were all interested in the topic, several major concerns came up during review. These include technical limitations of the methods chosen to analyze this challenging protein family (e.g., determination of orthology, selection analysis, and so on), and that new ideas, including claims about non-coding evolution and positive selection, are not convincingly supported by the analysis presented.

Response: In our study, we focused on the co-evolution between zinc fingers in KZFPs and non-TE regions, not ‘non-coding regions’. Non-TE regions are located in both coding and non-coding regions.

Reviewer #1:

1) The title and abstract make it clear that the authors are trying to argue that non-coding sequence contributes to rapid evolution of the KRAB-ZFP family….

Response: As we mentioned above, we focused on the co-evolution between zinc fingers in KZFPs and non-TE regions, not ‘non-coding regions’. Non-TE regions are located in both coding and non-coding regions.

5) Page 6 line 122: The authors do not define, here or in the methods, what constitutes a "variant" KRAB domain.

Response: In fact, the meaning of variant KRAB domains had been simply described here (Page 6, line 120-122). The variant KRAB domains display a very significant degree of sequence divergence from the KRAB A-box consensus sequence, and variant KRAB domains are clustered into one separated branch in the phylogenetic tree of KRAB domain A-box amino acid sequence. This description was similar to that in the reference (Helleboid et al., 2019). We will explain it more detailly in method section in the further revision of the manuscript.

8) Page 9 lines 189-193: Does the 90% cited here refer to 90% of the ~50% that are called as "tending to bind non-TE sequence" or 90% of all KZFPs? Regardless, this point is very misleading: the fact that less than 50% of the binding sites of a KZFP is not found to overlap TEs does not mean that the KZFP only binds to non-TEs.

Response: Here, ‘90%’ refer to 90% of all KZFPs. We did not state that ‘less than 50% of the binding sites of a KZFP is not found to overlap TEs means that the KZFP only binds to non-TEs’. Instead, we mean that they tend to bind to non-TEs.

12) Page 11 lines 249-251: 1) It is not clear how the author defined genes as transcription factors (they also do not define the acronym), or why they included them in the analysis. 2) Additionally, the authors say that the divergence time of KZFPs is correlated with expression level but does not provide correlation values or the significance of these correlations.

Response: 1) Since KZFPs can bind to target genes and regulate their transcription, most of them are regarded as potential transcription factors. To confirm whether the special features of KZFPs found in our study are KZFP-specific or common to all transcription factors, we compared KZFPs with other transcription factors. The data source of transcription factors was described in the method section (page 18, lines 422-424). 2)We showed the correlation values in figure 4A and the corresponding P values were listed in Figure 4–source data 1.xlsx.

15) How were the target genes selected for qPCR validation among the KZFP targets? 2) In Fig.5 suppl. 3 the authors show that there is a fraction of genes that is only accessible in ESCs, but there is also a similar number of genes that is accessible both in ESCs and HEK293T cells, so the authors could have tried to validate some of those in both cell lines...

Response: 1) We screened the target genes with significant changes in the expression level from ESC into endoderm or mesoderm for qPCR validation. 2) Indeed, we have performed some validations (Fig.5 suppl. 1)

16) Page 16 lines 367-373: The conclusions that can be drawn from the ZNF611 reporter assay and associated evolutionary analysis are minimal. …There is almost no experimental methodology on how the tree was generated, how the authors overcame these issues, and how the authors identified the orthologous binding site in different species.

Response: Sequence alignments were performed using ClustalX (version 2.1) with default parameters (Larkin et al., 2007), and the phylogenetic tree (neighbor-joining tree) was constructed using MEGAX (Kumar, Stecher, Li, Knyaz, & Tamura, 2018) with default parameters. To identify the orthologous binding site in different species, firstly, we found the ZFN611 binding site in the ZNF611 ChIP peak sequence in STK38 promoter according to the predicted ZNF611 binding motif in human. Then we compared the ZFN611 binding site within the promoter of orthologous STK38 in different species.

17)There is not enough detail about how the human KRAB-ZFPs were identified. Bare minimum, the authors need to report thresholds used to determine if a protein's domains scored high enough to be either a KRAB or C2H2 ZF domain.

Response: All KRAB domains and C2H2 zinc fingers in human proteins were identified using HMMER v3.1b2 with E value < 0.01. The proteins containing both a KRAB domain and C2H2 zinc fingers were defined as KZFPs. This method was not described clearly in the manuscript (page 18). We will add detailed description of that in the revision.

20) How the authors performed the gene ontology enrichment/depletion analysis is not clear. For example, if the authors indeed prefiltered their list to remove genes that have no GO terms, that would bias the results.

Response: This has been described in the method section (page 23, lines 530-532). The genes that haven’t GO term annotation were filtered out. It’s also needed that the genes were expressed at least in one sample. These genes were regarded as the background of the enrichment/depletion analysis. This strategy was used widely in published papers.

Reviewer #2:

It is not clear how the authors identified KRAB-ZNF genes in the 80 species analysed, nor how they defined orthology relationship of KRAB-ZNF genes.

Response: The methods were described in lines 425-443 (page18-19). To identify the divergence time of KRAB domain in human KZFPs, protein sequences of 80 species from 80 genera in deuterostomia were downloaded from Ensembl database. All KRAB domains and C2H2 zinc fingers in proteins were identified using HMMER v3.1b2 with E value < 0.01. The proteins containing both a KRAB domain and C2H2 zinc fingers were defined as KZFPs. The divergence time of the full protein sequence was inferred according to the homology information from Ensembl Compara (Herrero et al., 2016; Vilella et al., 2009).

it is puzzling that the divergence time of the full protein sequence can be estimated above 400 Mya, while the root of the KRAB-ZNF gene family has been assigned to the common ancestor of coelacanths, lungfish and tetrapods (Imbeault et al., 2017).

Response: the root of the KRAB-ZNF gene family in the research (Imbeault et al., 2017) was based on the earliest appearance of the gene encoding both KRAB domain and zinc fingers. However, the divergence time of the full protein sequence based on pairwise alignments, Large-scale syntenies and Enredo-Pecan-Ortheus (EPO) multiple alignments (Herrero, et al., 2016). Thus, some of the orthologous proteins of human KZFPs do not containing a KRAB domain.

Peaks filtering should include, at the very least, the canonical ENCODE blacklisted regions (Amemiya et al., 2019)

Response: we have used the corresponding total input samples as controls to get credible peaks.

Of note, numerous ChIP-seq datasets from ENCODE are listed in the method, but are not referenced or mentioned in the text. Were those included in the ChIP-seq binding sites analysis? How do the two datasets (ENCODE and Imbeault et al., 2017) relate to one another?

Response: ChIP-seq datasets from ENCODE are included in the ChIP-seq binding sites analysis. We firstly used the ChIP-seq data in Imbeault et al., 2017, and ChIP-seq datasets from ENCODE were used as supplements of the ChIP-seq data of other KZFPs.

No details are given regarding the method used to assign "the expression level grade" of genes to a specific category.

Response: The threshold wasn’t described clearly in the manuscript. Genes with read counts over 10 are considered to be expressed, while genes with read counts less than 10 are considered to be unexpressed (undetected). For each dataset, we used the upper and lower quartiles of TPMs of all expressed genes to divide them into three expression level grades: low-abundant genes, the genes with TPMs lower than lower quartile; medium-abundant genes, the genes with TPMs between the lower quartile and the upper quartile; high-abundant genes, the genes with TPMs higher than the upper quartile.

The KD efficiency of ZNF611 is really poor (<20%, Figure 6B), and prevents further conclusions on this experiment (especially since a western blot cannot be performed). We are also sceptical about the statistical analysis performed in this panel. The authors should explain in detail which t-test was used and whether it was performed on raw or normalized values.

Response: The statistical method was described in the figure legend. We used grouped t test. And it was performed on normalized values (relative mRNA levels of predicted target genes were normalized to GAPDH).

Reviewer #3:

This paper gives the impression that it is two stories bundled together into one. One story is the evolution of the family and the other one is the experimental part focusing on a very specific KFZP, ZNF611. However, it is a rather weak synthesis with results of moderate interest and likely low phenotypic impact.

The authors state that the KFZP family is coevolving with TEs and suppresses their expression. According to previous knowledge, that is why this family is evolving so fast. However, the authors argue that this fast evolution is further attributed to the fact that KFZPs also positively regulate the promoters of other non-TE genes. They have analysed published Chip-seq data toward this end. Furthermore, they have experimentally identified that a "young" KFZP, ZNF611 can bind to a promoter element of the STK38 gene and positively regulate its expression in ESCs. However, I did not see substantial experimental evidence supporting a strong phenotypic effect of this particular regulation.

Reviewer #2:

This work interestingly addresses the evolutionary pressures undergone by KRAB-ZNF genes. However, a large part of the manuscript is based on the analysis of pre-existing datasets, but neither exploits these data in new ways nor reveals novel findings overlooked in the original studies. The authors' findings are not a significant addition to the conclusions made by the original investigations, which are, by the way, not properly referenced and often misquoted. Moreover, when the authors attempt to build a systematic method for the identification of non-TE related / activating functions for KRAB-ZNFs, the experimental validation tends to point to few regulatory exceptions rather than general principle for the KRAB-ZNF family. The paper finishes by the analysis of a single non-TE target of a young KRAB-ZNFs, ZNF611, which is clearly not the best candidate considering the proposed model of bimodal evolution of KRAB-ZNFs (old vs. young). The picture that comes out of this manuscript is that of a patchwork of analyses that struggle to stand together as a whole.

Major points:

Figure 1 / Comparison of the divergence time of the full sequence, KRAB domain and zinc fingers in KZFPs: The method section is not very clear, which suggests that the authors may have done their analysis by relying on pre-existing database annotations which could bias the estimation of the divergence time.

-It is not clear how the authors identified KRAB-ZNF genes in the 80 species analysed, nor how they defined orthology relationship of KRAB-ZNF genes. This should precede the estimation of the divergence time. Methods to infer orthology for KRAB-ZNF genes has been based the on best reciprocal hit of the full protein-sequence by Blast (Liu et al., 2014) or on KRAB-ZNF fingerprint (Imbeault et al., 2017). Is it based on Ensembl? It is known that Ensembl has a poor annotation of KRAB-ZNF genes especially in distantly related species with human. Clarification is needed regarding de novo KRAB-ZNF gene detection, annotation and comparison in the method section.

-Related to this, it is puzzling that the divergence time of the full protein sequence can be estimated above 400 Mya, while the root of the KRAB-ZNF gene family has been assigned to the common ancestor of coelacanths, lungfish and tetrapods (Imbeault et al., 2017). In addition, some of the oldest KRAB-ZNF genes found in the human genome are ~320 Mya (Liu et al., 2014). How do the authors reconcile this with the estimation of the full protein divergence time?

Figure 2 / The diversification pattern of KRAB domains and zinc fingers in humans: The authors suggest that old KZFPs tend to have a variant KRAB variant domain and thus are involved in non-canonical protein-protein interactions. This analysis has been entirely made in Helleboid et al., 2019, who further validated these results by identifying the interactome of these proteins by mass-spectrometry. Considering the timeline of this submission and the release of the original paper, the authors could have modified their conclusions. They could also have taken greater advantage of non-overlapping findings, such as the disordered nature of the variant KRAB domain. This is interesting but under-exploited.

Figure 3 / KZFPs tend to bind to non-TE regions in exon and promoter: The analysis of pre-existing data from different sources come with considerable drawbacks, notably in terms of unforeseen experimental artifacts and biases, which could affect peak calling, data interpretation and conclusion. As such, KZFPs may display promiscuous binding to unrelated "opened" regions, especially when they are overexpressed in a non-native context (Amemiya et al., 2019; Marinov et al., 2014). While the authors tested different parameters of the ChIP-seq analysis pipeline, I do not see any attempts to assess the overall reliability of KZFPs peaks within open regions in the method section or in supplementary figures:

-Peaks filtering should include, at the very least, the canonical ENCODE blacklisted regions (Amemiya et al., 2019). Additional steps of filtering should be included such as building background models that are experiment-specific and cell-type specific, as it has been done in the past (Helleboid et al., 2019; Imbeault et al., 2017; Schmitges et al., 2016). Does it change the overall proportion of peaks falling into TE/non-TE regions?

-As emphasized in the manuscript, targets of KRAB-ZNFs are expected to be highly specific (Schmitges et al., 2016) as only few of them display similar key amino-acids in their ZFs (Figure 2E/F) and may depend on the appearance of their binding site in evolution (Figure 6). As such, only a minimal overlap of non-TE targets peaks is to be expected for different KRAB-ZNFs proteins: it is likely that non-TE targets bound by many KRAB-ZNFs may result from promiscuous binding sites. The authors should show the overlap of non-TE targets bound by different KRAB-ZNFs before and after filtering steps.

-As a consequence, these promiscuous binding sites would skew the results of the over-/under-representation of genes in specific biological processes (as presented in Figure 3D) and gene essentiality tolerance (in Figure 3E). What would be the result of these analyses once peaks and gene lists are filtered? Similarly, what would be the result if only promiscuous binding sites were considered?

-Of note, numerous ChIP-seq datasets from ENCODE are listed in the method, but are not referenced or mentioned in the text. Were those included in the ChIP-seq binding sites analysis? How do the two datasets (ENCODE and Imbeault et al., 2017) relate to one another?

Figure 4 / KZFP genes encoding young zinc fingers tend to have higher expression level in early embryonic development and the ESC differentiation into mesoderm:

-The author should refer to previous work on young KZFPs expression during human embryogenesis (Pontis et al., 2019) when they introduce this section. This is especially important since the TE-controlling function of ZNF611 has been investigated in this study, and is not discussed or mentioned in Figure 6.

-No details are given regarding the method used to assign "the expression level grade" of genes to a specific category. Is it common arbitrary thresholds used for all genes or is it based on something similar to a z-score value ? Clarification is needed.

Figure 5 / KZFPs can positively regulate target genes by binding to non-TE regions in endoderm or mesoderm differentiation: We would suggest the authors reorganize the figure 5 to bring their strongest evidence of KRAB-ZNFs activating function in the main figure. For instance, genes over/under-representation (Figure 5C) and essentiality (Figure 5D) are not very informative. On the other hand, the Figure 5-figure supplement 1D/E could be presented in the main figure as it reinforces the link between chromatin accessibility and regulatory activities of KRAB-ZNFs in non-TE regions. Of note, while the authors may conclude to regulatory differences between ESC and HEK293, it would be farfetched to superimpose their conclusions to mesoderm and endoderm differentiation without experimental validation. Therefore, the authors should tone down their conclusion in the corresponding section.

For the KRAB-ZNFs functionally investigated in Figure 5-figure supplement 1D/E, the authors should highlight :

-Their divergence time, the type of KRAB domain, their known interactors and endogenous expression levels in ESCs, HEK293, during endoderm and mesoderm differentiation (it is impossible to zoom in Figure 4).

-The proportion of peaks falling in TE/non-TEs region and their associated chromatin accessibility in the different cell types (such as plotHeatmap function from the deepTools suite).

-The correlation matrix of the chromatin accessibility signals in non-TE binding sites between the two cell lines should be displayed for all the KRAB-ZNFs functionally investigated.

Figure 6 / The emergence of new sequence in STK38 promoter may drive the evolution of zinc fingers in ZNF611: While the emphasis on KZFPs divergence time and KRAB domain feature is clear in the first part of the manuscript, the shift toward the functional assessment of a young KRAB-ZNF is somehow inconsistent and should be explained.

-As mentioned above for the KRAB-ZNFs of Figure 5-figure supplement 1D/E, ZNF611 features (divergence time,...) should be displayed in the figure or stated in the text. The number of peaks of ZNF611 in non TE/ non-TE regions should be plotted. Also, previous work on ZNF611 function during embryogenesis should be introduced in this section.

-ZNF611 expression during mesoderm differentiation (with corresponding correlation) and ESCs should be added to Figure 6-figure supplement 1A.

Overall, the effect of ZNF611 overexpression or knock-down appears to be mild, and should be reinforced by additional information:

-Considering the discrepancy of the effect of ZNF611 overexpression and knock-down on the level of STK38 (Figure 6A/B): (i) a western blot analysis of ZNF611-FLAG protein levels in overexpressing cells (like in Figure 5 - figure supplement 1C) could indicate that the overexpression of the protein is actually mild compared to overexpression mRNA levels of ZNF611. Similarly, a previous study analysed the effect of ZNF611 overexpression in hESCs (Pontis et al., 2019), is STK38 upregulated in those datasets? That would reinforce the conclusions made by the authors.

-The KD efficiency of ZNF611 is really poor (<20%, Figure 6B), and prevents further conclusions on this experiment (especially since a western blot cannot be performed). We are also sceptical about the statistical analysis performed in this panel. The authors should explain in detail which t-test was used and whether it was performed on raw or normalized values.

-Since the BMPR2 gene remained unaffected by ZNF611 "KD" or "overexpression", could the authors show / perform the same analysis as for STK38 promoter region in Figure 1C-D for this gene?

-The authors emphasize that ZNF611 functions in mesoderm differentiation through STK38 regulation. This analysis was conducted in the pluripotent state (hESCs). What about the differentiation potential of these cells toward the mesoderm lineage? Does it prevent STK38 upregulation?

-The authors have shown that KRAB-ZNF effect is largely cell type dependent (figure 5 - figure supplement 1D/E), while the experimental assessment of ZNF611 was done in ESCs, the luciferase assay was performed in HEK293 (figure 6H-I). The authors should repeat the experiments in ESCs or tone down their conclusions.

-Interestingly, RACDE use TE-related sequences to identify the binding motif of KRAB-ZNFs, suggesting that the binding motif of ZNF611 to STK38 promoter is fairly similar to its TE-derived consensus motif (figure 6F). How many binding sites of ZNF611 in non-TE region present binding sites with a close similarity to the consensus motif derived from TE-binding? Are there changes in specific DNA bases of the canonical binding site motif that could predict activating function of ZNF611 in non-TE regions?

Reviewer #1:

Summary:

In this study, the authors seek to determine patterns of KRAB-ZFP family evolution and identify the factors that drive those patterns. To do so, they first annotated KRAB-ZFP genes in the human genome and determined the age of these genes in four different ways: orthology, divergence age of full protein, KRAB, and ZnF domain respectively. They found that age estimates based on the KRAB domain and Zinc finger array were older and younger, respectively, relative to full-length or orthology-based estimates of divergence, and that many human KRAB-ZFPs emerged in the eutherian common ancestor. They also determined that older KRAB-ZFPs were more likely to have variant, disordered KRAB domains, and that zinc finger arrays were most variable at the residues directly in contact with DNA. By reanalyzing existing data, the authors claim that most KRAB-ZFPs bind to non-TE regions, and that many KZFP genes are expressed during early embryonic development. They show correlative evidence that KRAB-ZFPs are capable of positively regulating gene expression, and functionally validate a single candidate gene of a KZFP using reporter gene assays. Based on this evidence, they propose a 2-way model of evolution of KRAB-ZFP evolution, where older KRAB-ZFPs are more likely to have non-TE silencing roles and thus have different patterns of evolution compared with younger KRAB-ZFPs.

General Comments:

While the subject of KRAB-ZFP family evolution is of interest, the data and conclusions the authors present in this manuscript are mostly confirmatory. Nearly every major conclusion of the paper, including the 2-way model of KRAB-ZFP evolution, has been extensively documented before by the Trono lab (Imbeault, et al. 2017 Nature; Helleboid, et al. 2019 EMBO J; Ecco, et al. 2017; Pontis, et al. 2019), many of which the authors cite. The conclusion that older KZFPs gained new functions not related with TEs repression (such as imprinting regulation or meiotic hotspot determination) is already well established knowledge, which goes together with the model of higher purifying selection of the zinc finger array to retain the binding specificity, while the KRAB domain loses interaction with KAP1. Furthermore, the fact that KZFPs don't only bind to TEs has also been already reported by Imbeault et al. that originally provided the datasets re-analyzed in this manuscript.

The functional validation of ZNF611 binding to one of its target sequences is welcome and adds another example of a KRAB-ZFP that might have positive transcription regulatory function, however it is only a single KRAB-ZFP in a single assay. The finding that a KRAB-ZFP is capable of activating gene expression is also confirmatory (Ye at al. 2004; Frietze et al. 2010; Hallen et al. 2011).

There is value in replicating existing research, but the article is not written with that in mind. One contrast with previous studies is that their reanalysis of existing ChIP-seq data showed KRAB-ZFPs primarily bind to non-TE regions. However, these findings are based on thin evidence. It is not enough to say that a KRAB-ZFP mostly binds non-TE regions because >50% of its binding sites are outside of a TE. Rather, more quantitative statistics, such as enrichment or depletion of binding in a given genomic compartment compared to a random expectation is required. Additionally, there is no evidence such as heatmaps or metaplots over a subset of peaks to further demonstrate that the peaks identified in the new analysis are any better than the previous analysis. The authors argue that the more significant p values of their peaks are indicative of better peak calls, but there is no formal comparison of true/false negative rate (such as at known binding sites). Furthermore, many TEs, which are poorly mappable, will have less significant p values simply because fewer unique reads are mapped there relative to unique sequences. More careful analysis will be needed to assess these claims.

Finally, the paper itself is hard to read and the logic is difficult to follow, often due to a lack of sufficient detail. The methodology is also light on details, making it challenging to understand exactly what the authors did or did not do (see specific examples below). Additionally, the figures (especially Figure 1, Figure 3A, and Figure 4) are difficult to read and understand as currently presented.

Specific Comments:

1) The title and abstract make it clear that the authors are trying to argue that noncoding sequence contributes to rapid evolution of the KRAB-ZFP family. While this is possibly true, the authors' data, which is limited to a phylogenetic analysis of a single gene (using methodology that does not work well for highly repetitive sequences such as the KRAB-ZFP C2H2 zinc finger array) and its potential binding site. Much more analysis (such as selection analysis of more KRAB-ZFPs and their predicted or empirically determined binding sites) is required to make this claim.

2) Page 4, lines 66-70: The authors present the two possible models of KRAB-ZFP evolution (ie: arms race/domestication model) as if they are mutually specific, when most argue they would not be. Also, the authors state: "and (2) the domestication model (Ecco et al., 2017; Pontis et al., 2019), in which KZFPs regulate domestication of TEs instead of restraining the transposition potential of TEs". This should be rephrased, because in most of the cases reported, the "domesticated TEs" have lost transposition potential and only regulatory and protein coding sequences got domesticated with new functions. If the authors were referring to the adaptation of KZFPs to non-TE related functions, this cannot be called domestication, since KZFP genes are already from the host.

3) Page 5, lines 91-93: Here and throughout the authors use language such as "later" or "earlier" which is confusing - these should be replaced with "younger/more recent" and "older".

4) Page 6, lines 111-115: This section is highly speculative and should be moved to discussion.

5) Page 6 line 122: The authors do not define, here or in the methods, what constitutes a "variant" KRAB domain.

6) Page 7 lines 129-133: The authors only inferred their conclusion, yet they state that their result is consistent with a previous study. No real evidence is provided there.

7) Page 7 line 138-140: The authors say that the data suggests variant KRAB domains were formed gradually rather than in a burst, but their analysis is not sufficient to conclude this. Also, the only conclusion that can be drawn from Figure 2A is that the KZFPs that were clustered as "vKRAB" are on a separated branch in the tree on the left. This would mean that early in evolution some KZFP got a "vKRAB" and subsequently this gene underwent duplication and diversification, like all the other KZFP genes with "sKRAB" did.

8) Page 9 lines 189-193: Does the 90% cited here refer to 90% of the ~50% that are called as "tending to bind non-TE sequence" or 90% of all KZFPs? Regardless, this point is very misleading: the fact that less than 50% of the binding sites of a KZFP is not found to overlap TEs does not mean that the KZFP only binds to non-TEs. Some of this non-TE binding could also be an artifact of overexpression, which has not been considered but which has been well documented (for example ZFP809, Macfarlan Lab, and PRDM9 Simon Myers lab).

9) Lines 196-197, the authors state that they randomly selected 30 KZFPs. The authors should state in a supplementary figure which KZFPs were selected and, among them, what is the percentage of KZFPs that bind or not to TEs according to the analysis performed in the original paper (Imbault et al. 2017) and in this manuscript.

10) Page 11 line 230: Here and throughout the rest of the document the authors use the acronym "PCGs" without defining it (outside a figure legend).

11) Page 11 lines 234-237: Here the authors cite their use of pLI, RVIS, Shet, and dN/dS values as evidence of purifying selection. Of those, only dN/dS measures purifying selection, and the authors do not specify whether the dN/dS values they obtain are statistically significant evidence of purifying selection relative to a neutral model (likely the case when only considering chimp-human, as the authors do). Moreover, while the other measures do suggest some constraint, the differences between the KZFP-TE and KZFP-nonTE protein coding genes is very subtle. Also, they don't provide any explanation as to why, according to their claim, there should be less purifying selection for the KZFPs involved in mesoderm differentiation. Thus, the authors should temper their claims or else omit this data.

12) Page 11 lines 249-251: It is not clear how the author defined genes as transcription factors (they also do not define the acronym), or why they included them in the analysis. Additionally, the authors say that the divergence time of KZFPs is correlated with expression level but does not provide correlation values or the significance of these correlations.

13) Page 12 lines 266-268: This is not surprising, since TEs are generally silenced, while the rest of the genes can be either active or silent, so comparison of accessibility of cumulative TEs versus non-TEs will inevitably show open chromatin for non-TEs.

14) Page 13 lines 280-286: Here the authors try to draw conclusions from comparing chromatin accessibility of binding sites in ESCs and 293T cells and conclude that because they are more accessible in ESCs that suggests that KRAB-ZFPs activate in conditions. In reality, it is difficult to compare epigenetic states across cell lines, especially in undifferentiated vs differentiated, making it almost impossible without genetic manipulation to determine that KRAB-ZFPs are the cause of these differences.

15) How were the target genes selected for qPCR validation among the KZFP targets? In Fig.5 suppl. 3 the authors show that there is a fraction of genes that is only accessible in ESCs, but there is also a similar number of genes that is accessible both in ESCs and HEK293T cells, so the authors could have tried to validate some of those in both cell lines...Also, if the KZFPs are responsible for the target genes activation, why overexpression did not activate genes that are repressed in HEK293T cells? The ChIP-exo dataset used here (from Imbeault et al. 2017) was obtained from overexpression of the KZFPs in HEK293T cells, so obviously the proteins could bind to these genes in this cell line. This would rather suggest that if it's true that the tested KZFPs can promote transcriptional activation, this might be a secondary effect, since it might rely on something else making the genes already accessible and expressed in ESCs.

16) Page 16 lines 367-373: The conclusions that can be drawn from the ZNF611 reporter assay and associated evolutionary analysis are minimal. First, the authors cloned in a large chunk of DNA (1.2kb) rather than just the predicted binding site. This is mitigated somewhat by the deletion, but the deletion construct also deletes sequence upstream of the binding sites making the results hard to interpret. Additionally, the evolutionary analysis is very weak - traditional methods to generate phylogenetic trees do not work well for repetitive sequences, such as the ZnF arrays, and the bootstrap values on the tree are poor. There is almost no experimental methodology on how the tree was generated, how the authors overcame these issues, and how the authors identified the orthologous binding site in different species.

17) Page 18 lines 417-424: There is not enough detail about how the human KRAB-ZFPs were identified. Bare minimum, the authors need to report thresholds used to determine if a protein's domains scored high enough to be either a KRAB or C2H2 ZF domain.

18) Page 19: Given the highly repetitive nature of KRAB-ZFPs, it is not sufficient to use the homology estimations from Ensembl to identify orthologous proteins. Other methods, such as synteny, should be used to confirm orthologs. Additionally, the authors identify homologs between different KRAB domains based on %identity, but this will likely give spurious results, as functional domains do not evolve neutrally and often have high similarity across proteins due to functional constraint. Regarding the phylogenetic analysis, there is again not enough detail to explain how the authors overcome issues with alignments and low bootstrap values - additionally, they did not perform a model test prior to constructing the tree, which can impact the final results.

19) Page 22 lines 517-520: The authors do not elaborate why they chose FC > 1.1 or FC < 0.9 to call differentially expressed genes

20) Page 23 lines 529-532: How the authors performed the gene ontology enrichment/depletion analysis is not clear. For example, if the authors indeed prefiltered their list to remove genes that have no GO terms, that would bias the results.

21) Page 24 lines 552-554: For the non-targeting siRNA, it is unclear whether this is a scramble or targeting another gene (such as GFP)?

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Reply to the reviewers

We would like to thank the reviewers for their comments and suggestions. Our responses to them are listed below. We are hopeful that they will be satisfied with our responses and the changes we made in the revised version of the manuscript.

REVIEWER #1

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Reviewer #1 (Evidence, reproducibility and clarity (Required)): In this manuscript, Ameen and colleagues report the results of a multidimensional proteomic analysis which combined quantitative proteomics, phosphoproteomics and N-terminomics in an effort to identify neuronal proteins displaying altered abundance or modifications by proteolysis and/or phosphorylation following an excitotoxic insult. Excitotoxicity is known to initiate by over-activation of ionotropic glutamate receptors which allows an increase in intracellular Ca2+ , ultimately leading to activation of proteases. The analysis revealed that glutamate treatment for up to 240 min did not significantly affect the abundance of neuronal proteins but caused dramatic changes in the phosphorylation state of many neuronal proteins. Based upon the phosphopeptides and neo-N-peptides, which contain the neo-N-terminal amino acid residue generated through proteolytic cleavage of intact neuronal proteins during excitotoxicity, the authors identified the proteins that undergo phosphorylation, dephosphorylation and/or enhanced proteolytic processing in excitotoxic neurons. By combining different software packages, they found that these modified proteins form complex interactions that affect signaling pathways regulating survival, synaptogenesis, axonal guidance and mRNA processing. These data suggest that perturbations in the aforementioned pathways mediate excitotoxic neuronal death. Then, the authors showed by Western blot analysis that CRMP2, a crucial regulator of axonal guidance signaling, exhibited enhanced truncation and reduced phosphorylation at specific sites upon glutamate treatment. These events may contribute to injury to dendrites and synapses associated with excitotoxic neuronal death. Furthermore, the authors showed that calpains are responsible for the proteolytic processing and cathepsins for enhanced degradation of proteins during excitotoxicity. Blockage of calpain-mediated cleavage site of the tyrosine kinase Src during excitotoxicity confers neuroprotection in an in vivo model of neurotoxicity. In that regard, over twenty protein kinases are predicted to be activated in excitotoxic neurons. Collectively, this study contributes to the construction of an atlas of phosphorylation and proteolytic processing events that occur during excitotoxicity and as such they can be targeted for therapeutic purposes.

**Comments** Comment: The identification of potential calpain cleavage sites in neuronal proteins modified during excitotoxicity is an interesting finding of the study. However, the atlas presented appears to miss components such as Kinase D-interacting substrate of 220 kDa (Kidins220), also known as ankyrin repeat-rich membrane spanning (ARMS), a protein recently shown to be cleaved by calpain during excitotoxicity (López-Menéndez et al, 2019, Cell Death and Disease 10, 535).

Response: The calpain cleavage site of neuronal ARMS/KIDINS220 was mapped to the peptide bond between Asn-1669 and Arg-1670 (Gamir-Morralla, et al. (2015) Cell Death & Diseases 6, e1939). The cleavage is expected to generate two truncated fragments – one of ~185 kDa and another of ~10 kDa at the N-terminal and C-terminal sides, respectively of the cleavage site. Our TAILS analysis failed to detect the 10 kDa fragment which contains the neo-N-terminus generated by calpain cleavage. Here are the possible explanations:

The neo-N-terminus of the 10 kDa C-terminal fragment is unlikely to be observed in our experiment as the TAILS method relies on the production of peptides by trypsin. The 10 kDa fragment has Arginine as the first amino acid which means that the N-terminal peptide released and isolated by the TAILS method would be a single amino acid. In their publication, Gamir-Morralla, et al. showed that the total levels of both intact and degraded ARMS/Kidins220 decreased as a result of ischemic cerebral stroke, suggesting degradation rather than proteolytic processing to generate stable truncated fragments as the final outcome of calpain cleavage of ARMS/Kidins220 (Figure 2b of the publication by Gamir-Morralla, et al.). The TAILS method predominantly detects proteolytic processing whereas degradation can be more difficult to capture. Degradation often results in peptides containing less than 5-6 amino acids that are difficult to align with a single protein or result in transient peptide that may not be detectable in neurons at 240 min after glutamate treatment. **Overall, it is possible that Kidins220 is generated but was undetected by the TAILS approach.

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Comments: The CRMP2 antibody (Cell Signalling, 35672) used for western blots (figure 5D, also figure S11) and immunofluorescence (figure 5E) is problematic. Copied from https://www.cellsignal.com/products/primary-antibodies/crmp-2-d8l6v-rabbit-mab/35672: Monoclonal antibody is produced by immunizing animals with a synthetic peptide corresponding to residues surrounding lle546 of human CRMP-2 protein. The truncated CRMP2 (figure 5D) studied in the whole section (residues 1-516 or 1-517, ~57kDa) cannot be recognized by this monoclonal antibody. The detected band with the red letters in figure 5D might represent another cleavage product. In any case, asking Cell Signalling for more information about the exact immunogen might help, but since it's monoclonal and derived from residues surrounding lle546 it's very hard to include residues before aa516 and the unique epitope recognition upstream of aa516. The whole result section and discussion has to be reconsidered. Alternatively another antibody can be used to repeat those experiments in order to support the hypothesis. Time and resources are very familiar to authors since they have to repeat their previous work with a new antibody. Finally, there are no "western blot" and "immunofluorescence" methods for CRMP2.

Response: We would like to apologise for incorrectly listing the catalogue number of the anti-CRMP2 antibody purchased from Cell Signalling technology. Rather than the rabbit monoclonal anti-CRMP2 antibody (Cell Signalling, Cat#: 35672), we used the polyclonal anti-CRMP2 antibody (Cell Signalling, Cat#9393) to perform all the Western blot and immunofluorescence analysis in this paper. The e-mail confirming the purchase of this antibody is appended. According to the vendor, the antibody was raised by immunizing rabbits with a synthetic peptide derived from the human CRMP2 sequence. We decided to order this antibody because Zhang, et al. (Sci Rep. 2016; 6: 37050) reported that it could detect the truncated CRMP2 fragments generated by calpain cleavage in primary cortical neurons in vitro in response to axonal damage.

*The procedures of Western blot and immunofluorescence detailing the correct CRMP2 antibody descriptions are added in the revised version of the submitted manuscript.

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Comment: The truncated DCLK1 bands detected in figure S8B cannot be attributed to the proteolytic processing of DCLK1 at the sites described: T311↓S312, S312↓S313 and N315↓G316 (predicted M.W. of the (C-terminal) products: 48.7-49.1kDa (figure S8A) which is very close to be well-separated with conventional PAGE). The number and the separation of the bands suggest other cleavage sites. Response: We agree with the reviewer’s comment that conventional SDS-PAGE cannot differentiate the proteolytic products generated by cleavage at the three sites identified by TAILS. Furthermore, the TAILS methods could not detect all peptides generated by a protein during proteolysis. Therefore, validating our results with a Western blot experiment may reveal unidentified peptides in certain cases. We have now added the following statement in the revised manuscript to reflect the presence of other cleavage sites: “Besides detecting the 50-56 kDa truncated fragments, the antibody also cross-reacted with several truncated fragments of ~37-45 kDa. These findings suggest that DCLK1 underwent proteolytic processing at multiple other sites in addition to the three cleavage sites identified by our TAILS analysis.”

Comment: Could the striking observation that almost all proteolytic processing during excitotoxicity is catalyzed by calpains and/or cathepsins have derived (partially) from unspecific targets of calpeptin such as a subset of tyrosine phosphatases (Schoenwaelder and Burridge, 1999: approx. 1h treatment of fibroblasts with approx.. 10x less concentration) or other(s)? Response: Schoenwaelder and Burridge (1999, JBC 274:14359) reported that calpeptin exhibits both protease inhibitor as well as a protease inhibitor-independent activities in fibroblasts. Besides inhibiting calpains and cathepsins, they demonstrated that calpeptin could selectively inhibit a subset of membrane-bound tyrosine phosphatases. Since the TAILS method monitored the protease inhibitor activity of calpeptin, the proteolytically processing events mitigated by calpeptin in neurons during excitotoxicity are likely attributed to its protease inhibitor activity. Additionally, Schoenwaelder and Burridge reported this unconventional protease inhibitor-independent activity of calpeptin in fibroblasts. Since the protein tyrosine kinases expressed in neurons and fibroblasts are different, it is unclear if calpeptin can also exert such activity in neurons.

Comment: Describing the final part of figure 4C the authors suggest that "Liver kinase B1 homolog (LKB1), CaM kinase kinase β (CaMKKβ) and transforming growth factor‐β‐activating kinase 1 (TAK1) are the known upstream kinases directly phosphorylating T172 of AMPKα to activate AMPK (Herrero-Martin et al., 2009; Woods et al., 2005; Woods et al., 2003). Our findings therefore predict activation of these kinases during excitotoxicity (Figure 4C)." The first question arising here is whether these three kinases are the only ones know to phosphorylate AMPKα. Even if this is true, it is highly speculative to suggest that the findings of the present study predict the activation of these kinases during excitotoxicity, without providing the necessary experimental data, since the increased phosphorylation of AMPK may be an indirect effect of the reduced function of a phosphatase. Thus the proposed model does not hold. Response: Agree. We have therefore revised our interpretation of the results to reflect this possibility. The Revised sentence on page 13 reads “**Liver kinase B1 homolog (LKB1), CaM kinase kinase β (CaMKKβ) and transforming growth factor‐β‐activating kinase 1 (TAK1) are the known upstream kinases directly phosphorylating T172 of AMPKα to activate AMPK (Herrero-Martin et al., 2009; Woods et al., 2005; Woods et al., 2003), while a member of the metal-dependent protein phosphatase (PPM) family could dephosphorylate T172 of AMPK in cells (Garcia-Haro et al., 2010). Our findings therefore predict activation of these kinases and/or inactivation of the PPM family phosphatase in neurons during excitotoxicity (Figure 4C).”

Additionally, we also deleted the schematic diagram depicting the possibility of activation of LKB1, CaMKKβ and TAK1 in Figure 4 of the revised manuscript.

__**Minor points**

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Minor Comment: Highlights could present the key points of the study in a more straightforward manner. Response: Agree. We have edited the highlights in our revised manuscript to make them more straightforward.

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Minor comment: Figure 4A is too complicated. Proteins considered as hubs of signaling pathways in neurons should be somehow highlighted to distinguish them.

Response: Agree. We have now highlighted the signalling hubs by shading them in green in the revised figure. As we merged figures 2 and 4 of the original manuscript, these signalling hubs are presented in Figure 2B of the revised manuscript.

Minor Comment: The analysis of proteins with enhanced truncation and reduced phosphorylation such as CRMP2 and DCLK1 is fragmented. In addition, the authors should mention the criteria based on which these proteins were selected for further analysis.

Response: IPA analysis revealed synaptogenesis and axonal guidance as the top-ranked perturbed canonical signalling pathways governed by neuronal proteins undergoing significantly increased proteolytic processing and altered phosphorylation. As CRMP2 and DCLK1 are the key players in these pathways, they were chosen for further biochemical analysis to validate the TAILS results. To address this point, we added a few statements in the sections describing results of biochemical analysis of CRMP2 and DCLK1 in the revised manuscript. The additional sentences on page 13 now read “IPA analysis of the significantly modified neuronal proteins identified in our study predicted perturbation of signalling pathways governing axonal guidance and synaptogenesis in neurons during excitotoxicity (Figure S7). Since CRMP2 (also referred as DPYSL2) is a key player in neuronal axonal guidance and synaptogenesis (Evsyukova et al., 2013) and it underwent significant changes in phosphorylation state and proteolytic processing (Figures 5A and S7), it was chosen for validation of our proteomic results.” The additional sentences on page 15 read ”Similar to CRMP2, DCLK1 is also a key player in regulation of axonal guidance and synaptogenesis (Evsyukova et al., 2013). Since our TAILS results revealed significant proteolytic processing of DCLK1 (Figure S8A), it was chosen for validation of our proteomic results.”

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Minor comment: The potential therapeutic relevance of phosphorylation and proteolytic processing events that occur during excitotoxicity can be further explored. Response: Thanks for the suggestion. We have added a paragraph describing the additional evidence that protein kinase inhibitors and cell-permeable inhibitors blocking calpain cleavage of specific neuronal proteins as potential neuroprotectants to reduce brain damage induced by ischemic stroke. The additional sentences near the end of the Discussion section (page 25) now read “Since CRMP2 is key player in axonal guidance and synaptogenesis revealed by our proteomic analysis as the most perturbed cellular processes in excitotoxicity, blockade of its cleavage to form the truncated CRMP fragment is another potential neuroprotective strategy. Indeed, a cell-permeable Tat-CRMP2 peptide encompassing residues 491-508 close to the identified cleavage sites of CRMP2 could block calpain-mediated cleavage of neuronal CRMP2 and protect neurons against excitotoxic cell death (Yang et al., 2016)**.”

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The additional paragraph at the end of the Discussion section (page 25) now reads: “Besides the neuronal proteins undergoing enhanced proteolytic processing during excitotoxicity, protein kinases predicted by our phosphoproteomic results to be activated during excitotoxicity are also targets for the development of neuroprotective drugs. For example, our results demonstrated significant activation of neuronal AMPK during excitotoxicity, suggesting that aberrant activation of AMPK can contribute to neuronal death. Of relevance, small-molecule AMPK inhibitors could protect against neuronal death induced by ischemia in vitro, and brain damages induced by ischemic stroke in vivo. Likewise, inhibitors of Src and other Src-family kinases were known to protect against neuronal loss in vivo in a rat model of in traumatic brain injury (Liu et al., 2008a; Liu et al., 2017). Future investigation of the role of the excitotoxicity-activated protein kinases in excitotoxic neuronal death will reveal if small-molecule inhibitors of these kinases are potential neuroprotective drug candidates.”

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Minor comment: I am sorry but I could not find Figure 8, which is supposed to show the "In vivo model of NMDA neurotoxicity" (please, see page 30).

Response: Our apology for the mistake. This should be Figure 6 of the revised manuscript.

Minor comment: Introduction: O'Collins et al., 2006; Savitz and Fisher, 2007; both references are missing.

Response:* This was an oversight from our part and the references have been added to the revised manuscript.**

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Minor comment: Figure S1A-B: vehicle treatment time course is needed. Response: All neurons were cultured in neurobasal media for seven days. The control neurons were incubated in culture media while we started treating the other neurons with glutamate for MTT and LDH assay. The additional paragraph describing the design of the cell viability/death assays in page 32 reads “Primary cortical neurons were incubated for 480 min with and without the addition of 100 μM of glutamate. The control neurons were incubated for 480 min in culture medium. For neurons treated with glutamate for 30 min, 60 min, 120 min and 240 min, they were pre-incubated in culture medium for 450 min, 420 min, 360 min and 240 min, respectively prior to the addition of glutamate to induce excitotoxicity. For neurons treated with glutamate for 480 min, they were treated with glutamate just after seven days of culture in neurobasal media.”

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Minor comment: Figure 5E: Control close-up is missing. Response: A close-up view of the control neurons is now provided in Figure 4E of the revised manuscript.

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Minor comment: "Moreover, the number of CRMP2-containing dendritic blebs in neurons at 240 min of glutamate treatment was significantly higher than that in neurons at 30 min of treatment (inset of Figure 5E)." Such a statistic is not shown in the graph. Response: The statistical analysis results are now added to the revised manuscript in Figure 5E.

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Minor comment: "Consistent with this prediction, our bioinformatic analysis revealed that the identified cleavage sites in most of the significantly degraded neuronal proteins during excitotoxicity are mapped within functional domains with well-defined three-dimensional structures (Figures 6A)." Authors might mean figure S12A? Response: Correct. Our apology for the mislabelling. This has been corrected to “S12A”in the revised manuscript.

Minor comment: "Neuronal Src was identified by the three criteria of our bioinformatic analysis to be cleaved by calpains to form a stable truncated protein fragment during excitotoxicity (Figures 6A and Table S6)." Authors might mean figure 6D?

Response: Correct. Our apology for the mislabelling. Since we merged figures 2 and 4 of the original manuscript. This has been corrected to now read “(Figure 5D)” on page 18 of the revised manuscript.

Minor comment: Figure 2B: Clusters 1, 3, 4 and 6 do not follow treatment trends homogenously in all time points. For example in cluster 1 there is a phosphopeptide following the pattern 1, 0, -1 and another one following the pattern 0, 1, -1, which is actually a very different pattern even if the end value is stable (-1). The first example could belong to the cluster 6 as well, while the second example to cluster 5. Please elaborate on the rationale behind the categorization. Is there any other clustering method that can be used without making the categorization more complicated? Response: Since we merged Figures 2 and 4 of the original manuscript. This comment relates to the right panel of Figure 2A of the revised manuscript. The rationale behind the categorization of the phosphopeptides into six clusters was based upon the patterns of changes of their abundance (i.e. average of log-2 normalized z-score of phosphopeptide intensity) in three sample groups. **We calculated the number of permutations where the number of sample groups in set (n) = 3 (i.e. Control neurons, neurons of 30 min glutamate treatment and neurons of 240 min glutamate treatment) and number of sample groups in each permutation (r) = 3 (i.e. all three sample groups should be present in each permutation). Hence the number of permutations is 6. The six clusters refer to the six possible permutations of the patterns of abundance changes of the identified phosphopeptides rather than the end results.

Minor comment: A problem of the manuscript is its length and lack of coherence. Apart from presenting the data from the proteomics, phosphoproteomics and N-terminomics analyses, the authors focus on several different proteins to perform validation experiments and further characterize the biological significance of their modification. Because these proteins do not fall on the same pathway, the authors end up presenting several independent stories that complicate the reader. Response: We agree that proteins that do not operate in the same signalling pathway were chosen for further biochemical analysis. Their choice was justified because they are key players in the most perturbed canonical signalling pathways identified by bioinformatic analysis with the IPA software. We agree that this may complicate the reader. However, it also helps to illustrate that excitotoxic neuronal death is a complicated cell death process caused by dysregulation of multiple neuronal proteins which regulate different cellular processes.

Minor comment: Moreover, it is necessary for the authors to restructure their introduction, and avoid over-representing previous research on nerinetide, which is not used anywhere in the manuscript. Instead, the introduction must be more focused to better capture the necessity and essence of the present study. Response: We agree. Based on the reviewer’s comments, we decided to restructure the introduction by shortening the description of the results of Nerinetide research. Please refer to the track changes of the revised manuscript for the changes.

Minor comment: Taking into account figures 1 and S2 I understand that the authors combined samples of neuronal cell cultures (treated or not with Glu) with samples from mouse brains (that have undergone ischemic stroke/TBI or sham operation). If this is the case, why did the authors do that? How did they combine the different samples? And why this is not mentioned anywhere is the main text? Response: For a data-independent acquisition (DIA) based mass spectrometry experiment, it is essential we generate a library of identifiable peptides first using a standard data-dependent acquisition (DDA) approach. For the DIA type experiment to work, the identified peptides have to be in that library first. Excitotoxicity is a major mechanism of neuronal loss caused by ischemic stroke and traumatic brain injury. We therefore included the brains of sham-operated mice, brains of mice suffering ischemic stroke and traumatic brain injury to construct the spectral libraries and that is why the library contains pooled samples from the representative samples. Pre-fractionation of the pooled peptides was also performed to increase the number of identifiable peptides and generate a deeper library.

• Once we generated that library, all samples are analysed individually as a separate DIA experiment. The DIA approach then makes use of the generated library for identification and quantitation. This methodology allows for deeper identification and lower number of missing values. These statements were added in the method section of the revised manuscript (page 33)*

Minor comment: Regarding figure 5D, the authors write in the main text "Consistent with our phosphoproteomic results, the truncated fragment CRMP2 fragments could not cross-react with the anti-pT509 CRMP2 antibody (Figure 5D)" In the upper blot the truncated CRMP2 fragment runs well below the 70 kDa marker. However, in the middle panel, where we see the blot with the phospho specific antibody, the respective area of the blot has been cropped, so we cannot see whether the truncated fragment cross-reacts with the phospho specific antibody. Response: The presentation of the western blots in Figure 5D in the revised manuscript are now less cropped and clearly demonstrate there is no cross reactivity of the phospho specific antibody with the truncated fragment. Please refer to the revised Figure 5 for the updated Western blot images.

Minor comment: It is strange that only 1 and 13 proteins showed significant changes in abundance at 30 and 240min respectively. Especially after 240min of glutamate treatment one could expect that many proteins should change in their levels, since the neurons are almost diminished by cell death at that point. How could the authors explain this phenomenon? Additionally, in their previous publication, they showed that much more proteins change significantly in abundance following glutamate treatment (at 30min and 240min).

Response: Even though our global spectral libraries contain over 49,000 identifiable peptides derived from 6524 proteins, only 1696 quantifiable proteins were identified in the DIA mass spectrometry analysis (Figure 1) because we used stringent criteria for their identification: (i) false discovery rate of We agree with the reviewer that many more proteins are expected to change their abundance at 240 min as significant cell death was detected. However, if we had used less stringent false discovery rates of their identification and quantification, included proteins with just one unique identified peptide and lowered the threshold of abundance fold changes, many more proteins with significantly changed abundance would be detected. But we preferred to use these stringent criteria to ensure a high confidence in our identification of neuronal proteins undergoing significant changes during excitotoxicity.*

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In agreement with the low number of neuronal proteins exhibiting significant changes in abundance reported in this manuscript, our previously published study (Hoque, et al. (2019) Cell Death & Diseases) detected only 26 neuronal proteins undergoing changes in abundance. Hence, we disagree with the reviewer that our previous publication reported much more proteins undergoing changes in abundance in excitotoxicity.

Reviewer #1 (Significance (Required)): Comment on significance: The manuscript delivers a large amount of data, regarding changes in the proteome, the activation of specific kinases, phosphatases, as well as the molecular pathways that are activated at distinct time points of excitotoxicity. This information could be used in future studies to validate and develop potential therapeutic strategies that could protect against neuronal loss in various neurological disorders. Response: We are excited that Reviewer #1 felt that this large amount of generated data will be useful for subsequent studies to validate and develop novel therapeutic strategies.

Comment on significance: The same group has very recently published a work very similar to the particular manuscript (Hoque et al. Cell Death and Disease, 2019). In their previous publication, the authors cover a large part of their current objectives. They performed again a proteomic and phosphoproteomic analysis of mouse primary cortical neurons treated with glutamate for distinct time points, in their aim to identify changes in expression and phosphorylation state of neuronal proteins upon excitotoxicity. Apart from the N-terminome, which they investigate in their current manuscript, the proteomic and phospho proteomic analysis are very similar. As such, and because of the fact that the current manuscript is very extensive, the authors should consider to minimize it, and include only their novel findings (changes in the N-terminome, the involvement of specific kinases that contribute to excitotoxic neuronal death, the regulatory mechanism of CRMP2, etc).

Response: Since the coverage of phosphoproteins undergoing changes in neurons during excitotoxicity identified in the current study is much higher than that of phosphoproteins identified in our previously published study, we prefer to retain the description of the phosphoproteomic findings in this manuscript. Nonetheless, we agree that the manuscript needs to be shortened. Our suggestions to shorten the manuscript are listed below:

1. Move the description and results of global proteomic analysis to supplementary information. Since we made the same observation that only a small number of neuronal proteins undergo significant changes in abundance during excitotoxicity in our previously published study, moving the global proteomic analysis results away from the main text will not adversely impact the quality of the presentation.
2. For the description of how we classified the identified N-terminal peptides as those derived from degradation and those derived from proteolytic processing, we would like to move it to the supplementary information. Comment on significance: The authors should describe in a simpler way the proteomic and bioinformatics analyses they are using in the manuscript. It is difficult to understand the methodology used if you are not an expert in proteomics and bioinformatics. My suggestion is to revise their text and make it simpler and more concise. Response: We agree with this criticism. As we are not allowed to make a major revision of the manuscript at this stage, the revised manuscript contains only minor revisions that addresses all of the comments and suggestions provided by the two reviewers. Further changes will be added in the next revised version. Our suggestions to further restructure the manuscript are listed below:

Figure S5 depicting the rationale for classification of N-terminal peptides as products of degradation and those of proteolytic processing will be moved to the main text. The description of the rationale in the main text will be revised to help readers who are not experts in proteomics to better understand the rationale. A diagram depicting the workflow of our TAILS method will be added as a supplementary figure. For bioinformatic analysis of the proteomic results, we will provide in the supplementary information the definition of the following terms relevant to Ingenuity Pathway Analysis and PhosphoPath analysis of the perturbed biological processes and signalling pathways: (a) Canonical Signalling Pathways, (b) Cellular Processes and (c) Interaction Networks. A short description of how their identification benefits the mapping of the neurotoxic signalling networks in neurons will be provided in the supplementary information.

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REVIEWER #2

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Reviewer #2 (Evidence, reproducibility and clarity (Required)): Comment: In this article, Ameen and collaborators identify the modified proteins during neuronal excitotoxicity by using an in vitro model in which mouse primary cortical neurons are treated 30 and 240 min with 100 µM Glutamate. They use different approaches: a quantitative label-free global and phospho-proteomic methods and a quantitative N-terminomic procedure called Terminal Amine Isotopic Labelleling of Subtrates (TAILS). Results show that 240 min glutamate has minimal impact on protein abundance (13 neuronal proteins show significant changes) but enhance a modification of phosphorylation state and proteolysis of nearly 900 proteins. A significant part of these proteins are involved signalling pathway involved in cell survival, synaptogenesis and axonal guidance.

The paper is globally well written and experiments are convincing. The methodology and the analysis are well described and well explain. The text and each figure are clear and accurate. However, I have just one comment that needs answers and/or clarifications. Thanks for your work. Response: We appreciate the compliment provided by this reviewer on our submitted manuscript.

**Minor comment:**

Minor comment: Primary neurons are used at DIV7 and it has been shown that at DIV7 the percentage of astrocytes is relatively low, however astrocytes plays a key role in glutamate recapture and release. It will be relevant to know the percentage of glial cell in the culture model of the authors and how astrocytes are involved in glutamate recapture and also in excitotoxicity.

Response: The compositions of the DIV7 cultures are: 94.1+/- 1.1 % neurons, 4.9%+/-1.1% astrocytes, and *

Reviewer #2 (Significance (Required)):

Comment on significance: Excitotoxicity is a cell death process involved in many neurological disorders. However, nowadays, there are no existent FDA-approved pharmacological agents targeted to protect against excitotoxicity leading to neuronal death. A better comprehension of excitotoxicity is required to improve prevention, therapy and reparation following the disease.

With this work, the authors highlighted modified proteins in excitotoxic neurons. Interestingly, few of these proteins are involved in cell survival, mRNA processing or axonal guidance. This atlas of phosphorylation and proteolytic processing events during excitotoxicity permit the identification of new therapeutic targets such as calpain-mediated cleavage of Src kinase. This atlas will interest a lot of team working on neurological disorders such as Alzheimer disease, Parkinson disease or stroke. It will permit to better characterize cellular/molecular events involved in neuronal loss and will permit to find new therapeutic targets. Response: In response to this comment and a similar comment by Reviewer 1, we expanded the discussion to include the potential therapeutic values of our findings.

Comment on significance: My field of expertise: Stroke, cell death, excitotoxicity, signalling pathways and molecular targets, autophagy. I don't have sufficient expertise to evaluate proteomic analysis.

Response: No response is needed.

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

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Referee #2

Evidence, reproducibility and clarity

In this article, Ameen and collaborators identify the modified proteins during neuronal excitotoxicity by using an in vitro model in which mouse primary cortical neurons are treated 30 and 240 min with 100 µM Glutamate. They use different approaches: a quantitative label-free global and phospho-proteomic methods and a quantitative N-terminomic procedure called Terminal Amine Isotopic Labelleling of Subrates (TAILS). Results show that 240 min glutamate has minimal impact on protein abundance (13 neuronal proteins show significant changes) but enhance a modification of phosphorylation state and proteolysis of nearly 900 proteins. A significant part of these proteins are involved signalling pathway involved in cell survival, synaptogenesis and axonal guidance.

The paper is globally well written and experiments are convincing. The methodology and the analysis are well described and well explain. The text and each figure are clear and accurate. However, I have just one comment that needs answers and/or clarifications. Thanks for your work.

Minor comment:

Primary neurons are used at DIV7 and it has been shown that at DIV7 the percentage of astrocytes is relatively low, however astrocytes plays a key role in glutamate recapture and release. It will be relevant to know the percentage of glial cell in the culture model of the authors and how astrocytes are involved in glutamate recapture and also in excitotoxicity.

Significance

Excitotoxicity is a cell death process involved in many neurological disorders. However, nowadays, there are no existent FDA-approved pharmacological agents targeted to protect against excitotoxicity leading to neuronal death. A better comprehension of excitotoxicity is required to improve prevention, therapy and reparation following the disease.

With this work, the authors highlighted modified proteins in excitotoxic neurons. Interestingly, few of these proteins are involved in cell survival, mRNA processing or axonal guidance. This atlas of phosphorylation and proteolytic processing events during excitotoxicity permit the identification of new therapeutic targets such as calpain-mediated cleavage of Src kinase. This atlas will interest a lot of team working on neurological disorders such as Alzheimer disease, Parkinson disease or stroke. It will permit to better characterize cellular/molecular events involved in neuronal loss and will permit to find new therapeutic targets.

My field of expertise: Stroke, cell death, excitotoxicity, signalling pathways and molecular targets, autophagy. I don't have sufficient expertise to evaluate proteomic analysis.

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

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Referee #1

Evidence, reproducibility and clarity

In this manuscript, Ameen and colleagues report the results of a multidimensional proteomic analysis which combined quantitative proteomics, phosphoproteomics and N-terminomics in an effort to identify neuronal proteins displaying altered abundance or modifications by proteolysis and/or phosphorylation following an excitotoxic insult. Excitotoxicity is known to initiate by over-activation of ionotropic glutamate receptors which allows an increase in intracellular Ca2+ , ultimately leading to activation of proteases. The analysis revealed that glutamate treatment for up to 240 min did not significantly affect the abundance of neuronal proteins but caused dramatic changes in the phosphorylation state of many neuronal proteins. Based upon the phosphopeptides and neo-N-peptides, which contain the neo-N-terminal amino acid residue generated through proteolytic cleavage of intact neuronal proteins during excitotoxicity, the authors identified the proteins that undergo phosphorylation, dephosphorylation and/or enhanced proteolytic processing in excitotoxic neurons. By combining different software packages, they found that these modified proteins form complex interactions that affect signaling pathways regulating survival, synaptogenesis, axonal guidance and mRNA processing. These data suggest that perturbations in the aforementioned pathways mediate excitotoxic neuronal death. Then, the authors showed by Western blot analysis that CRMP2, a crucial regulator of axonal guidance signaling, exhibited enhanced truncation and reduced phosphorylation at specific sites upon glutamate treatment. These events may contribute to injury to dendrites and synapses associated with excitotoxic neuronal death. Furthermore, the authors showed that calpains are responsible for the proteolytic processing and cathepsins for enhanced degradation of proteins during excitotoxicity. Blockage of calpain-mediated cleavage site of the tyrosine kinase Src during excitotoxicity confers neuroprotection in an in vivo model of neurotoxicity. In that regard, over twenty protein kinases are predicted to be activated in excitotoxic neurons. Collectively, this study contributes to the construction of an atlas of phosphorylation and proteolytic processing events that occur during excitotoxicity and as such they can be targeted for therapeutic purposes.

Comments

The identification of potential calpain cleavage sites in neuronal proteins modified during excitotoxicity is an interesting finding of the study. However, the atlas presented appears to miss components such as Kinase D-interacting substrate of 220 kDa (Kidins220), also known as ankyrin repeat-rich membrane spanning (ARMS), a protein recently shown to be cleaved by calpain during excitotoxicity (López-Menéndez et al, 2019, Cell Death and Disease 10, 535).

The CRMP2 antibody (Cell Signalling, 35672) used for western blots (figure 5D, also figure S11) and immunofluorescence (figure 5E) is problematic. Copied from https://www.cellsignal.com/products/primary-antibodies/crmp-2-d8l6v-rabbit-mab/35672: Monoclonal antibody is produced by immunizing animals with a synthetic peptide corresponding to residues surrounding lle546 of human CRMP-2 protein. The truncated CRMP2 (figure 5D) studied in the whole section (residues 1-516 or 1-517, ~57kDa) cannot be recognized by this monoclonal antibody. The detected band with the red letters in figure 5D might represent another cleavage product. In any case, asking Cell Signalling for more information about the exact immunogen might help, but since it's monoclonal and derived from residues surrounding lle546 it's very hard to include residues before aa516 and the unique epitope recognition upstream of aa516. The whole result section and discussion has to be reconsidered. Alternatively another antibody can be used to repeat those experiments in order to support the hypothesis. Time and resources are very familiar to authors since they have to repeat their previous work with a new antibody. Finally, there are no "western blot" and "immunofluorescence" methods for CRMP2.

The truncated DCLK1 bands detected in figure S8B cannot be attributed to the proteolytic processing of DCLK1 at the sites described: T311↓S312, S312↓S313 and N315↓G316 (predicted M.W. of the (C-terminal) products: 48.7-49.1kDa (figure S8A) which is very close to be well-separated with conventional PAGE). The number and the separation of the bands suggest other cleavage sites.

Could the striking observation that almost all proteolytic processing during excitotoxicity is catalyzed by calpains and/or cathepsins have derived (partially) from unspecific targets of calpeptin such as a subset of tyrosine phosphatases (Schoenwaelder and Burridge, 1999: approx. 1h treatment of fibroblasts with approx.. 10x less concentration) or other(s)?

Describing the final part of figure 4C the authors suggest that "Liver kinase B1 homolog (LKB1), CaM kinase kinase β (CaMKKβ) and transforming growth factor‐β‐activating kinase 1 (TAK1) are the known upstream kinases directly phosphorylating T172 of AMPKα to activate AMPK (Herrero-Martin et al., 2009; Woods et al., 2005; Woods et al., 2003). Our findings therefore predict activation of these kinases during excitotoxicity (Figure 4C)." The first question arising here is whether these three kinases are the only ones know to phosphorylate AMPKα. Even if this is true, it is highly speculative to suggest that the findings of the present study predict the activation of these kinases during excitotoxicity, without providing the necessary experimental data, since the increased phosphorylation of AMPK may be an indirect effect of the reduced function of a phosphatase. Thus the proposed model does not hold.

Minor points

Highlights could present the key points of the study in a more straightforward manner.

Figure 4A is too complicated. Proteins considered as hubs of signaling pathways in neurons should be somehow highlighted to distinguish them.

The analysis of proteins with enhanced truncation and reduced phosphorylation such as CRMP2 and DCLK1 is fragmented. In addition, the authors should mention the criteria based on which these proteins were selected for further analysis.

The potential therapeutic relevance of phosphorylation and proteolytic processing events that occur during excitotoxicity can be further explored.

I am sorry but I could not find Figure 8, which is supposed to show the "In vivo model of NMDA neurotoxicity" (please, see page 30).

Introduction: O'Collins et al., 2006; Savitz and Fisher, 2007; both references are missing.

Figure S1A-B: vehicle treatment time course is needed.

Figure 5E: Control close-up is missing.

"Moreover, the number of CRMP2-containing dendritic blebs in neurons at 240 min of glutamate treatment was significantly higher than that in neurons at 30 min of treatment (inset of Figure 5E)." Such a statistic is not shown in the graph.

"Consistent with this prediction, our bioinformatic analysis revealed that the identified cleavage sites in most of the significantly degraded neuronal proteins during excitotoxicity are mapped within functional domains with well-defined three-dimensional structures (Figures 6A)." Authors might mean figure S12A?

"Neuronal Src was identified by the three criteria of our bioinformatic analysis to be cleaved by calpains to form a stable truncated protein fragment during excitotoxicity (Figures 6A and Table S6)." Authors might mean figure 6D?

Figure 2B: Clusters 1, 3, 4 and 6 do not follow treatment trends homogenously in all time points. For example in cluster 1 there is a phosphopeptide following the pattern 1, 0, -1 and another one following the pattern 0, 1, -1, which is actually a very different pattern even if the end value is stable (-1). The first example could belong to the cluster 6 as well, while the second example to cluster 5. Please elaborate on the rationale behind the categorization. Is there any other clustering method that can be used without making the categorization more complicated?

A problem of the manuscript is its length and lack of coherence. Apart from presenting the data from the proteomics, phosphoproteomics and N-terminomics analyses, the authors focus on several different proteins to perform validation experiments and further characterize the biological significance of their modification. Because these proteins do not fall on the same pathway, the authors end up presenting several independent stories that complicate the reader.

Moreover, it is necessary for the authors to restructure their introduction, and avoid over-representing previous research on nerinetide, which is not used anywhere in the manuscript. Instead, the introduction must be more focused to better capture the necessity and essence of the present study.

Taking into account figures 1 and S2 I understand that the authors combined samples of neuronal cell cultures (treated or not with Glu) with samples from mouse brains (that have undergone ischemic stroke/TBI or sham operation). If this is the case, why did the authors do that? How did they combine the different samples? And why this is not mentioned anywhere is the main text?

Regarding figure 5D , the authors write in the main text "Consistent with our phosphoproteomic results, the truncated fragment CRMP2 fragments could not cross-react with the anti-pT509 CRMP2 antibody (Figure 5D)" In the upper blot the truncated CRMP2 fragment runs well below the 70 kDa marker. However, in the middle panel, where we see the blot with the phospho specific antibody, the respective area of the blot has been cropped, so we cannot see whether the truncated fragment cross-reacts with the phospho specific antibody.

It is strange that only 1 and 13 proteins showed significant changes in abundance at 30 and 240min respectively. Especially after 240min of glutamate treatment one could expect that many proteins should change in their levels, since the neurons are almost diminished by cell death at that point. How could the authors explain this phenomenon? Additionally, in their previous publication, they showed that much more proteins change significantly in abundance following glutamate treatment (at 30min and 240min).

Significance

The manuscript delivers a large amount of data, regarding changes in the proteome, the activation of specific kinases, phosphatases, as well as the molecular pathways that are activated at distinct time points of excitotoxicity. This information could be used in future studies to validate and develop potential therapeutic strategies that could protect against neuronal loss in various neurological disorders.

The same group has very recently published a work very similar to the particular manuscript (Hoque et al. Cell Death and Disease, 2019). In their previous publication, the authors cover a large part of their current objectives. They performed again a proteomic and phosphoproteomic analysis of mouse primary cortical neurons treated with glutamate for distinct time points, in their aim to identify changes in expression and phosphorylation state of neuronal proteins upon excitotoxicity. Apart from the N-terminome, which they investigate in their current manuscript, the proteomic and phospho proteomic analysis are very similar. As such, and because of the fact that the current manuscript is very extensive, the authors should consider to minimize it, and include only their novel findings (changes in the N-terminome, the involvement of specific kinases that contribute to excitotoxic neuronal death, the regulatory mechanism of CRMP2, etc).

The authors should describe in a simpler way the proteomic and bioinformatics analyses they are using in the manuscript. It is difficult to understand the methodology used if you are not an expert in proteomics and bioinformatics. My suggestion is to revise their text and make it simpler and more concise.

Author Response

Reviewer #1

1) In many instances inappropriate controls were used. For instance, a straightforward experiment to corroborate the authors model would be to employ cells that exclusively express non-phosphorylatable eIF4E mutant (such as eIF4E KI MEFs described in Furic et al., 2010) and/or MNK KOs to establish the requirement of eIF4E phosphorylation and potential cross-talk with MNK dependent mechanisms, respectively. Although there were some attempts to do this (e.g. MNK1 KD, using pharmacological inhibitors that are by the way quite non-specific), the data are insufficient to support the authors' claims. Moreover, the interaction between eIF4E and eIF4G and potential changes in the eIF4F levels that are likely to confound authors' conclusions were not assessed.

2) Several mechanisms involving indirect effects of mTOR on eIF4E phosphorylation that have been reported in the literature were not considered. For instance, it is plausible that mTOR affects eIF4E phosphorylation by bolstering eIF4E:eIF4G association and recruitment of MNKs.

Appropriateness of the controls to be employed is imperative. We would appreciate if controls that appear inappropriate were identified for us to improve upon. We also endorse that pharmacological inhibitors like MNK inhibitor tend to be promiscuous. However, their use in combination with knockdown experiments offers a reasonable choice for strengthening a data point. We are surprised at the insistence of the reviewer for his emphasis on indirect regulation of eIF4E phosphorylation via eIF4G and eIF4F to proximate mTORC1 and MNK response, despite the evidence herein that identifies direct regulation of this phosphorylation by mTORC1 coupled with rapamycin induced feed back response by MNK. Data generated by us so over the years including some interesting unpublished observations (Majeed R and Andrabi KI) have strengthened our contention that eIF4E phosphorylation is regulated by mTORC1 directly with eIF4E: eIF4G regulation as a back up.

3) The evidence for direct phosphorylation of eIF4E by mTOR was based on non-optimally designed experiments. The description of methodology for the in vitro kinase assays was inadequate, and the experiment was carried out solely using GST-WTeIF4E as a substrate without appropriate controls. There also appears to be rapamycin dependent eIF4E phosphorylation in KD mTOR lanes.

The in vitro kinase assay for eIF4E as a mTORC1 substrate has been described in detail by us previously (Batool et-al 2020). The experiment referred to, by the reviewer has been included as part of supplementary data only to serve as a ready reference.

4) The authors use non-transformed cells as a control for eIF4E overexpression, whereby eIF4E overexpression is well-established to transform immortalized cells (Work from Sonenberg's, Bitterman's etc. labs).

The primary data to appreciate the dynamics of eIF4E expression is represented by human tumour samples (Fig 1A-D), that clearly indicated tumour specific over-expression and eIF4E hyper-phosphorylation. In an attempt to substantiate the universality of this observation, we examined its expression across several cell lines including the ones that are not transformed. In addition, non-transformed cells were used to assess whether phosphorylation of eIF4E was a function of its over-expression which otherwise not be possible to appreciate in a tumour cell scenario.

5) Functional assays are warranted to establish the effects of proposed mechanism on cell functions/fate.

We appreciate the significance of functional assays and intend to include them wherever necessary.

6) Many blots throughout the paper were of insufficient quality to be clearly interpreted.

We would like to know which blots the reviewer is referring to.

7) Many interpretations of the results were not justified by the data (e.g. in Figure 1C it is claimed that phosphorylation of eIF4E is increased in overexpressors, but this could be simply due to the increase in total protein levels).

We do not believe that the enhanced phosphorylation of eIF4E is due to the increase in the total protein. As seen in Fig.1C the levels of the protein are the same throughout.

8) Most of the work relies on transient (except for FLAG-S6K1) overexpression strategies which are prone to artifacts and not likely to represent physiological stoichiometry of investigated proteins.

We have already used five stable cell lines. It is not possible to generate stable cells for every protein as we are studying signalling cross-talks. We believe that we have used enough positive and negative controls to rule out the possibility of artefacts.

9) It has been previously shown (e.g. Lowe & Pelletier's labs) that eIF4E confers resistance to rapamycin by mechanisms that were clearly distinct and at least in my opinion far better substantiated than those published previously by the authors and proposed here. Indeed, eIF4E overexpression results in increased eIF4F levels, which has been shown to attenuate efficacy of not just rapamycin, but also active mTOR inhibitors, and many other oncogenic-kinase inhibitors.

Our study although being in concert with other evidences suggesting the feedback activation of Mnk/4E pathway upon mTORC1 inhibition differs from some of the studies as quoted by the reviewer. The basic difference for this anomaly lies in the difference of the experimental conditions that we use to monitor the phosphorylation status of eIF4E, that lies from a range of 20 min to 48 hrs at 50nM concentration of Rapamycin. Studies carried out elsewhere use either 250nM conc. of rapamycin for 2hrs (Michael C. Brown-2017), 100nM for 2 hrs (Rebecca L Stead-2013) or use of rapalogs for 12 hrs (Pierre E Joubert-2015). Although, these and many other studies have implicated crosstalk to explain increase in 4E phosphorylation upon mTOR inhibition, yet they grossly fall short of comprehensively monitoring the status of 4E phosphorylation from 20 min to 2 hrs at lower conc. of rapamycin. We believe that use of higher concentration of Rapamycin allows the Mnk1 induced phosphorylation to resurface early (>3 hrs) to reconcile with the literature about the rapamycin dependent upsurge in 4E phosphorylation.

10) Many published articles are misinterpreted as supporting the authors' claims. For instance, the authors write that "the inconsistent stature of mTORC1 as a 4EBP1 kinase in vivo" and the reference provided suggests that GSK3beta may phosphorylate 4E-BP1 in addition to mTOR which in certain contexts may lead to rapamycin resistance. As far as I understand, this, and other similar studies, do not challenge the status of mTORC1 as a 4E-BP1 kinase in vivo, but that GSK3beta (and other kinases such as Pim kinases, CDK1) may also phosphorylate 4E-BPs in certain contexts. Moreover, as initial studies on active-site mTOR inhibitors by Thoreen et al., and Feldman et al., as well as studies from Blenis' and Sonenberg's groups indicated, rapamycin does not efficiently inhibit 4E-BPs n the vast majority of contexts, which suggest that GSK3beta-dependent resistance to rapamycin may result from mTOR effectors other than 4E-BPs

We have previously summarized the studies that question the stature of 4E-BP1 as an mTOR substrate. We would like the reviewer to go through that manuscript (Batool et al, EJCB, 2017). We have missed to cite that paper in this manuscript.

Reviewer #2

1) A large portion of Figures 1-3 is a reproduction of data from the authors' 2020 paper (Batool et al., 2020) which showed that elF4E is phosphorylated by MNK1, and that MNK1 is repressed by activation of mTORC1 signaling. While some new experiments have been added (e.g. the analysis showing increased expression of S6k1 in cancer cell lines/tissue and the in silico peptide docking analysis), these are minimal additions to the recently published work from this group.

This study was built on our previous publication that suggest eIF4E as an important effector of mTORC1. This study however, focusses on the regulation of S6K1 and following are the additions in the paper:

• Overexpression of eIF4E WT and S209E correlates with S6K1 phosphorylation and activity and is rapamycin-insensitive (Figure 1E, F and Supplementary Figure S1).

• S6K1 TOS, but not HM phosphorylation is required for its interaction with eIF4E (Figure 4A, D).

• mTORC1 is required for priming S6K1 for activation while as mTORC2 activity is responsible for phosphorylation of TOS- and CT-deficient S6K1 (Figure 5D, F).

• Identification of a region in S6K1 that mediates mTORC2 response (Fig 6).

• Identification of a short peptide in S6K1, which appears to interact with PHLPP1 (Fig 7).

2) One new finding in this paper is that elF4E binds the TOS motif on S6K1 and this binding promotes the hydrophobic motif phosphorylation of S6K1. The authors interpret their data to mean that binding of elF4E induces a conformational change to relieve autoinhibition. Is there any structural information to support this conformational change? What if the binding of elF4E recruits the hydrophobic motif kinase (mTORC2 proposed) in the absence of a conformational change? There are multiple other explanations that need to be considered and addressed.

TOS deletion/ mutation renders S6K1, inactive due to:

The failure of hydrophobic motif (HM) to get phosphorylated implying that TOS may recruit a kinase to phosphorylate HM and activate the enzyme (prevailing model). If this were true, then phospho-mimicking HM should rescue the loss of enzyme activity due to TOS- mutation, which however is not the case.

Or

The failure of carboxy terminal domain (CTD) to disinhibit, implying that TOS-engagement must somehow orchestrate CTD disinhibition (conformational change) to allow HM phosphorylation as a consequence. Since loss of function due to TOS-mutation/deletion can be rescued only by CTD truncation, it is reasonable to infer that TOS engagement with 4E must serve to remove inhibition due to CTD by a change in conformation to facilitate HM phosphorylation to occur in TOS independent manner.

Although there is no structural data, the inferences are compelling to propose the conformational change at the behest of eIF4E interaction with S6K1.

The possibility of mTORC2 recruitment by eIF4E is not supported by any data. This is because TOS &CTD deleted variant of S6K1 continues to be phosphorylated in a torin sensitive manner (Fig 5D).

Other consideration have also been discussed to the best of our ability.

3) The authors propose that PHLPP1 is constitutively bound to S6K1 to suppress hydrophobic motif phosphorylation, and serum stimulation causes the release of PHLPP1 to fully activate S6K1. Unfortunately, this potentially important mechanism is experimentally addressed by only 3 co-IPs in Figure 7: overexpressed PHLPP1 co-IPs with a GST fusion with residues 78-85 of S6K1, PHLPP1 co-IPs with S6K1 (and less efficiently in the presence of serum), the PHLPP1 regulation of S6K1 is abolished in a construct in which residues 78-95 are deleted. The identification of a PHLPP1-binding determinant on S6K1 is significant but the current data just scratch the surface. What are the residues? Are they evolutionarily conserved? Are they conserved in other PHLPP1 substrates? Does the GST fusion with these 8 amino acids result in the activation of S6K1 by sequestering PHLPP1? A compelling mechanistic analysis is missing and should be provided especially since PHLPP1 is in the title of the paper.

While deletion of sequence between 78-85 renders S6K1 non-responsive to serum stimulation, it does not affect its sensitivity towards rapamycin. Also, GST fusion of these 8 amino acids resulted in the activation of S6K1 as it sequestered PHLPP1. Some more experiments can be added to further support the contention. Three out of eight amino acids appear to be evolutionary conserved. We have performed a detailed mutagenesis of the region and the data is part of a manuscript in preparation.

4) Deletion of residues 91- 109 inactivates S6K1, which the authors interpret as meaning the regions is critical for mTORC2 binding and HM phosphorylation. But this encompasses the Gly-rich loop and its deletion will inactivate any kinase.

The deletion, 91-109, referred to by the reviewer, was introduced to evaluate the ability of this S6K1 variant to act as a substrate for mTORC2 mediated HM phosphorylation rather than to determine the state of S6K1 enzyme activity as perceived by the reviewer. Regardless of the influence this deletion may have in the activity state of S6K1, it should have no bearing on the ability of mTORC2 to phosphorylate S6K1at its HM situated 300 amino acids carboxy terminus to the deletion. Since this deletion results in the failure of mTORC2 to phosphorylate S6K1 at Hm, we drew following conclusion.

• This region appeared sufficient to mediate HM phosphorylation irrespective of the presence of TOS motif.

• That this region may support mTORC2 docking.

• That mTORC2 mediated S6K1 phosphorylation is specific and not a random event (Refer to discussion).

Reviewer #3

1) While the authors claim that MNK1 is not the "primary" kinase phosphorylating eIF4E, they fail to show the lack of CGP57380 effect on p-eIF4E(S209) and pS6K1(T412) phosphorylation in HEK293 cells they preferentially use for their experiments.

As suggested by the reviewer, the blots can easily be probed for p-eIF4E (S209) and pS6K1(T412) to check the effect of CGP57380 in HEK293 cells, though this has already been done in our previous manuscript (Batool et al, Molecular and Cellular Biochemistry, 2019).

2) The quality of pS6K1(T412) blots is questionable: while on Figure 1DEF, Figure 2A, Figure 5C and Figure 7B there is a clear single band, on Figure 1G, Supplementary figure S1, Figure 5ABDEF, Figure 6CDE and Figure 7ADE the authors ignore the strong band and appear to focus on the weak one.

The reviewer has rightly noticed the presence of one sharp band in some blots probed with Thr412 and two bands in few. The difference lies in the use of two different antibodies (Cell Signaling Technology Cat no. 9205 and 9234). One among them detects only one band while other detects two bands may be because of the potency of the antibody towards a particular species.

3) The authors do not comment on the reproducibility nor present quantitation of the essential experiments (Figure 1EFG, Figure 3D, Supplementary figure S1, etc). Quantitation should at least include essential WBs (pS6K1(T412) and p-eIF4E(S209)) and S6K1 activity towards S6 and must explicitly state the number of independent experiments and the reported statistic.

The quantitation for these figures can be added as suggested by the reviewer.

4) The authors should comment on the puzzling result in Figure 1F where control shRNA significantly decreases S6K1 activity towards S6.

We acknowledge that this is an anomaly and can be corrected.

5) The authors should consider alternative models. Thus, for instance, Blenis lab has previously shown that S6K1 and mTORC1 cooperate in the context of eIF3 complex. Could this mechanism contribute to the increased S6K1 activity upon eIF4E overexpression?

This possibility was over ruled as we observed a direct binding of eIF4E and S6K1.

Furthermore, I would strongly recommend extensive editing to improve the structure and style of the manuscript.

We agree to re-structure and re-style the manuscript as and when required.

Reviewer #3

High eIF4E/4EBP1 ratio is known to predict low cell sensitivity to mTOR inhibitors, suggesting that high eIF4E could help bypass mTOR requirement for cell growth and cap-dependent mRNA translation. The manuscript by Majeed et al examines how eIF4E affects S6K1 HM phosphorylation and activity. The authors claim that phosphorylated eIF4E (and not mRaptor) is the factor required "to overcome mTORC1 dependence of S6K1" activation and suggest mTORC2 (rather than mTORC1) as a kinase phosphorylating S6K1 HM.

To support this conclusion, the authors argue that:

• overexpression of eIF4E WT and S209E correlates with S6K1 phosphorylation and activity and is rapamycin-insensitive (Figure 1EF, Supplementary Figure S1)

• mTORC1 activity is required for S6K1 and eIF4E phosphorylation (Figure 2AB, Figure 3BCE)

• S6K1 TOS, but not HM phosphorylation is required for its interaction with eIF4E (Figure 4AD)

• MNK1 activity is not required for eIF4E phosphorylation (Figure 3CD)

• mRaptor is not required for S6K1 binding to eIF4E (Figure 4DE)

• mTOR is required for S6K1 activity and mTORC2 activity is responsible for phosphorylation of TOS- and CT-deficient S6K1 (Figure 5DF)

Further, the authors identify a short peptide in S6K1, which appears to interact with PHLPP1.

While some of the results are indeed interesting, the presented data are not sufficient to support the authors' central claim (that eIF4E and not mRaptor/mTORC1 is required for mTORC1-independent S6K1 phosphorylation and activity). Thus, the key experiment to demonstrate that (phosphorylated) eIF4E is necessary and sufficient for S6K1 phosphorylation and activity in the presence of rapamycin is missing. Figure 1F and Figure 1G come closest to that, but still fall short of convincingly supporting the central claim. Further, the fact that mTORC2 could phosphorylate the HM in TOS- and CT-deficient S6K1 has already been elegantly and definitively shown by Ali & Sabatini in their 2005 JBC publication.

Besides the central deficiencies outlined above, the following major points should be addressed:

1) While the authors claim that MNK1 is not the "primary" kinase phosphorylating eIF4E, they fail to show the lack of CGP57380 effect on p-eIF4E(S209) and pS6K1(T412) phosphorylation in HEK293 cells they preferentially use for their experiments.

2) The quality of pS6K1(T412) blots is questionable: while on Figure 1DEF, Figure 2A, Figure 5C and Figure 7B there is a clear single band, on Figure 1G, Supplementary figure S1, Figure 5ABDEF, Figure 6CDE and Figure 7ADE the authors ignore the strong band and appear to focus on the weak one.

3) The authors do not comment on the reproducibility nor present quantitation of the essential experiments (Figure 1EFG, Figure 3D, Supplementary figure S1, etc). Quantitation should at least include essential WBs (pS6K1(T412) and p-eIF4E(S209)) and S6K1 activity towards S6 and must explicitly state the number of independent experiments and the reported statistic.

4) The authors should comment on the puzzling result in Figure 1F where control shRNA significantly decreases S6K1 activity towards S6.

5) The authors should consider alternative models. Thus, for instance, Blenis lab has previously shown that S6K1 and mTORC1 cooperate in the context of eIF3 complex. Could this mechanism contribute to the increased S6K1 activity upon eIF4E overexpression?

Furthermore, I would strongly recommend extensive editing to improve the structure and style of the manuscript.

Reviewer #2

This manuscript builds on a previous publication from the authors identifying an mTORC1-sensitive and MNK1-mediated phosphorylation of elF4E, which they now propose is involved in the mechanism of activation of S6 kinase1 (S6K1). Specifically, the authors propose that the binding of MNK-1-phosphorylated elF4E to the TOR Signaling motif (TOS) of S6K1 relieves autoinhibition of the kinase, in turn promoting the phosphorylation by mTORC2 of the regulatory hydrophobic motif phosphorylation site. Furthermore, they propose that this phosphorylation is kept in check by binding of the phosphatase PHLPP1 to an 8 amino acid segment on S6K1, and that serum stimulation results in the release of PHLPP1 to increase phosphorylation at the hydrophobic motif and allow full activation. This is a potentially very interesting finding but unfortunately the data are poorly presented, many experiments are superficial, and alternative explanations are not considered.

Major comments:

1) A large portion of Figures 1-3 is a reproduction of data from the authors' 2020 paper (Batool et al., 2020) which showed that elF4E is phosphorylated by MNK1, and that MNK1 is repressed by activation of mTORC1 signaling. While some new experiments have been added (e.g. the analysis showing increased expression of S6k1 in cancer cell lines/tissue and the in silico peptide docking analysis), these are minimal additions to the recently published work from this group.

2) One new finding in this paper is that elF4E binds the TOS motif on S6K1 and this binding promotes the hydrophobic motif phosphorylation of S6K1. The authors interpret their data to mean that binding of elF4E induces a conformational change to relieve autoinhibition. Is there any structural information to support this conformational change? What if the binding of elF4E recruits the hydrophobic motif kinase (mTORC2 proposed) in the absence of a conformational change? There are multiple other explanations that need to be considered and addressed.

3) The authors propose that PHLPP1 is constitutively bound to S6K1 to suppress hydrophobic motif phosphorylation, and serum stimulation causes the release of PHLPP1 to fully activate S6K1. Unfortunately, this potentially important mechanism is experimentally addressed by only 3 co-IPs in Figure 7: overexpressed PHLPP1 co-IPs with a GST fusion with residues 78-85 of S6K1, PHLPP1 co-IPs with S6K1 (and less efficiently in the presence of serum), the PHLPP1 regulation of S6K1 is abolished in a construct in which residues 78-95 are deleted. The identification of a PHLPP1-binding determinant on S6K1 is significant but the current data just scratch the surface. What are the residues? Are they evolutionarily conserved? Are they conserved in other PHLPP1 substrates? Does the GST fusion with these 8 amino acids result in the activation of S6K1 by sequestering PHLPP1? A compelling mechanistic analysis is missing and should be provided especially since PHLPP1 is in the title of the paper.

4) Deletion of residues 91- 109 inactivates S6K1, which the authors interpret as meaning the regions is critical for mTORC2 binding and HM phosphorylation. But this encompasses the Gly-rich loop and its deletion will inactivate any kinase.

Reviewer #1

In this article Majeed et al propose a previously unrecognized model of S6K1 activation whereby eIF4E interacts with the TOS motif of S6K1, which facilitates phosphorylation of its hydrophobic motif by mTORC2. The authors also propose that another motif in S6K1 is responsive for serum induced and PHLPP1-mediated activation of S6K1. Furthermore, the authors propose that eIF4E may be a direct downstream substrate of mTORC1, and that mTOR is a major kinase that phosphorylates eIF4E. Although of potential interest, the data are frequently overinterpreted, the experimental design is not optimal, previous literature was not adequately considered, and many of the authors' conclusions were open to alternative explanations. My specific comments are outlined below:

1) In many instances inappropriate controls were used. For instance, a straightforward experiment to corroborate the authors model would be to employ cells that exclusively express non-phosphorylatable eIF4E mutant (such as eIF4E KI MEFs described in Furic et al., 2010) and/or MNK KOs to establish the requirement of eIF4E phosphorylation and potential cross-talk with MNK dependent mechanisms, respectively. Although there were some attempts to do this (e.g. MNK1 KD, using pharmacological inhibitors that are by the way quite non-specific), the data are insufficient to support the authors' claims. Moreover, the interaction between eIF4E and eIF4G and potential changes in the eIF4F levels that are likely to confound authors' conclusions were not assessed.

2) Several mechanisms involving indirect effects of mTOR on eIF4E phosphorylation that have been reported in the literature were not considered. For instance, it is plausible that mTOR affects eIF4E phosphorylation by bolstering eIF4E:eIF4G association and recruitment of MNKs.

3) The evidence for direct phosphorylation of eIF4E by mTOR was based on non-optimally designed experiments. The description of methodology for the in vitro kinase assays was inadequate, and the experiment was carried out solely using GST-WTeIF4E as a substrate without appropriate controls. There also appears to be rapamycin dependent eIF4E phosphorylation in KD mTOR lanes.

4) The authors use non-transformed cells as a control for eIF4E overexpression, whereby eIF4E overexpression is well-established to transform immortalized cells (Work from Sonenberg's, Bitterman's etc. labs).

5) Functional assays are warranted to establish the effects of proposed mechanism on cell functions/fate.

6) Many blots throughout the paper were of insufficient quality to be clearly interpreted.

7) Many interpretations of the results were not justified by the data (e.g. in Figure 1C it is claimed that phosphorylation of eIF4E is increased in overexpressors, but this could be simply due to the increase in total protein levels).

8) Most of the work relies on transient (except for FLAG-S6K1) overexpression strategies which are prone to artifacts and not likely to represent physiological stoichiometry of investigated proteins.

9) It has been previously shown (e.g. Lowe & Pelletier's labs) that eIF4E confers resistance to rapamycin by mechanisms that were clearly distinct and at least in my opinion far better substantiated than those published previously by the authors and proposed here. Indeed, eIF4E overexpression results in increased eIF4F levels, which has been shown to attenuate efficacy of not just rapamycin, but also active mTOR inhibitors, and many other oncogenic-kinase inhibitors.

10) Many published articles are misinterpreted as supporting the authors' claims. For instance, the authors write that "the inconsistent stature of mTORC1 as a 4EBP1 kinase in vivo" and the reference provided suggests that GSK3beta may phosphorylate 4E-BP1 in addition to mTOR which in certain contexts may lead to rapamycin resistance. As far as I understand, this, and other similar studies, do not challenge the status of mTORC1 as a 4E-BP1 kinase in vivo, but that GSK3beta (and other kinases such as Pim kinases, CDK1) may also phosphorylate 4E-BPs in certain contexts. Moreover, as initial studies on active-site mTOR inhibitors by Thoreen et al., and Feldman et al., as well as studies from Blenis' and Sonenberg's groups indicated, rapamycin does not efficiently inhibit 4E-BPs n the vast majority of contexts, which suggest that GSK3beta-dependent resistance to rapamycin may result from mTOR effectors other than 4E-BPs

Reviewer #3

This manuscript describes a complete model of robust insect navigation. The originality of this remarkable work relies on a clear endeavour to describe the neural basis of each function involved in the homing behaviour of the ant. This paper focuses on the neural processing related to various theoretical hypotheses in terms of signal processing. Several previous studies replicated the route following behaviour but did not account for visual homing, i.e., the ability of the ant to return to familiar regions from novel locations. The proposed model extends the one proposed by Webb in 2019 to account for two very challenging points: the ability of the ants to home from new locations and the ability of the ant to switch between strategies according to the context.

Major points:

• I was very surprised by the slow velocity of the simulated ant (Vo = 1cm/s) compared to the real one (about 50cm/s). Why is the speed so slow? This point must be discussed. Is there any fundamental reason?
• Concerning the path integration strategy, the distance does not seem to be measured (odometer) or included in the model.
• What would happen to the simulated ant if an obstacle was placed on the familiar route? What is the robustness of the Zernike-based moment algorithm to the unpredicted presence of an obstacle that could appear during the homing? I suggest doing additional simulations in this sense that could show the robustness of the proposed navigation model. These new simulations could be in line with the well-known experiments proposed by Wehner and Wehner (Insect navigation: use of maps or ariadne's thread?).

Page 16, lines 417: would it be possible to plot Crf with respect to angular orientation of the simulated ant in various places (every 10° steps for example)?

Reviewer #2

The beautifully illustrated manuscript by Sun et al is a challenging but highly rewarding, interesting and intellectually stimulating modeling study that proposes a unified model of insect navigation, which, at least in large parts, is constrained by neuroanatomical and physiological data. It elegantly combines previous models of path integration of the central complex and visual learning in the mushroom body (underlying visual homing) and proposes a third model for habitual route following. In the end, all three models are integrated and mapped onto known neural structures of the insect brain, most notably the central complex and the mushroom body. The information extracted from the environment is decomposed using a novel method that separates rotationally invariant feature information from rotational variant directional information. While the first is used to carry out visual homing based on image familiarity, the second is used to follow habitual routes. The important novelty in the paper is that this new information processing strategy allows to integrate all mentioned navigational modules. Moreover, it does so using previous biologically constrained models and expands this basis towards a full system that can replicate numerous behavioral data from ants, including difficult experiments, in which ants have to trade off different strategies against each other. I highly welcome this paper as an important addition to both the literature on the insect central complex, as well as to more theoretical navigational work, in particular as many predictions can be made based on the presented models. Nevertheless I have several points that need to be addressed.

Major comments:

1) Accessibility to a broad readership. While the general text is written very well and the content is highly interesting for a life science (in particular insect neuroscience) audience, the methods section and some aspects of the reasoning behind the model are very technical. Being an insect neurobiologist myself, I struggle to follow large parts of the methods and had admittedly never heard of Zernike moments. Given that the mathematical model and the concepts of frequency analysis are the foundations of the paper, I suggest to add some more intuitive and broadly accessible language that would allow a biologist to grasp at least the key principles of what is done by those initial analyses of the visual information in the model (of course, the math is needed for a computational audience and essential for replication of the model, but a few additions might go a long way for biologists). A schematic illustration as to what Zernike moments are, maybe combined with some simple examples might help a lot. This is important as the paper is not only directed towards computational biologists, but is highly relevant also for physiologists, anatomists and behaviorists, most of whom (extrapolating from my own mathematical ignorance) probably fail to grasp the essence of the new principles presented.


2) Neuroanatomical correspondence of model details: The paper claims that the model is in most parts biologically constrained and that most elements can be mapped onto known neurons. Where this was not possible (route following) the authors speculated about the possible implementations. While on the levels of neuropil groups this is all quite true, the details, especially in the central complex, are less clear and many of the proposed circuits have no known counterpart in any insect brain to date. This is not saying that those parts of the model are not realistic or interesting, but that the claim that they correspond to existing neurons in the central complex, is slightly misleading. I will list a series of obvious mixups of cell types below, which need to be corrected (2.1), but additionally, it should be clearly stated where the model does not (yet) have a solid grounding in biology (see point 2.2). Finally, the speculative route following implementation seems at odds with neurophysiological data from various species and alternative pathways and implementations seem more likely (point 2.3).

2.1)

• Line 126: CPU3 neurons are supposed to be a mirrored TB1 ring attractor network? I'm not sure if this is what the authors want to say, as CPU3 neurons are known in locusts (Heinze and Homberg, 2008), but connect the PB with the FB as columnar cells. If the authors mean CPU4 cells, these neurons are also not forming a ring-network (even though they could receive shifted compass information from TB1 cells by some means). Most simply, would not a parallel set of TB1 cells be optimally suited for this task? There are four TB1 cells for each column in the PB, potentially enough for four parallel ring attractors. These cells are neurochemically distinct and could function independently (see Beetz et al, 2015).
• There is no known direct connection between the EB and the FB (proposed in figure 4)
• There is no direct connection from the OL to the CX (indicated in caption of figure 1 as underlying PI).
• line 348: CL2 neurons should be CL1 (CL2 correspond to fly P-EN neurons, not E-PG)
• In the PI section of the methods, sometimes TN cells are referred to as TN2 cells or just as TN cells. TN2 is one of two types of TN cells (tangential noduli neurons) and was the one primarily used for the standard model of Stone et al 2017. Please be consistent. Also, the tuning cells of the visual homing circuit are called TN cells. This is very confusing and should be changed.

2.2) There are no known ring attractors in the FB. The only ring attractor shown experimentally is the one in the EB/PB, which employs recurrent feedback loops with the PB (E-PG/P-EN/P-EG cells; equal to CL1a, CL2, and CL1b) and inhibitory neurons in the PB (TB1 or delta7 cells). While a similar recurrent connection pattern is thinkable in the FB as well, using unknown types of columnar cells, there is no experimental support for that. Pontine cells might also form local connections that could result in a RA, but that is even more speculative. Please clearly state that the numerous RAs required by the model are hypothetical and have not yet any biological correspondence in the form of identified cell types. Also, I suppose not all the neuron rings drawn in the figures are ring attractors. I suggest making that distinction clearer (the many abbreviations for the different neuron rings do not make this easier to follow either).

2.3) The authors assume a second compass system in the PB that is fed directly from the OL via the posterior optical tract. There is no evidence for this beyond a single cell type from locusts that connects the accessory medulla (circadian clock) to the POTU, which is also innervated by TB1 neurons. However, there is no connection to the visual part of the OL, and no physiological data exists on the AME->POTU connection. In contrast, the anterior optic tract via the AOTU has been shown in Drosophila to contain many neurons that respond to visual features and they converge on the head direction cells in the EB via a recently resolved mechanism. It seems odd to ignore this known compass pathway and propose another one for which no evidence exists. That said, the authors use the anterior pathway to construct a desired heading via an ANN residing in the AOTU/BU pathway, information that is then used to feed into an EB ring attractor that then connects to additional attractors in the FB. Whereas the EB attractor (in conjunction with the PB) exists, there is no evidence for FB based ring attractors and there is no known direct connection between the EB and the FB. While this all results in a really nice figure, it unfortunately is misleading and based on not enough evidence to show it so prominently (readers might easily take it for factual).

If I may, I would like to point out that there is an alternative solution for at least the compass problem: There are four individual CL1 cells in each column of the EB in locusts as well as in flies (EPG/PEG cells). While they are identical in their projection patterns, some connect the PB to the EB and others connect the EB to the PB, so that there are in theory enough cells to form two parallel recurrent loops (needed to maintain a head direction signal). One of them could be driven by landmarks, while the other could be driven by global compass cues. Whereas the current idea is that both inputs converge on a single head direction signal (celestial and local cue based), this might not be true, given that local cues have been tested in Drosophila and global cues in locusts and some other species. These neurons are neurochemically distinct and most likely play different functional roles.

Finally with respect to the desired heading, a short term plasticity based, associative mechanism linking the phase of the head direction signal and the local environment was recently demonstrated in Drosophila (Fisher at al. 2019 and Kim et al, 2019). The authors state that several of these phases can be stored and retrieved in each respective environment. To me this sounds very close to what the authors of the current study suggest for routes in ants. Please consider these points and revise the proposed circuit identity accordingly.

3) The overall layout of the model is not fully clear to me from the paper. The authors present many (nicely illustrated) parts of the model, but I fail to reconcile some of the partial models with one another and have no immediate way of seeing how many neurons there are overall, or what their complete connectivity patterns are. I assume this is all obvious from the code itself, but being a neuroanatomist and physiologist, I struggle to get an intuition for the circuits based on Python code. This hinders independent interpretation and finding alternative solutions for mapping the model onto anatomical neural circuits once newly discovered neurons become available in the future. I suggest including (at least in the supplements) a full graphical depiction of the model with all existing neurons and their connections. Maybe using a force directed graph diagram like used by the authors of Stone et al. 2017 for their path integration model results in a model illustration that is intuitively understandable for researchers who think more in terms of anatomy. But even if it turns out to be somewhat messy, it would still be helpful.

Reviewer #1

This is an interesting and timely study on a topic of considerable interest: computational strategies used by insects to perform their remarkable navigational feats. The authors identify shortcomings in existing models – specifically, that they do not account for the entire range of capabilities and the flexibility that the most accomplished of insect navigators display – and integrate and build upon prior models to successfully fill these gaps. The integrated model pins specific computational functions on specific anatomical structures, making it, in principle, testable in the near-medium term. The figures are well-made and the writing is compact but readable. Here are a few specific concerns:

1) It is entirely reasonable that the authors combine experimental and modeling work from a range of different insect species to build different pieces of their own model. By and large they are careful to state which is which. However, they could make it clearer which assumptions are based on experimental data and which are based on prior models (i.e., not actual data). As an example, although the mushroom body has been suggested by numerous modeling studies and conceptually driven reviews to be involved in visual navigation, the experimental evidence for this is lacking, and their precise role is far from well-established.

2) I commend the authors for integrating useful components from prior models to construct their integrated model, but, although the figures go some way towards clarifying how the different pieces might fit together, it would be useful to make even clearer what is entirely novel here and what is derived/integrated from previous work. In addition, although the authors make a testable case for the involvement of the fan-shaped body in a series of different navigational computations, controlled by the mushroom body, the figures are still somewhat complex and confusing. Please try and further clarify them.

3) The authors could derive more constraints from the fly physiology literature than they do. As examples, Fisher et al., Nature, 2019 and Kim et al., Nature, 2019 have relevant findings relating to plasticity in mapping visual stimuli onto a compass representation. Turner-Evans et al., eLife, 2017 has a data-driven ring attractor model that is relevant, and Turner-Evans, bioRxiv, 2019 features data demonstrating that the fly compass for current heading relies on visual input from the anterior optic tubercle, contrary to the authors' assumption deriving from an anatomical pathway from the posterior optic tubercle to the protocerebral bridge (175-176). On a somewhat related note, the fly heading system does not necessarily show 'bar following' in open loop (line 164): the experiments cited (Seelig & Jayaraman, 2015) were performed in closed loop, with the animal controlling bar position.

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 preprint: https://www.biorxiv.org/content/10.1101/856153v1

Summary

This is an original, focussed study that offers a new model to explain the neuronal “computation” that underlies insect navigation. The authors identify shortcomings in existing models – specifically, that they do not explain the entire range and flexibility of insect navigational capabilities – and integrate and build upon prior models to successfully fill these gaps. The integrated model is particularly valuable because it relates specific computational functions to specific anatomical structures, most notably the central complex and the mushroom body. It is an important addition to both the literature on the insect central complex, as well as to theoretical work on insect navigation. Many testable predictions can be made based on the presented models. The figures are well made and the writing is compact. Nevertheless, several points need to be addressed.

Reviewer #3

The authors report the use of a novel model of intracardiac infusion of Aβ peptides in zebrafish larvae to study the effects of Aβ on sleep and neuronal activity. They provide convincing data that preparations of shorter Aβ oligomers induce neuronal activity and decrease sleep, while longer oligomers suppress neuronal activity and decrease sleep. They then delete known Aβ receptor proteins, and show that the effects of Aβ-short can be blocked by deletion of Adrb2 and Pgrmc1, while the effects of Aβ-long are blocked by prion protein deletion, or specific drugs.

This is a unique system and the method for administering Aβ that is quite powerful, and the experiments are rigorous and generally use multiple converging approaches (for instance genetic+pharmacologic) to support their findings. The reversibility of the effect, as well as blockade with specific pharmacological agents suggests that these are not non-specific toxic events. The findings provide a framework with which to potentially test other neurodegenerative proteins (such as a-syn), and to inform similar studies in mammalian systems.

1) While the experiments are well performed and the data intrinsically consistent, the applicability to mammals (and humans) is a consideration. Infusion of Aβ into the heart of larvae is a highly artificial system, and events that occur during sudden changes in Aβ levels may be different that those observed when Aβ is chronically present (as in AD). For example, infusion of Aβ peptide into the brains of mice or rats can induce acute, local neurodegeneration that is not observed in APP transgenic mice with chronically elevated Aβ levels. This is a fundamental shortcoming of the model, and there is little that can be done to address it, but it should be perhaps mentioned in the Discussion.

2) The implications of this bidirectional effect of short and long oligomers for sleep phenotypes in AD are also a bit unclear, as oligomers of all sizes are likely present in AD brain (though perhaps in different ratios as the disease progresses). It would be helpful to determine which pathway is dominant when both short and long oligomers are infused together, perhaps in different ratios. This is the only experiment I would suggest.

Reviewer #2

The use of zebrafish to investigate the role of beta amyloid polymers on sleep/wake regulation is potentially interesting as AD patients suffer from insomnia. Here Ozcan and colleagues inject oligomers synthesized in vitro into the fish neonate hearts and fish motion was then recorded and used as a proxy for sleep and wake states. The authors found a correlation between the polymer length and the impact on fish motor and brain activity.

While the findings are potentially interesting, several points are unclear or concerning to the reviewer:

1) First, all the experiments and interpretations rely on overexpression of Abeta polymers; there is no description or investigation in this study of the normal baseline of Abeta accumulation in this species. One would expect to see such data in Fig. 1 and S1 for example. Is there in fish a night vs. day, sleep vs. night rhythm of Abeta accumulation/expression?

2) The fish undergo anesthesia and heart perforation and are recorded a few hours later. How can handling, surgical stress, and confounds of prior anesthesia be eliminated from "sleep-wake" data interpretation?

3) It is hard for the reader to distinguish a specific effect on sleep/wake. Increased or decreased motion could be due to toxicity or specific stimulation of neuronal circuits due to non physiological presence of exogenous oligomers. The authors try to tackle this issue with cfos and ERK staining, but Fig. 2 shows at least 6 different staining patterns, none of them compared to a sleep/wake baseline of staining. It is quite worrisome to see such a broad over expression of cfos throughout the brain when A beta is accumulated. Are the fish having a seizure? Toxicity could lead to reduced motion and even if it's reversible it can still be transient toxicity until oligomers are washed out. Hyperactivity could be due to a specific overstimulation of neurons as illustrated by cfos and ERK staining.

4) Injections in mutant backgrounds indeed show some specificity in binding/interaction but still it does not demonstrate that the impact is on wake or sleep regulation per se. Again only motion or broad brain staining (at one time point) are shown. An alternative interpretation is that adrb2a, pgrmc, prp1 can indeed bind Abeta but relay the toxic or aspecific impact of oligomers over expression in a brain that normally does not accumulate such molecules.

This study has the potential to be extremely interesting but many controls and demonstration of endogenous Abeta role on sleep-wake cycle are needed.

Reviewer #1

There is a growing appreciation about the fundamental bidirectional link between sleep and Alzheimer's disease. Here Rihel and colleagues use a zebrafish model coupled to the injection of amyloid beta oligomers (the initiating pathogenic species for AD) to examine the link between Abeta and sleep. They demonstrate that the length of the oligomers determines whether Abeta induces wake (short Abeta) or sleep (long Abeta), providing novel insights into the role of different forms on sleep/wake. Importantly, they extend their findings to reveal novel molecular insights into the mechanisms into how Abeta exerts these sleep/wake effects. Overall, the findings make an important advance that will be of interest to a broad readership.

I have one significant concern relating to claims that these studies reveal novel functions for the endogenous Abeta. A key missing experiment in this regard is manipulation of the endogenous Abeta gene/protein (or even assessment of endogenous Ab) and thus it is unclear if exogenous (intracardiac) injection of Abeta faithfully reproduces how an endogenous neuronal pathway would deliver Abeta in terms of location, local concentrations and kinetics. I think the findings are significant and important on their own without having to make this claim, which in this case is highly speculative. I would suggest either addressing experimentally or rewording and de-emphasizing this point in the text to make clear the speculative possibilities. In any case, these shortcomings should be more forthrightly noted.

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 preprint: https://www.biorxiv.org/content/10.1101/610014v2

Summary

This study describes the use of intracardiac infusion of various sized amyloid-beta (Aβ) peptides in zebrafish larvae to study the effects of Aβ on sleep and neuronal activity and dissect the molecular mechanism of their action. They show that short Aβs induce neuronal activity and decrease sleep, while long Aβs suppress neuronal activity and decrease sleep. They use genetic perturbations to show that short Aβs act through Adrb2 and Pgrmc1, while long Aβs act via PrP.

As described below, the reviewers consider this manuscript to be a potentially important methodological and conceptual advance, but recommend that the authors address the following concerns:

The model is based on intracardiac injection of Abeta, so the phenotypes result from exogenous expression/overexpression. Given this, the authors should refrain from drawing conclusions about endogenous Abeta. At the same time, the manuscript would benefit from minimal characterization of the endogenous molecules. For instance, is there a rhythm of Abeta expression over the sleep:wake cycle?

The fish undergo anesthesia and heart perforation and are recorded a few hours later. What are the controls for handling, surgical stress, and confounds of prior anesthesia? On a related note, can the authors exclude toxicity, which could affect motion? They address this point by showing cfos and ERK staining, but many different patterns are observed and none are compared to staining under baseline sleep:wake conditions. It is also concerning that the c-fos expression is so widespread. The reversibility of the effect is important and the role of specific molecules is interesting, but these still do not demonstrate impact on wake or sleep regulation per se.

Given that AD brains likely have oligomers of all sizes, it would be good to know what happens when short and long oligomers are infused together.

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Reply to the reviewers

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

The manuscript describes two advances. First is the technical development for a protein targeting system called PInT that brings a target protein close to (~320 bp) a DNA sequence of interest. The idea is that localisation of the target protein allows one to distinguish its effects on the DNA sequence either in cis (when targeted) or in trans (when not targeted but expressed at the same level). Since targeting is conveyed by simply adding the small molecule ABA to the experiment, it is easy to compare the two situations. This is a clever idea and it is substantiated by data showing that the components of PInT do not affect triplet repeat instability or gene expression of GFP, into whose gene the PInT system is placed. Moreover, targeting is shown to enable enzymatic activity in the targeted region. Using the DNA methylase DNMT1, there are local increases in DNA methylation. Similarly, targeting the histone deacetylase HDAC5 results in local decreases in histone H3 acetylation.

We thank the reviewer for a thoughtful and helpful review.

What is not clear from these experiments, however, is whether the targeted proteins can interact normally with partner proteins to form functional complexes. One necessary control is to add ChIP for at least one interacting protein each for DNMT1 and for HDAC5 and show that targeting permits normal protein-protein interactions. This experiment is straightforward as specific interacting proteins are known and good antibodies to precipitate those proteins are available.

This is a good suggestion and we plan on doing this experiment in our 59B-Y-HDAC5 and 89B-Y-DNMT1 lines with and without ABA using interacting proteins. The exact interacting protein to be used will depend on the antibodies availability and quality, which we will test. We will start with UHRF1 and HDAC3 for PYL-Dnmt1 and PYL-HDAC5, respectively.

Overall, PInT would likely be useful for many groups studying the effects of chromatin modifiers on a DNA sequence of interest.

The second advance is conceptual and is focused more specifically on triplet repeat expansions. The manuscript describes experiments that measure genetic instability of long CAG-CTG repeats with and without protein targeting. The results show that allele size distributions are not significantly affected by targeting either DNMT1 or HDAC5. One curious outcome that is not discussed is contraction frequency in the HDAC5 experiment. Zero contractions are reported compared to 10-20% contractions in the other two experiments. Authors need to provide an explanation.

Lack of contractions in this experiment is likely due to the lower number of repeats in this line (59 vs 89/91). It is known that longer repeats display higher frequency of contractions, and contractions are rarely seen in short repeats (Larson et al Neurobiology of Disease 2015, Gomes-Pereira et al PLOS Genet 2007, Morales et al HMG 2020). Albeit, the threshold may be different in our HEK293-derived cells. Of note, we had a clone of 89B-Y-HDAC5 that did not express the expected amount of GFP for unknown reasons and we did not use it here. However, small pool PCRs using this line with 89 repeats showed that contractions were indeed present. Although we cannot rule out that the reason for the contractions is the unknown mutation(s), it suggests that the difference is due to the size of the expansion. We have added a comment in the methods section.

It reads: “We have noted that cell lines with repeats that are mildly expanded (e.g., 59 CAGs) have fewer contractions than longer ones. This is consistent with several studies in the context of DM1 and HD [82], albeit the size threshold for seeing more contractions may be shorter in HEK293-derived cells than in mice.”

The major issue with this set of experiments is that there is no positive control where instability is shown to be clearly manipulated. A knockdown of FAN1 would be the most likely avenue to pursue for identifying a positive control. This is straightforward to perform since successful FAN1 knockdowns have been described in the literature.

We agree that a positive control to show that the model behaves as expected is necessary. We will add the experiments proposed by the reviewer in the revised version of the manuscript.

The manuscript also looks at effects on gene expression measured by GFP fluorescence intensity. The potential significance is to see if disease-causing genes with expanded triplet repeats can be silenced by targeting chromatin-modifying enzymes. In the examples tested here, the answer seems to be no. Expression of DNMT1 or HDAC5 reduce fluorescence even in the absence of targeting. Upon targeting, there is a small further decrease, but the expanded triplet repeat resists this further decrease. Domain analysis of HDAC5 indicates that protein-protein interactions, not deacetylase activity, are important for silencing. The key interaction may be with HDAC3, since small molecule inhibition of HDAC3 relieved repeat length-dependent silencing by HDAC5. It was very curious that targeting HDAC3 actually increased expression, instead of silencing. The explanation for this observation was inadequate.

We have added the following paragraph to the discussion to address this.

It reads: “We found that targeting of PYL-HDAC3 increases gene expression slightly, independently of repeat size and in the presence of an inhibitor of its catalytic activity. Although this appears counterintuitive, several studies suggest that this is not unexpected. Specifically, HDAC3 has an essential role in gene expression during mouse development that is independent of its catalytic activity [73]. Moreover, HDAC3 binds more readily to genes that are highly expressed in both human and yeast cells [74,75]. The mechanism or function of HDACs binding to highly expressed genes are currently unknown.”

The claim on page 16 final paragraph that the manuscript 'settled a central question for both HDAC5 and DNMT1 and their involvement in CAG/CTG repeat instability' is not supported by the data. Most of the results are negative so it is premature to claim the question is 'settled'.

We have rephrased all the conclusions about this in the text, emphasizing that we find no evidence of a role in cis, rather than stating that there is no role in cis.

Overall, with appropriate modifications described here, these experiments would be of interest with regards to potential therapies of triplet repeat expansion diseases, where silencing the expanded gene is the goal.

**Minor concerns**

P 4, last line. 59 bp should read 59 repeats - This is now fixed.

P 5, line 2. 38 bp of what? This is now amended. It reads: “The CAG/CTG repeats affect splicing of the reporter in a length-dependent manner, with longer repeats leading to more robust insertion of an alternative CAG exon that includes 38 nucleotides downstream of the CAG, creating a frameshift [30].”

P 10, first paragraph. DNA methylation levels rise from ~10% to ~20% with DNMT1 targeting. Is there a good precedent in the literature that the magnitude of this increase can be expected to be biologically meaningful?

To our knowledge, it is the first time that DNMT1 is used for targeted epigenome editing. This is therefore the first evidence that targeting DNMT1 leads to silencing of a reporter construct. Nevertheless, this reviewer’s comment stands: is an increase in DNA methylation of 10 to 20% biologically relevant? The answer to this is yes, changes in 10-20% are known to have functional impact on gene expression in various settings (for example see the recent study in developing oocytes by Li et al Nature 2018). Furthermore, there is evidence that DNMT1 has weak de novo activity (Li et al Nature 2018, Wang et al Nat Genet 2020), consistent with a small increase in CpG methylation upon targeting. We now acknowledge in the discussion that one reason for the lack of effect upon targeting may be that the changes in CpG methylation are not dramatic enough. We also point out more clearly that changes of 10 to 20% are correlated with changes in repeat instability (Dion et al HMG 2008). We have amended the text to reflect this.

The results now reads “To do so, we performed bisulfite sequencing after targeting PYL-DNMT1 for 30 days. This led to changes of 10 to 20% in the levels of CpG methylation, a modest increase(Fig. 3C), which is in line with the weak de novo methyltransferase activity of DNMT1 (for example see [39,40]). Similar changes in levels of CpG methylation in Dnmt1 heterozygous ovaries and testes were seen to correlate with changes in repeat instability in vivo [31].”

The discussion now states: “It should be pointed out that there remains the possibility that DNMT1 targeting did not lead to large enough changes in CpG methylation to affect repeat instability.”

P12 first paragraph. Text describing Fig 5 is confusing. First, GFP expression is referred to in terms of fold decrease, but subsequently in percent. Second, the ABA-induced silencing looks to reduce expression from about 0.6 to 0.5 of control. I presume this is where the claim of 16% comes from but it was not clear. Indeed, this is what we mean.

We now state: “In 16B-Y-DNMT1 cells, ABA treatment decreased GFP expression by 2.2-fold compared to DMSO treatment alone. Surprisingly, ABA-induced silencing was 1.8 fold compared to DMSO alone, or 16% less efficient in 89B-Y-DNMT1 than in 16B-Y-DNMT1 cells.”

P 15 paragraph 2. Where does the P value of 0.78 come from? Fig 7B shows no corresponding value. The P-value in figure 7B has now been corrected.

Reviewer #1 (Significance (Required)):

See above.

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

**Summary:**

We still do not know whether epigenetics contributes to repeat instability and/or transcriptional activity in unstable CAG/CTG repeat associated pathologies. The aim of this manuscript is to examine whether induced binding of DNMT1 (CpG methylation) or HDAC5 (histone H3 acetylation) modulates CAG/CTG repeat instability and/or gene silencing upon expansion. For this the authors developed a highly sophisticated reporter system (PlnT) that allows to recruit a specific chromatin modifying enzyme (DNMT1/ HDAC5) to a GFP reporter near a CAG/CTG expansion, in the course of transcription (Dox-inducible promoter). This is to determine whether the CTGs, when lengthened and transcribed, become unstable or impede gene activity via epigenetic modifications.

We appreciate the reviewer highlighting the importance of the question that we address here and the usefulness of PInT.

**Findings:**

1.Binding of DNMT1 to the reporter results in a modest increase (~10%) in local DNA methylation, with no change in repeat instability.

3.Targeting HDAC5 to the reporter results in local reduction in histone H3 acetylation, with no effect on repeat stability.

4.DNMT1/HDAC5 binding reduces GFP intensity differentially, in normal but not expanded alleles.

5.The N-terminal domain of HDAC5, when mutated, abolishes the reduction in GFP expression levels.

6.RGFP966 abolishes the allele-specific effect of HDAC5, resulting in a general decrease in GFP expression regardless of repeat tract size

7.CTG expanded alleles abolish the reduction in GFP repression by HDAC5 via HDAC3 activity

**Conclusions:**

Based on the results using the PlnT reporter assay, the authors claim that:

1.HDAC5 and DNMT1 do not affect repeat instability in cis

2.Expanded CAG/CTGs reduce the efficiency of gene silencing by targeting DNMT1/HDAC5 to the locus

3.Gene silencing that is mediated by HDAC5 recruitment can be abolished by inhibition of HDAC3 activity

Unfortunately, none of the claims in this manuscript are convincing.

We note that in the comments below the reviewer does not include a reason why he/she does not find the claims convincing. We therefore cannot address this criticism.

**General Comments:**

The major drawback of the PlnT experimental approach is that it ignores the importance of the flanking regions and the genomic organization of the endogenous locus. This is a major concern as it makes the conclusions irrelevant to the related loci. In the case of myotonic dystrophy type 1, for example, the reporter should reside within a CpG island, should be positioned immediately next to CTCF binding site(s), and should be transcribed bi-directionally.

HDAC3 and DNMT1 were found to have effects on repeat instability both at reporters, which do not harbour flanking sequences from disease loci, and indeed at endogenous loci in vivo (Dion et al HMG 2008, Debacker et al PLoS Biol 2012, Suelves et al Sci Rep 2017, Williams et al PNAS 2020). This highlights the fact that cis elements from disease loci are not required for chromatin modifiers to affect repeat instability.

The reviewer is suggesting a very interesting set of experiments where specific sequences may be added to our reporter and tested for their influence on gene expression and on repeat instability. PInT is ideally suited for this and we have now added a paragraph highlighting this in the discussion. We have also highlighted that the current study aims to isolate the repeats from its cis-elements to specifically side-step potential locus-specific effects and to look for chromatin modifiers that would be useful for epigenome editing for as many loci as possible.

Furthermore, only large expansions (at least several hundred copies) can trigger heterochromatin at the DM1 locus. None of these features are recapitulated by the PlnT reporter assay, making it difficult to draw any conclusion regarding the role of these chromatin modifying enzymes to the locus.

This is true for DM1 but untrue for other disease loci. For example, we have shown that there are changes in the flanking chromatin marks at the SCA1 locus of a mouse model with 145 repeats (Dion et al HMG 2008), DNA methylation is also affected near a SCA7 transgene with 92 CAG repeats (Libby et al PLoS Genet 2008) and transgenes containing CAG repeats (without the flanking sequences) lead to silencing regardless of where the transgene is integrated in the genome (Saveliev et al Nature 2003). Moreover, HDAC5 had effects on repeat expansion in a cell-based shuttle system containing as few as 22 CAG repeats (Gannon et al NAR 2012), again suggesting that chromatin modifiers affect repeat instability in a wide range of repeat sizes. We have reviewed this in Dion and Wilson TiG 2009.

In fact, the authors state in their Discussion that "targeting a chromatin modifying peptide to different loci can have very different effects"!

This is indeed the case and the reason why we sought to control for locus-specific effects using an exogenous reporter.

To better substantiate their conclusions the authors must set up an improved model system that takes into account the flanking regions and the 3D genomic organization of the locus (TADs). The preferable approach would be to insert a reporter cassette by homologous recombination into the differentially methylated/acetylated regions near the repeats, and compare between normal vs. expanded alleles.

We would like to point out that we have recently published a study where we looked at 3D chromatin folding at the DM1, HD, and the GFP transgene used here. We did not find any evidence for changes in TADs that would underlie changes in repeat instability at these loci (Ruiz Buendia et al Sci Advances 2020). We therefore do not think that it would be important to further manipulate 3D genomic organization in this context.

To be clear, we are not denying that cis elements are likely to have an effect, there is plenty of evidence supporting this. Rather, we are using a reporter assay to disentangle the potential locus-specific (or cis-element specific) effects from the trans-activating factors. In short, we focus on the trans-acting factors rather than on the cis-elements, as suggested by the reviewer.

We believe that the addition of the following paragraph highlights the goal of our study and also bring in the idea that cis acting elements can be studied using PInT.

It now reads:

“We designed PInT specifically to isolate expanded repeats tracts from other potential locus-specific cis elements. This is helpful to identify factors that would affect instability and/or gene expression across several diseases. Moreover, both HDAC3 and DNMT1 were found to impact repeat instability at different loci, including at reporter genes [31,33,36,37,45]. These observations highlight that cis-acting elements from disease loci are not required by chromatin modifiers to affect repeat instability. A potential application of PInT includes cloning in specific cis elements, including CTCF binding sites and CpG islands, next to the repeat tract and evaluate their effects on instability with or without targeting. In fact, PInT can be used to clone any sequence of interest near the targeting site and can be applied for a wide array of applications, beyond the study of expanded CAG/CTG repeats.”

My impression was that there is a lot of data but none of it makes sense.

The focus of the manuscript is not entirely clear: it starts with monitoring the effect of epigenetics on repeat instability and gene activity, then it shifts to the mechanism by which HDAC5 functions, and ends with the allele-specific effect of HDAC5 on gene expression. I lost my train of thought.

We have now improved the transitions in this new version of this manuscript. Specifically, at the core of this manuscript is the development of PInT, which is highly versatile and allowed us to study multiple aspects of expanded CAG/CTG repeat biology. We hope that it is now clearer.

**Other concerns:**

(1)the modest increase in methylation levels following DNMT1 recruitment (10%, reaching a total of 20% at the most) prevents from drawing any conclusions regarding the effect of methylation on stability or expression.

As mentioned in the response to reviewer 1 above, although 10% to 20% of CpG methylation are associated with changes in gene expression in a variety of settings, we now point out that one reason for the lack of effect in cis is that the de novo activity of DNMT1 is too weak to produce an effect.

(2)The effect of protein targeting on GFP levels should be better defined at the RNA/protein level. Does it act by blocking transcription? alternative splicing? or alters steady state levels?

Although the exact mechanism remains unclear, this goes beyond the current scope of this study. All these possibilities remain possible as we pointed out in the discussion.

(3)Fig 5: the scale is different for A vs. B and C. Also, better to compare the effect of targeting on equal sized expansions (either 91, 89 or 58 repeats).

We have fixed the scale on the figures.

Unfortunately, it is not possible to have the same repeat sizes for all the cell lines because by their very nature, repeats are unstable. We have added a note relating to this in the methods.

It reads: “Notably, it is not possible to obtain several stable lines with the exact same repeat size as they are, by their nature, highly unstable. This is why we have lines with different repeat sizes. Furthermore, the sizes can change over time and upon thawing.”

(4)Add asterix for significance in all figures.

This has now been done.

(5)Figure 6: show raw data rather than normalized.

We have now added representative flow cytometry profiles for each construct as a new supplementary figure (S5).

(6)Figure 7: there is a notable difference in GFP expression levels in untreated wild type control (16 CAG repeats) between A vs. B. Why?

Fig. 7a shows PYL targeting only, whereas 7b shows the GFP expression upon PYL-HDAC5 targeting. The values for PYL-HDAC5 targeting are lower because targeting it, unlike targeting PYL alone, silences the reporter.

(7)Avoid redundancy. No need to show schematic representations so many times.

We believe that the schematics make it clearer for the reader.

Reviewer #2 (Significance (Required)):

REFEREES CROSS-COMMENTING

I totally agree with the Reviewer #1 that the PinT targeting system is a potent experimental tool to study the function of specific chromatin binding proteins. However, the significance of the flanking regions is discounted.

We hope it is now clear that we are not discounting the potential significance of flanking regions and that rather we have designed the system to avoid their potentially complicating effects.

The fact that the recruitment of HDAC5 has resulted in a significant reduction in acetylated histones provides evidence for that "the targeted proteins can interact normally with partner proteins to form functional complexes". Still, I agree with that the activity of DNMT1 needs to be better established, considering the minor increase in DNA methylation levels.

We will be using ChIP against interacting proteins of DNMT1 and HDAC5 to address this issue.

The request for a positive control for repeat instability is totally correct.

We will be adding this in the revised manuscript.

It is difficult to discuss the missing effect of HDAC5 on contractions or the unexpected effect of HDAC3 on gene silencing bearing in mind the limits of the experimental system.

There is no expectation for the effect of HDAC5 on contractions as this has not been studied in any system yet. However, we believe that there is no contractions not because of HDAC5 per se but rather because of the shorter repeat size this line has (see comment to reviewer 1 above). We have now addressed the “unexpected effect” of HDAC3 by citing a number of studies finding a similar evolutionary conserved effect (see comment to Reviewer 1 above).

I also agree with the statement that "this manuscript settled a central question for both HDAC5 and DNMT1 and their involvement in CAG/CTG repeat instability", is not supported by the data.

We have now rephrased our conclusions. In this particular case, we changed ‘settled’ to ‘addressed’. We have also rephrased this in the results headings.

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

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Referee #2

Evidence, reproducibility and clarity

Summary:

We still do not know whether epigenetics contributes to repeat instability and/or transcriptional activity in unstable CAG/CTG repeat associated pathologies. The aim of this manuscript is to examine whether induced binding of DNMT1 (CpG methylation) or HDAC5 (histone H3 acetylation) modulates CAG/CTG repeat instability and/or gene silencing upon expansion. For this the authors developed a highly sophisticated reporter system (PlnT) that allows to recruit a specific chromatin modifying enzyme (DNMT1/ HDAC5) to a GFP reporter near a CAG/CTG expansion, in the course of transcription (Dox-inducible promoter). This is to determine whether the CTGs, when lengthened and transcribed, become unstable or impede gene activity via epigenetic modifications.

Findings:

1.Binding of DNMT1 to the reporter results in a modest increase (~10%) in local DNA methylation, with no change in repeat instability.

3.Targeting HDAC5 to the reporter results in local reduction in histone H3 acetylation, with no effect on repeat stability.

4.DNMT1/HDAC5 binding reduces GFP intensity differentially, in normal but not expanded alleles.

5.The N-terminal domain of HDAC5, when mutated, abolishes the reduction in GFP expression levels.

6.RGFP966 abolishes the allele-specific effect of HDAC5, resulting in a general decrease in GFP expression regardless of repeat tract size

7.CTG expanded alleles abolish the reduction in GFP repression by HDAC5 via HDAC3 activity

Conclusions:

Based on the results using the PlnT reporter assay, the authors claim that:

1.HDAC5 and DNMT1 do not affect repeat instability in cis

2.Expanded CAG/CTGs reduce the efficiency of gene silencing by targeting DNMT1/HDAC5 to the locus

3.Gene silencing that is mediated by HDAC5 recruitment can be abolished by inhibition of HDAC3 activity

Unfortunately, none of the claims in this manuscript are convincing.

General Comments:

The major drawback of the PlnT experimental approach is that it ignores the importance of the flanking regions and the genomic organization of the endogenous locus. This is a major concern as it makes the conclusions irrelevant to the related loci. In the case of myotonic dystrophy type 1, for example, the reporter should reside within a CpG island, should be positioned immediately next to CTCF binding site(s), and should be transcribed bi-directionally. Furthermore, only large expansions (at least several hundred copies) can trigger heterochromatin at the DM1 locus. None of these features are recapitulated by the PlnT reporter assay, making it difficult to draw any conclusion regarding the role of these chromatin modifying enzymes to the locus. In fact the authors state in their Discussion that "targeting a chromatin modifying peptide to different loci can have very different effects"! To better substantiate their conclusions the authors must set up an improved model system that takes into account the flanking regions and the 3D genomic organization of the locus (TADs). The preferable approach would be to insert a reporter cassette by homologous recombination into the differentially methylated/acetylated regions near the repeats, and compare between normal vs. expanded alleles.

My impression was that there is a lot of data but none of it makes sense.

The focus of the manuscript is not entirely clear: it starts with monitoring the effect of epigenetics on repeat instability and gene activity, then it shifts to the mechanism by which HDAC5 functions, and ends with the allele-specific effect of HDAC5 on gene expression. I lost my train of thought.

Other concerns:

(1)the modest increase in methylation levels following DNMT1 recruitment (10%, reaching a total of 20% at the most) prevents from drawing any conclusions regarding the effect of methylation on stability or expression.

(2)The effect of protein targeting on GFP levels should be better defined at the RNA/protein level. Does it act by blocking transcription? alternative splicing? or alters steady state levels?

(3)Fig 5: the scale is different for A vs. B and C. Also, better to compare the effect of targeting on equal sized expansions (either 91, 89 or 58 repeats).

(4)Add asterix for significance in all figures.

(5)Figure 6: show raw data rather than normalized.

(6)Figure 7: there is a notable difference in GFP expression levels in untreated wild type control (16 CAG repeats) between A vs. B. Why?

(7)Avoid redundancy. No need to show schematic representations so many times.

Significance

REFEREES CROSS-COMMENTING

I totally agree with the Reviewer #1 that the PinT targeting system is a potent experimental tool to study the function of specific chromatin binding proteins. However, the significance of the flanking regions is discounted. The fact that the recruitment of HDAC5 has resulted in a significant reduction in acetylated histones provides evidence for that "the targeted proteins can interact normally with partner proteins to form functional complexes". Still, I agree with that the activity of DNMT1 needs to be better established, considering the minor increase in DNA methylation levels. The request for a positive control for repeat instability is totally correct. It is difficult to discuss the missing effect of HDAC5 on contractions or the unexpected effect of HDAC3 on gene silencing bearing in mind the limits of the experimental system. I also agree with the statement that "this manuscript settled a central question for both HDAC5 and DNMT1 and their involvement in CAG/CTG repeat instability", is not supported by the data.

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Referee #1

Evidence, reproducibility and clarity

The manuscript describes two advances. First is the technical development for a protein targeting system called PInT that brings a target protein close to (~320 bp) a DNA sequence of interest. The idea is that localisation of the target protein allows one to distinguish its effects on the DNA sequence either in cis (when targeted) or in trans (when not targeted but expressed at the same level). Since targeting is conveyed by simply adding the small molecule ABA to the experiment, it is easy to compare the two situations. This is a clever idea and it is substantiated by data showing that the components of PInT do not affect triplet repeat instability or gene expression of GFP, into whose gene the PInT system is placed. Moreover, targeting is shown to enable enzymatic activity in the targeted region. Using the DNA methylase DNMT1, there are local increases in DNA methylation. Similarly, targeting the histone deacetylase HDAC5 results in local decreases in histone H3 acetylation. What is not clear from these experiments, however, is whether the targeted proteins can interact normally with partner proteins to form functional complexes. One necessary control is to add ChIP for at least one interacting protein each for DNMT1 and for HDAC5 and show that targeting permits normal protein-protein interactions. This experiment is straightforward as specific interacting proteins are known and good antibodies to precipitate those proteins are available. Overall, PInT would likely be useful for many groups studying the effects of chromatin modifiers on a DNA sequence of interest.

The second advance is conceptual and is focused more specifically on triplet repeat expansions. The manuscript describes experiments that measure genetic instability of long CAG-CTG repeats with and without protein targeting. The results show that allele size distributions are not significantly affected by targeting either DNMT1 or HDAC5. One curious outcome that is not discussed is contraction frequency in the HDAC5 experiment. Zero contractions are reported compared to 10-20% contractions in the other two experiments. Authors need to provide an explanation. The major issue with this set of experiments is that there is no positive control where instability is shown to be clearly manipulated. A knockdown of FAN1 would be the most likely avenue to pursue for identifying a positive control. This is straightforward to perform since successful FAN1 knockdowns have been described in the literature. The manuscript also looks at effects on gene expression measured by GFP fluorescence intensity. The potential significance is to see if disease-causing genes with expanded triplet repeats can be silenced by targeting chromatin-modifying enzymes. In the examples tested here, the answer seems to be no. Expression of DNMT1 or HDAC5 reduce fluorescence even in the absence of targeting. Upon targeting, there is a small further decrease, but the expanded triplet repeat resists this further decrease. Domain analysis of HDAC5 indicates that protein-protein interactions, not deacetylase activity, are important for silencing. The key interaction may be with HDAC3, since small molecule inhibition of HDAC3 relieved repeat length-dependent silencing by HDAC5. It was very curious that targeting HDAC3 actually increased expression, instead of silencing. The explanation for this observation was inadequate. The claim on page 16 final paragraph that the manuscript 'settled a central question for both HDAC5 and DNMT1 and their involvement in CAG/CTG repeat instability' is not supported by the data. Most of the results are negative so it is premature to claim the question is 'settled'. Overall, with appropriate modifications described here, these experiments would be of interest with regards to potential therapies of triplet repeat expansion diseases, where silencing the expanded gene is the goal.

Minor concerns

P 4, last line. 59 bp should read 59 repeats

P 5, line 2. 38 bp of what?

P 10, first paragraph. DNA methylation levels rise from ~10% to ~20% with DNMT1 targeting. Is there a good precedent in the literature that the magnitude of this increase can be expected to be biologically meaningful?

P12 first paragraph. Text describing Fig 5 is confusing. First, GFP expression is referred to in terms of fold decrease, but subsequently in percent. Second, the ABA-induced silencing looks to reduce expression from about 0.6 to 0.5 of control. I presume this is where the claim of 16% comes from but it was not clear.

P 15 paragraph 2. Where does the P value of 0.78 come from? Fig 7B shows no corresponding value.

Significance

See above.

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Reply to the reviewers

Reviewer #1

Summary

The authors present well written work on the evolution of proteome size and complexity, and the corresponding changes in chaperone proteins. Interestingly, they find chaperone copy numbers increase linearly with proteome size, despite the increasing 'complexity' of, in particular, post-LECA genomes. They suggest that to address the rise in complexity, organisms express chaperones at higher levels and an expanding network of co-chaperones has evolved across the tree of life.

Major comments

Comment-1. Summary reads strangely relative to the rest of the manuscript, and lists facts in a way that makes the purpose of the study confusing. I think most readers will dislike the characterisation of evolution as a progress from simple to complex, and the authors' might want to avoid this language throughout the manuscript- bacteria and archaea have also been evolving over this period of times, and have not become more 'complex'? Similarly the authors should reconsider their figure legend titles. As a specific example, 'in the course of evolution' should become 'across the tree of life'.

Response

Thank you for these crucial suggestions. We agree with the reviewer, and with Reviewer 2 (see below) that bacteria and archaea have also been evolving since their emergence, so basically, we (humans) and the simplest archaea have the same evolutionary origin. However, we all agree that the simplest archaea/bacteria are far more similar to LUCA than we are. That said, we accept the criticism that putting our analysis in the context of evolutionary time is an over-interpretation given that we have not examined the protein/proteome phylogeny (in relation to proteome complexity; for chaperones we have). We have thus reformulated the figures and text, to a comparison across the Tree of life, rather than a time-dependent evolutionary process. Specifically: as a first step, we revised the Figures to rename the X-axis as “Order of divergence”, rather than “Divergence time (million years)” in the previous version. In the revised main text we emphasized the fact that the branch lengths of the Tree of Life represent the relative order of divergence of the different clades, rather than time. All instances of ‘in the course of evolution’ has been replaced by ‘across the Tree of Life’.

Secondly, we revised the main text to emphasize on prokaryote vs. eukaryote comparison, rather than comparing organisms that diverged at different time-points. Within bacterial and archaeal domains, proteomes do not seem to expand against the order of divergence (as the reviewer argued, bacteria and archaea have not become more complex, also see Comment-5).

Thirdly, the word ‘complexity’ has been omitted from the manuscript. The section “The expansion of proteome complexity” now reads as “Proteome expansion by de novo innovations”. In the previous version, increasing complexity in fact implied a torrent of de novo innovations that impose a larger burden on the chaperone machinery. Instead of ‘complexity’, the latter is clearly stated in the revised manuscript.

In the spirit of these changes, the title of the revised manuscript, figure legend titles, and related section titles have been edited as follows.

Submitted version

Revised version

Paper title. On the evolution of chaperones and co-chaperones and the exponential expansion of proteome complexity

On the evolution of chaperones and co-chaperones and the expansion of proteomes across the Tree of Life

Section title. A Tree of Life analysis of the expansion of proteome complexity and chaperones

A Tree of Life analysis of the expansion of proteomes and chaperones

Section title. The expansion of proteome size

The expansion of proteome size across the Tree of Life

Section title. The expansion of proteome complexity

Proteome expansion by de novo innovations

Figure 1 legend title. Expansion of proteome size

Expansion of proteome size across the Tree of Life

Figure 2 legend title. Expansion of proteome complexity

Expansion of proteomes by de novo innovations

Further, changes have been made in the Summary and in the main text to exclude any impression that proteomes/organisms have become more complex with time. Rather we emphasized prokaryote versus eukaryote comparison.

Comment-2. I think the manuscript would be improved if the authors significantly shortened the discussion of genome size evolution- this is fairly well understood, and could be covered briefly, especially as the main focus of the manuscript is on the evolution of chaperone and co-chaperone repertoire. They could also make clearer quantitative links between protein complexity and the evolution of chaperones and co-chaperones- perhaps this should be in the discussion? The authors might also consider referencing 'The evolution of genome complexity', which could be relevant to this manuscript and might make the work of broader interest.

Response

We thank the reviewer for this suggestion. The main focus of our paper is indeed the evolution of chaperones and co-chaperones but within the context of the expansion of proteomes. Having this focus in place, the discussion on proteome size evolution (section: The expansion of proteome size across the Tree of Life) has been revised and shortened to emphasize more on prokaryote versus eukaryotic comparison.

The suggestion to provide “clearer quantitative links between protein complexity and the evolution of chaperones and co-chaperones” is indeed very useful and we authors sincerely thank the reviewer. To address this suggestion we revised Figure 4 to quantitatively compare the expansion of proteomes and that of chaperones, under one roof. This Figure compares proteome parameters that supposedly demands more chaperone action in all three domains of life and simultaneously summarizes the expansion of the chaperone machinery lacking de novo innovations.

The first paragraph of the Discussion section has been revised accordingly that walks the reader through the revised Figure 4 and finally introduces to the dichotomy it implies.

We did not understand the last comment “The authors might also consider referencing 'The evolution of genome complexity', which could be relevant to this manuscript and might make the work of broader interest.” We’d be glad to address it upon further clarification.

Comment-3. The authors state 'protein trees were generated and compared with ToL to account for gene loss and transfer events'. The methodology for this procedure is not given in the manuscript. The authors should back up this point, and make it clear this is why they reconstruct the trees. Currently it is not convincing to me that the authors have found HGT given the considerable phylogenetic uncertainty in the basal events in the tree of life. I also expect the tree of a single protein to be potentially lack information due to the short sequence considered and possible lack of power. The authors need to consider whether the data is really of high enough quality to assess this.

Response

Thank you for this suggestion. For the various chaperone families, we manually compared the protein trees with the Tree of Life. This is clearly stated in the revised Methods section (see Page 25, Lines 31-32). We agree, however, that the identifying HGT, and in general, trees of single domains that are highly diverged, are tricky. We did our best to address these caveats. Specifically:

We re-evaluated our work in the light of a recent study (PMID: 32316034). This paper discussed the phylogenetic uncertainties associated with molecular dating and re-evaluated the assignment of several protein families to LUCA. A careful analysis revealed that the reviewer is indeed right, meaning many of the HGT events shown in the previous version Figure 3B was indistinguishable from the phylogenetic uncertainties.

Accordingly, we revised the section “The core-chaperones emerged in early-diverging prokaryotes”. We removed the previous version Figure 3B, along with all instances of HGT events mentioned in the main text, except one (archaea to Firmicute HGT of HSP60, which is well-supported by the data and was also detected previously). Dating the emergence of chaperone families was also re-evaluated. Though the major conclusions were not altered, we discussed the phylogenetic uncertainties associated with our work and the overall confidence of each dating analysis. We believe these discussions would be very useful to the readers.

Finally, we note that most of our key assignments (points of emergence, and major HGT events) are in agreement with previous works. Specifically: the emergence of HSP20 and HSP60 to LUCA (Sousa et al., 2016; Weiss et al., 2016) and HSP60 being horizontally transferred from archaea to Firmicute (Techtmann and Robb, 2010) and HSP20 being horizontally transferred between bacterial clades and between bacteria and archaea (Kriehuber et al., 2010).

Comment-4. Methods- the authors could consider taking an alternative source of LUCA proteins, rather than those found in 'Nanoarchaeota and Aquificae': it's possible these are not representative of LUCA, and it seems a somewhat arbitrary choice- the authors could consider using one of the available curated sets, such as that generated by Ranea et al. (2006).

Response

The reviewer is right that a more robust LUCA set could be used. However, given that the revised manuscript focuses on comparison across the ToL, and foremost on prokaryote versus eukaryote comparison, we don’t think that refining this set is important. Foremost, this set was used for one purpose only, for determining changes in domain length. And, the set of 38 X-groups used for this analysis are in fact, the ones present in all organisms across the ToL. Hence, we kept the original analysis, while mentioning that these 38 X-groups are conserved across the ToL, and removed the argument for LUCA assignment. See Page 5, Line 22.

Comment-5. The patterns observed might only hold because of differences in the taxa that diverged pre and post LECA? The authors might consider subgroup analyses to ensure this is not the case. The authors could also consider using methods that take phylogeny into account.

Response

The reviewer is right that within prokaryotic domains proteomes do not seem to expand. For example, excluding a few early-diverging prokaryotes and parasites, proteome size in bacteria and archaea varies within 2000-3000 proteins per proteome. Only when pre-LECA and post-LECA organisms are compared, significant differences are observed. We thank the reviewer for this suggestion. We revised the main text to focus on prokaryote versus eukaryote comparison. This re-focusing does not change any of our major conclusions, but rather puts our analysis in the right context (see Comment 1).

Minor comments

Comment-6. 'Life's habitability has also expanded from its 10 specific niche of emergence-likely deep-sea hydrothermal vents, to highly variable and extreme 11 ranges of temperature, pressure, exposure to high UV-light, dehydration and free oxygen.' This is not really correct, as bacteria and archaea are found worldwide, and in the most extreme environments.

Response

Thank you for this suggestion. We removed the above-mentioned sentence.

Comment-7. 'We reconciled the topology of our tree'- on first read this was not clear, I did not realise the authors were only building trees for subsets of the data- time tree is the best source for the overall topology. The phrase 'manually curated and adjusted' is used in the methods. This language is much too vague, and not a clear explanation of the steps taken.

Response

We apology for this confusion. The overall topology of our Tree of Life is indeed taken for TimeTree. We edited the text in Page 4, Line 4 to clarify this issue.

The obtained tree topology was manually curated and adjusted to depict eukaryotes stemming from Asgard archaea and Alphaproteobacteria, by an endosymbiosis event. This is clearly mentioned in the Methods section (see Page 22, Lines 24-28).

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Reviewer #2

Summary

Rebeaud and colleagues analyze evolution of chaperones compared to the evolution of whole proteome complexity across the entire tree of life. Their principal conclusions are well captured in the following quote from the Discussion:

"Comparison of the expansion of proteome complexity versus that of core-chaperones presents a dichotomy-a linear expansion of core-chaperones supported an exponential expansion of proteome complexity. We propose that this dichotomy was reconciled by two features that comprise the hallmark of chaperones: the generalist nature of core-chaperones, and their ability to act in a cooperative mode alongside co-chaperones as an integrated network. Indeed, in contrast to core chaperones, there exist a consistent trend of evolutionary expansion of co-chaperones."

Major comments

Comment-1. The general theme of the evolution of proteome management is of obvious interest. Unfortunately, the entire analysis is shaky and fails to convincingly ascertain the authors' conclusions. There are many issues. Throughout the manuscript, the authors discuss 'expansion' of the proteome in bacteria, archaea and eukaryotes, creating the impression of a consistent evolutionary trend. No such trend actually exists if one considers the means or medians of proteome sizes within each of the three domains of life (there is a transition to greater complexity in eukaryotes). The maximum complexity, certainly, increases with time which can be attributed to the 'drunkard's walk' effect. This hardly qualifies as 'expansion'.

Response

The reviewer is right that within prokaryotes proteomes do not seem to significantly expand. Reviewer-1 raised a similar concern that prokaryotes and eukaryotes have been evolving for the same period of time and have not expanded significantly. We understand the misconception instated by the earlier version and we thank the reviewers for pointing it out. Accordingly, we revised the main text to clarify these issues, as described in the following.

Firstly, the main text was revised to emphasize on prokaryote versus eukaryote comparison. The reviewer agrees that compared to prokaryotes, “there is a transition to greater complexity in eukaryotes”. This re-focusing does not change any of our major conclusions, but rather provides a systematic comparison that is adequately supported by data.

Secondly, we revised the Figures to rename the X-axis as “Order of divergence”, rather than “Divergence time (million years)” in the previous version. We emphasized the fact that the X-axis actually represent the relative order of divergence of the different clades, rather than absolute dates. This emphasis certainly does not create the impression of a consistent evolutionary trend. Instead, combined with the revised main text, it depicts that only when pre-LECA and post-LECA organisms are compared, clear trends of proteome expansion is observed.

Comment-2. The authors further claim a 'linear' expansion of the chaperone set and 'exponential' expansion of the total proteome size. These are precise mathematical terms and, as such, require fitting to the respective functions. No such thing in this manuscript. Even apart from that shortcoming, the explanation of both 'linear' and 'exponential' are quite confusing. Thus, when explaining the 'linearity' of chaperone evolution, the authors refer to the lack of major innovation among the chaperones. This is correct in itself but has nothing to do with linearity. Apart from the aforementioned conceptual problems, the estimation of the 'exponential' growth of the proteome are naive, inconsistent and inaccurate.

Response

Our uses of ‘linear expansion’ versus ‘exponential expansion’ may have been confusing although we have defined quite clearly what we mean by that (i.e., that it is not the mathematical sense). The statement regarding “the lack of major innovation among the chaperones” was made in this context/definition and was consistent with it.

Nonetheless, to avoid confusion, we revised the main text by excluding the ‘linear expansion’ and ‘exponential expansion’ terms. We simply stated that a torrent of de novo innovations has occurred during the expansion of proteomes from prokaryotes to eukaryotes. In contrast, the evolutionary history of core-chaperones lacks such major innovations. Accordingly, the title of the revised manuscript, figure legend titles, and related section titles have been edited as follows.

Submitted version

Revised version

Paper title. On the evolution of chaperones and co-chaperones and the exponential expansion of proteome complexity

On the evolution of chaperones and co-chaperones and the expansion of proteomes across the Tree of Life

Section title. A Tree of Life analysis of the expansion of proteome complexity and chaperones

A Tree of Life analysis of the expansion of proteomes and chaperones

Section title. The expansion of proteome complexity

Proteome expansion by de novo innovations

Figure 1 legend title. Expansion of proteome size

Expansion of proteome size across the Tree of Life

Figure 2 legend title. Expansion of proteome complexity

Expansion of proteomes by de novo innovations

Comment-3. As the base point for the expansion estimates for archaea and eukaryotes, the authors take parasitic forms. Even leaving aside the highly dubious claims that these organisms belong to the clades that diverged first from the respective ancestors, parasites are not an appropriate choice for such estimates because they certainly are products of reductive evolution. For bacteria, inconsistently, the authors choose a free-living form from a dubious ancient clade, and not even the one with the smallest genome. All taken together, this robs the expansion estimates of any substantial meaning.

Response

This point is overall valid. Although we adamantly reject the insinuation of “dubious claims that these organisms belong to the clades that diverged first from the respective ancestors” – firstly, we did not make any claims to this end, but took the ToL constructed by others (Hedges et al., 2015); second, that these claims are dubious need to backup by counter-evidence/data and with all due respect, neither were provided by the reviewer. However, what is of concern is that in a symbiont/parasite chaperones of the host may have a key role, and thus the comparison to free-living organisms could be misleading. To address this concern we excluded the obligatory endosymbiont Nanoarchaeum equitans and the parasitic organisms from the expansion estimates and such discussions are now limited to free-living organisms only. Further, as described in response to Comment-1, the revised manuscript focuses on prokaryote versus eukaryote comparison.

Note that phylogenetic analysis often assigns parasitic and symbiotic organisms that have experienced reductive evolution as the earliest diverging clades of their corresponding kingdoms of life. Examples include Nanoarchaeum equitans, an obligate symbiont, assigned as the earliest diverging archaea (Hedges et al., 2015; Huber et al., 2002; Waters et al., 2003), and parasitic Excavate assigned as one of the earliest diverging eukaryotes (Burki et al., 2020; Simpson et al., 2002). In accordance with these studies, these parasitic and symbiotic organisms were included in our analysis. We acknowledged this fact in the Methods section (see Page 22, Lines 9-16).

Comment-4. The authors do make a salient and I think essentially correct observation: chaperones typically comprise about 0.3% of the proteins in any organism. As such, this presents no dichotomy in evolutionary trends to be explained. Surely, as examined and discussed in the paper, eukaryotes also show significant increases in the size and domain content of the encoded proteins, suggesting the possibility that might need more chaperones. However, if this is the explanandum, rather than the number of proteins in the proteome as such, it should be clearly stated. Furthermore, it is quite natural to assume that this increase in protein complexity without a commensurate increase in the chaperone diversity, is enabled by higher expression of the chaperones as suggested in the Discussion of this paper. I doubt there is any big surprise here and even much need for an extended discussion let alone a special publication.

Response

As emphasized, and shown, eukaryotes have not only larger proteomes in terms of the number of proteins or protein size. They have a higher content of proteins that are prone to misfolding. This is shown explicitly, in Figure 2 (namely, multidomain proteins, repeat, beta-rich proteins, etc’) and is reiterated in a summary figure (suggested by Reviewer 1). Further, in response to Reviewer-3’s suggestion, we showed that eukaryotes feature much higher proportions of aggregation-prone proteins per proteome than prokaryotes (Figure 2E).

To further clarify, we revised Figure 4 to quantitatively compare the expansion of proteomes and that of chaperones, under one roof. This Figure compares proteome parameters that supposedly demands more chaperone action in all three domains of life and simultaneously summarizes the expansion of the chaperone machinery lacking de novo innovations.

In addition, the first paragraph of this Discussions section is revised to state that from prokaryotes to eukaryotes, proteomes have expanded by duplication-divergence as well as by innovations (de novo emergence of new folds). Thus, it’s not about the size only (a challenge that a proportion expansion of chaperone genes would resolve, i.e., the 0.3%) but about proteome composition changing in a way that demands more and more chaperone action.

We also agree with the assertion that “it is quite natural to assume that this increase in protein complexity without a commensurate increase in the chaperone diversity, is enabled by higher expression of the chaperones”. However, we belong to a group of scientists for whom natural assumptions are insufficient, and think that supporting evidence is of importance.

Reviewer’s significance statement

As such, in the opinion of this reviewer, there is no substantial advance over the existing knowledge in this paper. Should the authors wish to revise, they would need to develop robust methodology to measure proteome expansion. That would involve starting from reconstructed ancestors rather than any extant forms (let alone parasites). I doubt that such analysis, non-trivial in itself, reveals an strong, consistent trends other than the well known increase in complexity in eukaryotes.

Response

We agree that to assert evolutionary, time-dependent trends one needs to analyze phylogenies and reconstructed ancestors, but still think that a comparison of proteome and chaperone contents along the Tree of Life is meaningful. We thus respectfully, yet adamantly disagree with “no substantial advance over the existing knowledge”. We strongly believe, as does Reviewer-3, that the results and the model presented in this paper are “fascinating to consider and… will stimulate a good deal of important discussion…”.

Reviewer #3

Summary

The manuscript by Rebeaud et al describes phylogenetic analyses of proteome and chaperone complexity. The authors analyzed species across the tree of life to predict the proteome and chaperone properties of ancestors spanning to the last universal common ancestor. Their analyses indicate that many proteome properties increased in complexity over evolutionary time including: average protein length, the number of multi-domain proteins, the size of the proteome, the number of repeat proteins, and the number of beta-superfold proteins that are known to be difficult to fold. Their analyses also indicate an expansion in chaperone families that corresponds to the increase in proteome complexity. Based on their analyses, the authors propose a model where early life relied on a limited number of chaperones (Hsp20 and Hsp60) and that as proteome complexity evolved, so did chaperone complexity. Core chaperones including Hsp90, Hsp70, and Hsp100 evolved relatively early, and later chaperone evolution was driven by the appearance and alterations of co-chaperones and auxiliary factors as well as by increases in the protein abundance of chaperones.

Major concerns

Comment-1. This work is appropriately based on phylogenetic inferences, but as such, the limitations and uncertainties of phylogenetic inferences need to be discussed. This in no way takes away from the work, quite the opposite, it would make it richer by encouraging broader interpretations where justified and clear understanding of where support for the model is strongest. Posterior probabilities need to be discussed and the range of properties that a likely ancestor might have based on the data should be discussed. How this impacts the conclusions and models should be discussed. Throughout the manuscript, the authors present most-likely ancestral models (as I understood it), what are the next most likely models? How much power is there to distinguish one model from another? It would be very helpful to have a section describing the limitations and uncertainties of the phylogenetic analyses and how these relate to the main findings and conclusions.

Response

We thank the reviewer for this suggestion. Reviewer-1 raised a similar suggestion (see Comment-3). The phylogenetic analysis in our paper included dating the emergence of core- and co-chaperone families, and attempt to infer major their HGT events, foremost in relation to the origin of eukaryotic chaperones. To highlight the uncertainties of phylogenetic inferences we re-evaluated our work in the light of a recent study (PMID: 32316034) that carefully analyzed the uncertainties associated with the assignment of several protein families to LUCA.

Ideally, for a protein family to be assigned to LUCA, there must be a single split of bacterial and archaeal domains at the root of the protein tree with strong bootstrap support, and the inter-domain branches would be longer than the intra-domain branches (PMID: 32316034). In the revised main text we discussed that only the HSP60 protein tree satisfies this criterion. HSP20 protein tree depicts a clear single split of bacterial and archaeal domains at the root, albeit with weak bootstrap support, and inter-domain branch lengths are smaller than intra-domain branch-lengths. We discussed that this is indeed the case of phylogenetic uncertainty, which means the sequence of this small, single-domain chaperone lacks the information to make reliable inference at the basal events in the ToL.

In addition, the HGT events discussed in the previous version appear to be indistinguishable from phylogenetic uncertainties and we removed all instances of HGT events mentioned in the main text as well as Figure 3B. Only one HGT event – HSP60 being horizontally transferred from archaea to Firmicute, which is well-supported by the data is kept in the revised main text. We believe these discussions would be very useful to the readers.

Finally, we note that most of our key assignments (points of emergence, and major HGT events) are in agreement with previous works. Specifically: the emergence of HSP20 and HSP60 to LUCA (Sousa et al., 2016; Weiss et al., 2016) and HSP60 being horizontally transferred from archaea to Firmicute (Techtmann and Robb, 2010) and HSP20 being horizontally transferred between bacterial clades and between bacteria and archaea (Kriehuber et al., 2010).

Comment-2. General features that impact foldability, including contact order, should be discussed and what features can be searched for in genomes that relate to these - e.g. beta-rich proteins.

Response

Thanks for this valuable idea! Contact order, and other predictors of problematic folding are highly relevant but their analysis is structure-based and hence inapplicable on the proteome (sequence) scale. We did, hwoever, estimate the proportion of aggregation-prone proteins in the proteome. These proteins were identified by CamSol method that assigns poorly soluble regions from sequence data. Indeed, some of these predicted ‘poorly soluble segments’ refer to the hydrophobic core of the respective folded state instead of ‘true’ aggregation hotspots. With this unavoidable potential caveat, it appears that compared to prokaryotes, aggregation-prone proteins in the proteome have become nearly 6-fold more frequent in Chordates.

Following changes were made to accommodate this new analysis:

Figure 2 is revised to include a new panel (panel-E) that shows the expansion of aggregation-prone proteins in the proteome across the Tree of Life. The same result is summarized in the summary Figure 4.

A new paragraph entitled “Proteins predicted as aggregation-prone became ~6-fold more frequent in the proteome” is added to the Results section, which describes the principle and the main results (see Page 7, Lines 14-28).

The methodology is included in the Methods section, in a paragraph entitled “Predicted proportion of aggregation-prone proteins in the proteome”, see Page 24 Lines 17-27. For each representative organism, the percent of aggregation-prone proteins in proteome data are provided as Data S10.

This analysis is also included in the revised Abstract: “Proteins prone to misfolding and aggregation, such as repeat and beta-rich proteins, proliferated ~600-fold, and accordingly, proteins predicted as aggregation-prone became 6-fold more frequent in mammalian compared to bacterial proteomes.” See Page 2, Lines 7-9.

Comment-3. "Core" chaperones needs to be defined.

Response

Thank you for this suggestion. We restructured Page 3 Lines 19-23 in the Introduction to clearly explain this aspect. The current text is quoted below.

“Chaperones can be broadly divided into core- and co-chaperones. Core-chaperones can function on their own, and include ATPases HSP60, HSP70, HSP100, and HSP90 and the ATP-independent HSP20. The basal protein holding, unfolding, and refolding activities of the core-chaperones are facilitated and modulated by a range of co-chaperones such as J-domain proteins (Caplan, 2003; Duncan et al., 2015; Schopf et al., 2017).”

Minor concerns and thoughts

Comment-4. This manuscript stimulated me to think about the dynamics between chaperone evolution and proteome evolution. The ability to tolerate proteins that need chaperones seems linked to major evolutionary innovations. Once you have these innovations though, you are addicted to the chaperones - and an expansion of the number of sub-optimal proteins. These ideas seem like they would be valuable to include in the discussion of this work. More generally, it would be wonderful to have a discussion of future directions that this work may spark.

Response

This is indeed a fascinating question or set of questions, that we have also become intrigued about following this work, We introduced a short section, though more of an ‘appetizer’ than a detailed discussion, as we know almost nothing about the co-evolution of new proteins and chaperones.

Reviewer’s significance statement

This manuscript provides a fascinating glimpse back in time of a fundamental interplay - between chaperone evolution/addiction and proteome evolution. I am not an expert in phylogenetic analyses so I cannot judge the details of the analyses. As an expert in molecular evolution and chaperones, I found the approach and model fascinating to consider and I believe it will stimulate a good deal of important discussion in these fields. I have one major concern that I feel ought to be addressed in the manuscript and a number of points that I would encourage the authors to consider. I am sure that these can be readily addressed and I look forward to seeing this work published and the further discussion and ideas that it may stimulate.

Response

Thank you!

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Referee #3

Evidence, reproducibility and clarity

The manuscript by Rebeaud et al describes phylogenetic analyses of proteome and chaperone complexity. The authors analyzed species across the tree of life to predict the proteome and chaperone properties of ancestors spanning to the last universal common ancestor. Their analyses indicate that many proteome properties increased in complexity over evolutionary time including: average protein length, the number of multi-domain proteins, the size of the proteome, the number of repeat proteins, and the number of beta-superfold proteins that are known to be difficult to fold. Their analyses also indicate an expansion in chaperone families that corresponds to the increase in proteome complexity. Based on their analyses, the authors propose a model where early life relied on a limited number of chaperones (Hsp20 and Hsp60) and that as proteome complexity evolved, so did chaperone complexity. Core chaperones including Hsp90, Hsp70, and Hsp100 evolved relatively early, and later chaperone evolution was driven by the appearance and alterations of co-chaperones and auxiliary factors as well as by increases in the protein abundance of chaperones.

Major concerns:

1. This work is appropriately based on phylogenetic inferences, but as such, the limitations and uncertainties of phylogenetic inferences need to be discussed. This in no way takes away from the work, quite the opposite, it would make it richer by encouraging broader interpretations where justified and clear understanding of where support for the model is strongest. Posterior probabilities need to be discussed and the range of properties that a likely ancestor might have based on the data should be discussed. How this impacts the conclusions and models should be discussed. Throughout the manuscript, the authors present most-likely ancestral models (as I understood it), what are the next most likely models? How much power is there to distinguish one model from another? It would be very helpful to have a section describing the limitations and uncertainties of the phylogenetic analyses and how these relate to the main findings and conclusions.
2. General features that impact foldability, including contact order, should be discussed and what features can be searched for in genomes that relate to these - e.g. beta-rich proteins.
3. "Core" chaperones needs to be defined.

Minor concerns and thoughts:

1. This manuscript stimulated me to think about the dynamics between chaperone evolution and proteome evolution. The ability to tolerate proteins that need chaperones seems linked to major evolutionary innovations. Once you have these innovations though, you are addicted to the chaperones - and an expansion of the number of sub-optimal proteins. These ideas seem like they would be valuable to include in the discussion of this work. More generally, it would be wonderful to have a discussion of future directions that this work may spark.

Significance

This manuscript provides a fascinating glimpse back in time of a fundamental interplay - between chaperone evolution/addiction and proteome evolution. I am not an expert in phylogenetic analyses so I cannot judge the details of the analyses. As an expert in molecular evolution and chaperones, I found the approach and model fascinating to consider and I believe it will stimulate a good deal of important discussion in these fields. I have one major concern that I feel ought to be addressed in the manuscript and a number of points that I would encourage the authors to consider. I am sure that these can be readily addressed and I look forward to seeing this work published and the further discussion and ideas that it may stimulate.

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Referee #2

Evidence, reproducibility and clarity

Rebeaud and colleagues analyze evolution of chaperones compared to the evolution of whole proteome complexity across the entire tree of life. Their principal conclusions are well captured in the following quote from the Discussion:

"Comparison of the expansion of proteome complexity versus that of core-chaperones presents a dichotomy-a linear expansion of core-chaperones supported an exponential expansion of proteome complexity. We propose that this dichotomy was reconciled by two features that comprise the hallmark of chaperones:the generalist nature of core-chaperones,and their ability to act in a cooperative mode alongside co-chaperones as an integrated network.Indeed, in contrast to core chaperones, there exist a consistent trend of evolutionary expansion of co-chaperones."

The general theme of the evolution of proteome management is of obvious interest. Unfortunately, the entire analysis is shaky and fails to convincingly ascertain the authors' conclusions. There are many issues. Throughout the manuscript, the authors discuss 'expansion' of the proteome in bacteria, archaea and eukaryotes, creating the impression of a consistent evolutionary trend. No such trend actually exists if one considers the means or medians of proteome sizes within each of the three domains of life (there is a transition to greater complexity in eukaryotes). The maximum complexity, certainly, increases with time which can be attributed to the 'drunkard's walk' effect. This hardly qualifies as 'expansion'. The authors further claim a 'linear' expansion of the chaperone set and and 'exponential' expansion of the total proteome size. These are precise mathematical terms and, as such, require fitting to the respective functions. No such thing in this manuscript. Even apart from that shortcoming, the explanation of both 'linear' and 'exponential' are quite confusing. Thus, when explaining the 'linearity' of chaperone evolution, the authors refer to the lack of major innovation among the chaperones. This is correct in itself but has nothing to do with linearity. Apart from the aforementioned conceptual problems, the estimation of the 'exponential' growth of the proteome are naive, inconsistent and inaccurate. As the base point for the expansion estimates for archaea and eukaryotes, the authors take parasitic forms. Even leaving aside the highly dubious claims that these organisms belong to the clades that diverged first from the respective ancestors, parasites are not an appropriate choice for such estimates because they certainly are products of reductive evolution. For bacteria, inconsistently, the authors choose a free-living form from a dubious ancient clade, and not even the one with the smallest genome. All taken together, this robs the expansion estimates of any substantial meaning.

The authors do make a salient and I think essentially correct observation: chaperones typically comprise about 0.3% of the proteins in any organism. As such, this presents no dichotomy in evolutionary trends to be explained. Surely, as examined and discussed in the paper, eukaryotes also show significant increases in the size and domain content of the encoded proteins, suggesting the possibility that might need more chaperones. However, if this is the explanandum, rather than the number of proteins in the proteome as such, it should be clearly stated. Furthermore, it is quite natural to assume that this increase in protein complexity without a commensurate increase in the chaperone diversity, is enabled by higher expression of the chaperones as suggested in the Discussion of this paper. I doubt there is any big surprise here and even much need for an extended discussion let alone a special publication.

Significance

As such, in the opinion of this reviewer, there is no substantial advance over the existing knowledge in this paper. Should the authors wish to revise, they would need to develop robust methodology to measure proteome expansion. That would involve starting from reconstructed ancestors rather than any extant forms (let alone parasites). I doubt that such analysis, non-trivial in itself, reveals an strong, consistent trends other than the well known increase in complexity in eukaryotes.

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Referee #1

Evidence, reproducibility and clarity

Summary:

The authors present well written work on the evolution of proteome size and complexity, and the corresponding changes in chaperone proteins. Interestingly, they find chaperone copy numbers increase linearly with proteome size, despite the increasing 'complexity' of, in particular, post-LECA genomes. They suggest that to address the rise in complexity, organisms express chaperones at higher levels and an expanding network of co-chaperones has evolved across the tree of life.

Major comments:

-Summary reads strangely relative to the rest of the manuscript, and lists facts in a way that makes the purpose of the study confusing. I think most readers will dislike the characterisation of evolution as a progress from simple to complex, and the authors' might want to avoid this language throughout the manuscript- bacteria and archaea have also been evolving over this period of times, and have not become more 'complex'? Similarly the authors should reconsider their figure legend titles. As a specific example,'in the course of evolution' should become 'across the tree of life' .

-I think the manuscript would be improved if the authors significantly shortened the discussion of genome size evolution- this is fairly well understood, and could be covered briefly, especially as the main focus of the manuscript is on the evolution of chaperone and co-chaperone repertoire. They could also make clearer quantitative links between protein complexity and the evolution of chaperones and co-chaperones- perhaps this should be in the discussion? The authors might also consider referencing 'The evolution of genome complexity', which could be relevant to this manuscript and might make the work of broader interest.

-The authors state 'protein trees were generated and compared with ToL to account for gene loss and transfer events'. The methodology for this procedure is not given in the manuscript. The authors should back up this point, and make it clear this is why they reconstruct the trees. Currently it is not convincing to me that the authors have found HGT given the considerable phylogenetic uncertainty in the basal events in the tree of life. I also expect the tree of a single protein to be potentially lack information due to the short sequence considered and possible lack of power. The authors need to consider whether the data is really of high enough quality to assess this.

-Methods- the authors could consider taking an alternative source of LUCA proteins, rather than those found in 'Nanoarchaeota and Aquificae':it's possible these are not representative of LUCA, and it seems a somewhat arbitrary choice- the authors could consider using one of the available curated sets, such as that generated by Ranea et al. (2006)

-The patterns observed might only hold because of differences in the taxa that diverged pre and post LECA? The authors might consider subgroup analyses to ensure this is not the case. The authors could also consider using methods that take phylogeny into account.

Minor comments:

'Life's habitability has also expanded from its 10 specific niche of emergence-likely deep-sea hydrothermal vents, to highly variable and extreme 11 ranges of temperature, pressure, exposure to high UV-light, dehydration and free oxygen.' This is not really correct, as bacteria and archaea are found worldwide, and in the most extreme environments.

' We reconciled the topology of our tree'- on first read this was not clear, I did not realise the authors were only building trees for subsets of the data- time tree is the best source for the overall topology. The phrase 'manually curated and adjusted' is used in the methods. This language is much too vague, and not a clear explanation of the steps taken.

Significance

The work presents interesting results that suggest that more 'complex' organisms have evolved a strategy to cope with increasing proteome size, and is interesting to researchers in the field of molecular evolution.

I am a researcher in population genetics and molecular evolution.

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Referee #3

Evidence, reproducibility and clarity

This study outlines calcium probes for assessing the poorly understood role of peroxisomes in calcium signaling. The authors suggest that these organelles sequester calcium from either calcium influx across the plasma membrane or from release from the ER/SR. This is important since we need to know more about the roles of these organelles in calcium homeostasis and signaling. However, it needs to be robustly demonstrated that the probes are targeted to the right organelle without confounding contamination from other organelles which can be very significant even for a small degree of mis-targeting.

Major

1. The difference between the signals seen between the peroxisome and cytosolic D3 versions are not compelling, other than a dampened spike with the former (higher resting levels, smaller peak). See below for pH concerns.
2. How clean is the peroxisome distribution? Prove that D3 spillover from its being partially in (or on) other compartments (e.g. cyto, ER) is not contributing to the changes. Selective manipulation of Ca2+ in these other compartments should not affect the peroxisome signal.
   • a. For example, the small changes in the D3-px could be explained by peroxisome not changing at all but rather the other compartments (where larger responses are observed) signal(s) contaminating the response.
     • b. e.g. if in the ER lumen, the signal should be eliminated with SERCA inhibitors (thapsigargin, CPA). They used Thapsigargin in cardiac myocytes, why not in HeLa during characterization)?
3. Any Ca2+ reporter will pH-sensitive to an extent, even D3 (Ca2+ binding, inherent fluorescent proteins).
   • a. It is essential to prove that the signal changes are not due changes perox pH. Target pH-sensitive proteins to the perox lumen by the same strategy and show that the same Ca2+ interventions do not cause pH changes.
   • b. The authors claim different resting levels of [Ca2+] in cytosol/mitochondria/peroxisome. The resting FRET level also depends on the resting pH of the compartments which may also be different. Certainly, mitochondria are more alkaline than the cytosol. Again, to interpret these are real Ca2+ differences requires the pH to be accounted for.
4. I am puzzled by the model, in particular in view of Fig 3. The genetically-encoded calcium indicator (GECI) is allegedly in on the cytosolic face of the peroxisome and measuring peri-peroxisomal Ca2+.
   • a. The changes with this reporter look pretty similar to the luminal reporter (save that the resting ratio may be lower). I don't understand how the lumen [Ca2+] > cytosolic [Ca2+] without a higher local [Ca2+] (unless there is an energy-driven uptake mechanism, but then how does this fit in with ER-driven Ca2+ release?).
5. The claim that resting peroxisome [Ca2+] is higher than cytosol is questionable. Is this a calibration artifact (e.g. compartment pH-differences or the reporter behaves differently in the lumen)? Such a gradient could not be sustained without energy-dependent Ca2+ uptake. The authors make no discussion of this.

Minor

1. Quantitate localization. Pearson's coefficients for GECIs and Peroxisomes.
2. Different upstroke rates of D3 with His vs Cao. Quantify.
3. Page 5. Line 161. 'Different sites', do the authors mean different sides? Similarly, the Legend of Fig 3.

Significance

Good peroxisome calcium probes is important to the genral calcium signaling field. This is fundamental science of interst to all cell biologists.

There has been little published on peroxisome calcium, although for example, the Pozzan lab published a paper in JBC in 2008 on a GFP-based lumenally targeted peroxisome probe. There is contradictory data in the field and reliable new approaches are needed.

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Referee #2

Evidence, reproducibility and clarity

The manuscript by Sargsyan et al describes an unappreciated role for peroxisomes in Calcium dynamics. Specifically, the authors propose that GPCR/VDCC/SOCE-mediated cytosolic Ca2+ elevation is rapidly sensed by peroxisomes and sequestered. The authors used/generated a peroxisome-targeted genetically encoded Ca2+ indicators which is elegant and powerful tool to monitor the luminal Ca2+ dynamics. While the results and conclusions are novel, there are some important gaps that need to be addressed for consideration for publication in EMBO J.

Comments:

Peroxisomes are single membrane bound organelles which are conserved across species spanning from yeast to humans. While housing only -100 proteins, they are responsible for essential steps in lipid metabolism, amino acid metabolism and ROS homeostasis. Unlike other organelles, peroxisomes import fully folded and cofactor-bound proteins into their matrix. Though peroxisomes house specific metabolic functions, there is extensive crosstalk with other organelles, including mitochondria. It is essential to test and define whether silencing/knockdown of mitochondrial Ca2+ transport components like MCU will impact peroxisome Ca2+ uptake upon stimulation with histamine or electrical stimulation.

Since peroxisomes buffer significant amount of Ca2+, it is worth testing whether blockade of mitochondrial Ca2+ uptake would not alter peroxisome mediated Ca2+ influx. This analysis will provide Ca2+ uptake rate of mitochondria vs peroxisomes (mallilankaraman K. et al CELL 2012 and Nemani N. et al Science Signaling 2020).

Peroxisomal synthesis of plasmalogens is Ca2+ and oxygen tension dependent, it is essential to show that altering Ca2+ controls plasmalogen synthesis.

In the introduction authors have stated that "Elevated mitochondrial uptake increases 39 mitochondrial reactive oxygen species (ROS) production and is associated with heart falure and ischemic 40 brain injury (Starkov et al., 2004; Santulli et al., 2015)." These cited articles remotely links MCU and ROS elevation. It is important to point out that Tomar et al 2016 Cell Reports clearly demonstrated that genetic ablation of MCU suppresses mROS production that is mitochondrial Ca2+ dependent.

Significance

The significance of the work is very high. The authors employ a variety of complementary techniques and experimental systems to demonstrate that peroxisomes indeed buffer a large quantity of Ca2+ upon stimulation.

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Referee #1

Evidence, reproducibility and clarity

These are straight forward studies aimed to develop probes to asses peroxisomal Ca2+ in rest and in response to receptor stimulation. The probes were designed to measure intraperoxisomal Ca2+ and the Ca2+ the peroxisome experience when cytoplasmic Ca2+ is increased. The pobes fill a need in understanding peroxisomal Ca2+ and Ca2+ signaling in general and should be very useful to investigators in the field.

The comments are aimed to help in improving the studies and taking them to the next stage.

The grammar needs improvement and the introduction needs sharpening. It is long and, in many places, not to the point. The results and discussion sections are also quite verbose.

The sidedness of the probes need to be validated further, especially since the peroxisomal Ca2+ increase follows the cytoplasmic and the slower reduction rate may results from the environment experienced by the probe. Simple experiments: how the probes respond to Ca2+ ionophore; does Ca2+ reduced rapidly when removed from the media of the digitonin permeabilized cells; how the cytoplasmic and peroxisomal thapsigargin responses compare using the protocols in 2A and 4A? Sidedness of PEX13-D3cpV was not examined.

Calculation of peroxisomal Ca2+ are based on Kd reported in the literature. The Kds of D3cpV-px and PEX13-D3cpV should be determined when in the peroxisome in permeabilized cells for the numbers to have any meaning.

How the localization of the probes look in the differentiated cardiomyocytes? How it compares to RyRs, VACC, etc..

The major weakness of the study is that the probes are used only as a tool. The enhance the study and bring it beyond an excellent technical achievement, the authors should use them to study a significant Ca2+-dependent peroxisomal function and show how the use of the tools eliminate the role of Ca2+ in such a function.

Significance

These are straight forward studies aimed to develop probes to asses peroxisomal Ca2+ in rest and in response to receptor stimulation. The probes were designed to measure intraperoxisomal Ca2+ and the Ca2+ the peroxisome experience when cytoplasmic Ca2+ is increased. The pobes fill a need in understanding peroxisomal Ca2+ and Ca2+ signaling in general and should be very useful to investigators in the field.

The major weakness of the study is that the probes are used only as a tool. The enhance the study and bring it beyond an excellent technical achievement, the authors should use them to study a significant Ca2+-dependent peroxisomal function and show how the use of the tools eliminate the role of Ca2+ in such a function.

Reviewer #2:

In 2011 these authors showed that Drosophila DmPI31 is a binding partner of the F box protein Nutcracker, a component of an SCF ubiquitin ligase (E3) required for caspase activation during sperm differentiation in Drosophila. DmPI31 binds Nutcracker via a mechanism that is also used by mammalian FBXO7 and PI31. Subsequently, they have shown that PI31 serves as an adaptor to couple proteasomes with dynein light chains and inactivation of PI31 inhibited proteasome motility in axons and disrupted synaptic proteostasis, structure, and function. In addition, conditional loss of PI31 in spinal motor neurons (MNs) and cerebellar Purkinje cells (PCs) caused axon degeneration, neuronal loss, and progressive spinal and cerebellar neurological dysfunction.

Here the authors show that like Fbxo7 mutant mice, PI31 conditional KO mice have a decreased testis and thymus size and motor neuron specific loss of either FBXO7 or PI31 produced similar phenotypes in motor neurons. They generated a mouse that conditionally expressed FLAG-tagged PI31 this could rescue PI31 mutant mice; this transgene (under a Chat driver) rescued the phenotype of FBXO7 mutant mice from which they concluded that the consequences of FBXO7 mutation relate to loss of PI31 function in the cell types studied.

FBXO7 is the substrate recognition module of a novel proteasome‐interacting E3 ubiquitin ligase. In addition to binding PI31, FBXO7 also drives PI31 ubiquitylation and thus regulates its cellular levels. That the transgene can rescue the phenotype in the Chat-expressing cells is surprising and striking. However, it would necessary to reveal more about the underlying molecular mechanism. In the cell types rescued, is there another E3 ligase with overlapping substrate specificity? Are there mitochondrial phenotypes that are not rescued?

Reviewer #1:

This manuscript focuses on the role played by the PI31 protein in regulating presynaptic proteasome abundance and the health of motor neurons. In particular, it presents striking data from knockout and conditional KO mice showing that depletion of PI31 and Fbxo7/PARK15 (Parknson's disease gene) yield similar phenotypes, including motor neuron defects, following their conditional depletion. Furthermore, in the absence of Fbxo7/PARK15, PI31 levels were greatly reduced. This suggested that a major role for Fbxo7 is to promote the abundance/stability of PI31. In support of this model, transgenic expression of PI31 completely rescued overall health, body weight and motor neuron morphology in Fbxo7 mutant mice. These results are impressive. However, the manuscript implies but does not show that the mechanism through which PI31 supports neuronal health is by promoting the axonal transport of proteasomes and thus suppressing the presynaptic accumulation of ubiquitinated proteins. Several key experiments to address this issue would greatly strengthen the manuscript (outlined below).

1) Major statements are made about the importance of PI31 for axonal transport of proteasomes and presynaptic aggregate clearance. In order to establish that PI31 is indeed supporting neuronal health by promoting axonal transport of proteasomes and clearing presynaptic protein aggregates, it is necessary to show:

-- That motor neuron presynaptic proteasome number is reduced in the PI31 and Fbxo7 KO mice and restored in the Fbxo7 mutant mice that express the PI31 transgene.

-- That expression of the PI31 transgene in the Fbxo7 mutant mice suppresses the presynaptic accumulation of P62 aggregates.

2) It would be helpful if the abstract defined the Parkinson's disease model (PARK15) that was investigated.

3) Quantification of the presynaptic P62 aggregate phenotype in figure 2 would be helpful as would including a higher magnification image of the wildtype synapse with the P62 labeling.

4) Given that the major phenotypes that are characterized are not directly related to Parkinson's disease, the upfront emphasis on Parkinson's disease might not be warranted. Although the mouse phenotypes that are reported are striking, the title in particular suggests a more direct connection to this disease than is warranted by the data.

5) Figures 3C and 4B: Individual data points should be plotted and a statistical test would be helpful.

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:

There is great interest in understanding the molecular basis of FBXO7/PARK15 pathogenesis and the present, high quality story includes an impressive rescue in cells transgenically overexpressing PI31 protein. Nevertheless, as discussed in greater detail below, the two reviewers felt that more work would be needed to document the molecular basis for this phenotype rescue.

Reviewer #3:

Summary

The manuscript presents an experiment in which participants listened to ten auditory sequences, generated with either first- or second-order statistical structure ("simple" vs "complex" SL respectively) and predicted 20 elements in each sequence during simultaneous EEG recording. Behavioural results showed that all participants performed better for simple than complex sequences and musicians performed better than non-musicians for both sequence types. A Bayesian model was developed with parameters controlling memory decay, sensory noise, model order (hierarchy) and selection noise, which were fitted to the responses of each participant. The results showed differences between musicians and non-musicians for parameters related to SL (model order, selection noise) but not parameters related to stimulus processing (sensory noise and memory decay). Specifically musicians showed evidence of higher-order prediction and lower selection noise. The EEG results linked increased amplitude at fronto-central electrodes at around 300 ms to modelled surprise for each participant, which was stronger for musicians than non-musicians. Separate analyses for models of different order produced evidence for an early modulation around 200ms for zeroth-order predictions which did not differ between musicians and non-musicians and a later modulation around 300ms for first- and second-order predictions which did differ between the two groups. These modulations were linked to the MMN and P300 respectively. The results are taken as evidence for better SL in musicians and discussed in terms of the Bayesian brain hypothesis.

Substantive Concerns

-- p. 4, para. 2: I believe that the evidence for musicians showing better SL is less strong than presented in the manuscript. In particular, using different stimuli and methods, both Loui et al., (2010) and Rohrmeier et al. (2011) found no difference between musicians and non-musicians in statistical learning of auditory sequences. Furthermore, with regard to reference 7 in the manuscript, although some studies have found larger ERAN amplitudes in musicians than non-musicians (Jentschke & Koelsch, 2009; Kim et al., 2011; Koelsch et al., 2007, 2002; Regnault et al., 2001) the differences are usually small and have not been replicated in all studies (e.g., Koelsch & Jentschke, 2008; Koelsch & Sammler, 2008; Miranda & Ullman, 2007; Steinbeis et al., 2006). The introduction and motivation for the experiment should be adapted to give a more detailed and balanced view of the literature and the divergence between the present results and those of Loui et al., (2010) and Rohrmeier et al., (2011) should be discussed and accounted for.

-- I'm not sure complexity is the most appropriate term to use in distinguishing statistical regularities of different order, since different transition tables at a single given order could be described as varying in statistical complexity. Having introduced the term, why not stick to "higher-order" and "lower-order"?

-- p 7: "Control analysis revealed that musicians and non-musicians do not benefit from an overall increase in performances during the course of the experiment." But there should be an improvement during each individual sequence, right? Is it possible to demonstrate this?

-- I think the authors should analyse the interaction in Fig. 1B and report whether or not it is significant.

-- I noted that while the authors report the consistency between the model and participants, they do not report the average accuracy of the model, which should be included for completeness. It would be good to report both of these analyses separately for complex and simple sequences, given the significant difference in performance between them.

-- p. 15: clarify that the same transition matrix was used for all five sequences of a given order

-- p. 15: what were the inclusion/exclusion criteria for the groups of musicians and non-musicians? How were participants recruited? This is important, especially given the divergence between the present findings and previous results (as noted above).

-- p. 16: are there any consequences of the fact that participants were aware of the probabilistic nature of the sequences and the differences between the two sequence types? Again, this seems to me to be an important divergence from other SL studies which could impact on the behavioural and neural effects observed and should, therefore, be discussed.

-- p. 16: "one participant was removed" - musician or non-musician?

-- p. 18 why was FCz used as the reference?

-- there are some inconsistencies in the way the model parameters are named - e.g., "late noise" in Supp. Figure 5. Please check through and use consistent terms throughout.

-- To facilitate replication and follow-up research, I would encourage the authors to make their data and model openly available.

Reviewer #2:

The paper compares musicians' behavior and ERP responses to those of non-musicians with the following statement in the abstract:

"these better performances could be due to an improved ability to process sensory information, as opposed to an improved ability to learn sequence statistics. Unfortunately, these very different explanations make similar predictions on the performances averaged over multiple trials. To solve this controversy, we developed a Bayesian model and recorded electroencephalography (EEG) to study trial-by-trial responses."

The authors claim:

"This higher performance is explained in the Bayesian model by parameters governing SL, as opposed to parameters governing sensory information processing. " This is correct - but meaningless - the experiment does not challenge sensory noise since the 3 sounds used are so distinct that sensory noise is zero in the two groups. Given that basic design - this phrasing is not only too strong, it is in proper.

My understanding is that are two actual observations in the paper:

1) Musicians' learning of second order markov statistics is better than that of non-musicians based on parameter fitting of a Bayesian model of their behavior in answering explicit questions regarding which sound (of 3 very distinct options) should come next.

2) ERP measures - specifically P300 of musicians, is more sensitive to this statistics as evident by its magnitude with respect to predictability/surprise of the sound based on serial statistics. These claims are interesting BUT - I am not convinced by the claim of specificity. I think the data (and previous studies) suggest that musicians do better with sound related judgments - with all respects.

I am not convinced that the model adds information since it explains the data as a good as single accuracy numbers (or did I miss something?). So I am not convinced that this trial by trial analysis adds information.

With respect to the specific model parameters:

Sensory noise is zero - the sounds are quite distinct. This is not an observation - this is how the experiment was designed. The authors admit that (indeed - any study that focused on sensory discrimination found an advantage in musicians) - but then state specificity, particularly in the abstract.

Regarding rate of decay - I wonder if this is relevant to overall performance when asked only up to 2nd order serial statistics. It may be sufficient for the task. The relevance of this parameter should be clarified.

Thus the lack of group difference in these parameters probably tells about the experiment rather than the groups.

Similarly, musicians' ERP responses are larger. But the early difference is not addressed at all. Is the earlier response sensitive to simpler stat - but in a similar way in both populations? Can't be - since they have a different magnitude. The authors base their analysis on (MEG analysis) in their 2019 paper. I tried to do the exact comparison, and wasn't sure about the mapping to components - please clarify the exact similarity.

Thus - overall - I am not sure that the model analysis provides new conceptual insights.

Reviewer #1:

In this work, the authors used a combination of modelling, behavioral methods and EEG to understand whether sensitivity to the statistical structure of unfolding sound sequences differs between musician and non-musicians. Overall they demonstrate that musicians are better than non musicians at predicting forthcoming items. Modelling suggests that this advantage arises because they estimate higher order transition probabilities than non-musicians. The analysis of EEG data recorded during task performance showed that the amplitude of the P3 correlated with item predictability. Further analyses suggested that musicians and non-musicians have similar responses to surprise in simple sequences, with divergence between the groups occurring for higher order transition probabilities.

I have several concerns about task design, analysis and interpretation of the data which are detailed below:

1) The EEG data are recorded whilst participants are performing the behavioral prediction task. Though probe trials occurred rarely, it is conceivable that participants were making an active judgement for each sequence item. There is therefore a concern that the measured EEG data would reflect this aspect (active task performance) rather than automatic SL. This makes conclusions about "neural statistical learning" (e.g. as in the title) difficult to make.

2) In the results section the authors consider various differences between the musician and non-musician groups that could lead to differences in performance. One aspect that does not seem to be considered is that of attention, or task engagement. Is it possible that the musician participants were simply more engaged/less bored by the task? The EEG data (figure 3) are consistent with this interpretation showing overall substantially larger responses in the musicians relative to the non musicians.

3) Relatedly, is it possible that the results in Figure 3C are at least partly related to the overall amplitude differences between groups? Higher SNR in the musician group may lead to higher beta values. One way around this is to normalize the data (e.g. based on the P1 response) before computing the correlations.

4) Figure 4: can you show the ERP data on which the beta values are based?

5) Figure 4: the authors seek to conclude that the two groups have similar responses to surprise in simple statistical contexts (K=0) with divergence occurring for more complex statistical structure. However, they do not provide statistics to support this claim. It is not enough to show no significant difference between groups for K=0, but significant differences for K=1, 2 : you need to demonstrate an interaction.

6) More broadly, though, I do not understand the theoretical implications for this finding: why would brain response to K=0 occur earlier than k=2? Shouldn't the prediction be formed already before sound onset (especially given the relatively slow sequence rate).

7) Discussion: "Our results shed light on the musical training induced plasticity". This statement confuses correlation with causation. The authors discuss the reservation later in the discussion but it should be removed altogether.

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 work constitutes an innovative and timely combination of modelling, behaviour and EEG to understand potential differences in SL abilities between musicians and non-musicians. However, as detailed below, we have many concerns regarding the modelling, experimental design and interpretation of the results.

Our major concerns are summarized here (and further elaborated in the individual reviews below):

1) Modelling: please report the accuracy of the model and whether this differs between groups.

2) You should analyse the interaction in Fig. 1B and report whether or not it is significant.

3) Relatedly, there appears to be an inconsistency between the behavioural results and the modelling. In the behavioural data you report a main effects of musicianship and of sequence complexity. Modelling of this data suggests that whilst the K for musicians is higher than non musicians it is substantially above 1 for both. If anything this should predict larger differences between groups in larger K than smaller K which is different from what is seen behaviourally. A similar inconsistency is present between the behavioural results and the results in figure 4 (see below). This requires careful consideration.

4) Can you do more to convince the reader that the model is performing well? Is the fit good, how does it vary across participants? Does rate of memory decay affect performance at all? Can you show good versus poor performers within the same group - do parameters also vary there?

5) It is important that you address the issues related to participants being aware of the stimulus construction. Are there any consequences of the fact that participants were aware of the probabilistic nature of the sequences and the differences between the two sequence types? This seems to be an important divergence from other SL studies which could impact on the behavioural and neural effects observed and should, therefore, be discussed.

6) The EEG data are recorded whilst participants are performing the behavioural prediction task. Though probe trials occurred rarely, it is conceivable that participants were making an active judgement for each sequence item. There is therefore a concern that the measured EEG data would reflect this aspect (active task performance) rather than automatic SL. This makes conclusions about "neural statistical learning" (e.g. as in the title) difficult to make.

7) In the results section the authors consider various differences between the musician and non-musician groups that could lead to differences in performance. One aspect that does not seem to be considered is that of attention, or task engagement. Is it possible that the musician participants were simply more engaged/less bored by the task? The EEG data (figure 3) are consistent with this interpretation showing overall substantially larger responses in the musicians relative to the non musicians.

8) In general, we think the model has been constructed with due care and attention and we like the separation of parameters related to statistical learning (model order and selection noise) and more general aspects of perception and cognition (sensory noise and memory decay). We think the difficulties arise in the relationship between the model and the experiment. Specifically, the sensory noise model parameter reveals very little in the analysis of this data because the sounds were so readily distinguishable, which appears to have been a deliberate choice in the experimental design, somewhat confusingly. The present stimulus set is therefore not suitable for distinguishing differences in sensory processing vs. SL between groups. We suggest that the authors could simply remove this parameter from the analysis and the paper would be clearer as a result. This would involve re-modelling and you will also have to reshape the way the experiment is motivated.

9) We have some questions about how the EEG data are analysed. In particular, the large amplitude difference between groups should be quantified, discussed and interpreted. We would also like to see stronger justification and discussion of why these differences are not affecting the main conclusions. We note that the authors provide R2 results in supp materials but we feel that a better approach may involve normalizing the responses before modelling. Higher SNR in the musician group may lead to stronger correlations. One way around this is to normalize the data (e.g. based on the P1 response) before computing the correlations.

10) You should perform the appropriate statistical analysis to support the claims associated with Figure 4. You seek to conclude that the two groups have similar responses to surprise in simple statistical contexts (K=0) with divergence occurring for more complex statistical structure. However, you do not provide statistics to support this claim. It is not enough to show no significant difference between groups for K=0, but significant differences for K=1, 2. You need to demonstrate an interaction between group and model order. Additionally, it was also not quite clear how modelling was performed here. We understand that you take surprise values from the model fitted to each participant but with the order fixed at 0, 1 or 2. This may mean that the other parameters might no longer be optimal in the context of the new fixed K values, depending on how different these were from the fitted values for each participant, which might plausibly differ for the musicians and non-musicians. To address this, Can you supplement the existing analysis with an analysis in which the K parameters are fixed at 0, 1 and 2, and the other parameters are re-optimised in the context of these fixed parameter values. Please also provide information about how well each individual data were fit, and whether there was a significant difference between musicians and non musicians. In general, we think the authors should present the result in figure 4 more cautiously and also flesh out the interpretation in more detail in relation to the literature along with a consideration of other potential interpretations. A small related point is that the term hierarchy is strongly related to this interpretation and we would prefer a more neutral term such as 'model order'.

11) The paper would benefit from a careful discussion of exactly what information, on top of that revealed with behaviour, is added by EEG and the significance of this in the context of the existing literature on expectation related ERP components.

Reviewer #3:

In this manuscript, Ramachandran and colleagues describe how cholecystokinin-related NLP-12 neuropeptide signalling in C. elegans can regulate two different behavioural programmes, area-restricted search (ARS) and basal locomotion, by conditionally engaging different specific receptors that are expressed in different neuronal targets. They thoroughly characterise the CKR-1 receptor which had not been described previously, and place its function in context with that of the previously known NLP-12 receptor CKR-2. The manuscript gives new insight into an interesting and likely conserved mechanisms of how neuromodulatory systems enable adaptive behaviour by coordinating the action of neural circuits even when they are not directly connected. The conclusions drawn appear solid and are justified by the data presented, and the experimental approaches and results are well documented.

The main problem with the work is a certain lack of clarity regarding the separation of the roles of the CKR-1 and CKR-2 receptors on basal locomotion/body bending and head bending/reorientations. Overexpression of NLP-12 places animals in a chronic ARS state, as described in a previous publication. Is the NLP-12 overexpression model representative of the increased reorientation in area restricted search, or of control of undulations in basal locomotion, or both? If it is primarily representative of area restricted search, this would mean that CKR-2, similarly to CKR-1, mediates the chronic ARS state induced by NLP-12 overexpression, because in fig. 1B and C its mutation causes a reduction in the phenotype, and deletion of both ckr-1 and ckr-2 causes a stronger reduction.

Also, it is unconvincing that SMD neurons do not express ckr-2 (see S3D); no comparison of ckr-1 and ckr-2 expression levels in SMD is provided and in fact the CeNGEN data of single cell RNAseq of C. elegans neurons shows similar expression of both receptors in SMDD (accessible at cengen.shinyapps.io/SCeNGEA). On the other hand, loss of ckr-2 on its own does not cause a significant reduction in ARS (fig 3A). To clarify this, the authors could measure the reorientation rate in the nlp-12OE ckr-2 mutant strain.

Given that ckr-1 overexpression as shown in figs 4-6 increases both body bending amplitude (and ARS-like high reorientation rate, the authors offer the interesting possibility that SMD may also affect basal locomotion. I would suggest an experiment that clarifies whether SMD also controls body bending in basal locomotion using the single-worm tracking assay shown in fig 2A with the SMD-specific ckr-1 rescue strains in a ckr-1 mutant background (as used in figure 7). Also they could measure body bending in the existing data on the SMD::Chrimson optogenetics.

Reviewer #2:

Ramachandran et al. report the discovery of a C. elegans GPCR - CKR-1 - that mediates some of the effects of the cholecystokinin-like neuropeptide NLP-12 on posture and foraging behavior. The discovery of this receptor permits further study of this neuropeptide signaling system, which is conserved from worms to vertebrates. Although CKR-1 is expressed in many neurons, the authors show that its function in SMD head-motorneurons is especially important for control of posture and foraging. The manuscript's strengths include: (1) rigorous characterization of receptor-ligand interactions in vitro, using a cell-based assay for GPCR activation, and in vivo, using genetic analysis, (2) compelling data in support of a model in which NLP-12 regulates SMD neurons to control foraging, (3) high-resolution analysis of C. elegans posture during foraging, which illustrates the complexity and richness of this behavior, and (4) the circuit model, i.e. a role for SMDs, is tested using a number of independent methods and clearly indicated.

The manuscript does have some weaknesses. In addition to specific technical points listed below, the manuscript discussed neuropeptides derived from a single source, the DVA pre-motor neuron, acting on distinct targets via distinct receptors in a conditional manner. This interesting model is suggested by the title and the abstract and comes up plainly in the introduction and discussion. However, the model is not clearly supported by the data, which primarily focus on the characterization of CKR-1 as a relevant receptor for NLP-12 peptides. Another weakness in the manuscript arises from the authors' switching between various assays for posture during locomotion, which makes it difficult for the reader to compare data between figures. Rich kymography data are relegated to supplementary figures, and data from only a subset of relevant genotypes are shown as kymographs. The manuscript would be strengthened by more uniform analysis of posture and foraging. Finally, while the data clearly show that effects of NLP-12 on posture and foraging require SMD neurons, the manuscript does not investigate how NLP-12 affects SMD activity. The manuscript would be strengthened by experiments showing a functional connection between DVA and SMD neurons, e.g. functional imaging of SMDs during optogenetic manipulation of DVAs.

Specific comments:

1) One premise of the work is that DVA neurons are the sole source in vivo of NLP-12 peptides. A recent study (Tao et al. 2019, Dev. Cell) shows that there is an alternate source of NLP-12, the PVD nociceptors. The authors should address the possibility that their assays also detect a contribution of PVD neurons to posture/foraging.

2) The text associated with Figure 1B-C is tentative with respect to assigning redundant functions to CKR-1 and CKR-2. Why? The data are clear; these receptors function redundantly.

3) The very nice in vitro analysis of NLP-12 receptors should include negative controls. Ideally, the authors would use a scrambled neuropeptide or a related neuropeptide to demonstrate specificity of the interactions between NLP-12 and CKR-1/2.

4) The different 'bending angles' used in Figures 1 and 2 make it difficult to compare data between figures. Also, the schematics used to explain the bending angles have small fonts and are hard to read.

5) Figure 3E shows the results of a nice experiment in which optogenetic activation of NLP-12-expressing cells - presumably DVA - causes reorientations. The authors assert that this effect requires CKR-1 but not CKR-2. The data, however, suggest that CKR-2 might have an effect. The variance of the data does not allow the authors to reject a null hypothesis, but they err in then assuming that this means that CKR-2 plays no role in the phenomenon. This experiment should be repeated to determine whether there is indeed a specific or privileged role for CKR-1 in mediating NLP-12-dependent reorientations.

6) Also, Figure 3E should show raw data - don't show proportional changes - and all Figure 3 should be scatter plots allowing the reader to assess the variance of the data.

7) The authors show that effects of receptor overexpression are suppressed by loss of NLP-12 peptides. Is there precedent for this kind of genetic interaction in the literature?

8) Also, the authors assert that suppression of effects of CKR-1 overexpression by loss of NLP-12 shows that NLP-12 peptides are the sole ligands for this receptor (page 9, line 17). It is not clear why the authors reach this conclusion.

9) There are some very nice data that are assigned to supplementary figures but might be better placed in main figures. Fig. S3A-B shows data that are integral to the authors' model and could be presented in a main figure. Also, the localization of NLP-12::Venus in DVA axons near SMD processes would be appropriate to show in a main figure. It would be ideal to mark SMDs with a red fluor so that NLP-12::Venus colocalization with SMD processes could be assessed.

10) The kymography data are nice but incomplete. The authors should show kymographs from strains of all relevant genotypes. This would include: (1) ckr-1(oe); nlp-12, (2) nlp-12, ckr-1, and ckr-2 single mutants, and (3) ckr-1; ckr-2 double mutants.

11) Page 12, last paragraph indicates that 'low levels' of expression rescue ckr-1 phenotype - how has the expression level been determined? I guess that the authors refer to the amount of DNA used for transgenesis, not a direct measure of transgene expression - this should be reworded.

12) The manuscript would be strengthened by experiments that measured the effect of DVA activation on SMD physiology and what contribution NLP-12 signaling makes to any functional connection between these neurons. One potential impact of this work is that it establishes a nice paradigm for new molecular genetic analyses of neuropeptide signaling. Direct observation of the effects of NLP-12 peptides on SMD neuron physiology would further strengthen the authors' conclusions and suggest mechanisms by which CKR-1 regulates cell physiology.

13) Minor comment: Fig S1C is a little confusing w/ respect to how the ligand is indicated - it implies that there exists a ligand-binding site at the amino terminus of the receptors.

Reviewer #1:

In this manuscript Ramachandran et al. provide a C. elegans behavioral genetics study focused on the worm cholecystokinin-like neuropeptide-receptor system. They show that nlp-12 neuropeptides released from the DVA neuron fulfill a dual role in controlling body posture as well as head-bending mediated area restricted search (ARS). Previous work showed that DVA controls body posture via nlp-12 signaling to ckr-2 receptor in ventral cord motor neurons. Moreover, nlp-12 signaling was implicated in ARS; but the exact circuit mechanisms and targets of nlp-12 remained elusive. The present work shows in a pretty straight forward way that ckr-1 in SMD head motor neurons is the missing link. In worms, ARS is composed of quiet complex body movements including high angle turns during the worm's forward crawling state. Nlp-12 and ckr-1 mutants show reduced head bending during ARS, while overexpression leads to a stark ectopic ARS like behavior. The authors convincingly show that SMDs are the site of action for ckr-1 and implicated in ARS. They show both requirement and sufficiency of SMDs for ARS like behaviors. The regulation of ARS vs. dispersive behaviors has been extensively studied at the levels of sensory and interneurons in the worm, but how the switch is implemented at motor circuits was largely unknown. Conceptually, this is one of only a few studies investigating the selective control of head versus body movements and provides some interesting insights into the underlying mechanisms; therefore, the study is definitely important and timely. But, it is unclear still how upper sensory circuits transmit the switch between ARS and dispersal to the DVA-SMD circuit. Moreover, the present study does not investigate the signaling pathway of ckr-1 in SMDs and its role in controlling neuronal activity, e.g. via Ca++ imaging. As a sole behavioral genetics study, however, I find the manuscript quite complete. The experiments logically build upon each other and the paper is well written. My only major critique is that parts of the behavioral analyses are described with insufficient detail so that it is unclear to the expert how and what exact movements were quantified. This should be addressed by providing more detailed figure captions, methods sections, more supplemental figures and movies.

1) The authors should exclude (or separate) reversal states and post-reversal turns in their analyses when measuring head bending, body bending and turn events, but it is unclear if they did so.

2) Fig 1C and methods: it is unclear what defines a singular bending event as marked on the y-axis. Did the authors measure the maximum angle during each half-oscillation? If yes, this should be explained and how maxima were calculated etc. Or do the histograms represent all values from all recording frames. In the latter case, the y-axis labelling is misleading, and I suggest use "fraction of frames".

3) Fig 1C: these are averaged histograms of n=10-12 worms, but what is the average number of events per worm and in total?

4) Fig 1B-C, 2A etc.: to perform the measurements as depicted in upper panels is not really trivial, and I have the impression that the authors used their software packages in a black-box manner. What are the exact image processing steps to implement these measurements, i.e. how was vertex and sides of the angles exactly positioned? The authors should provide a time-series of individual examples alongside with movies demonstrating how accurately the pipeline performs during complex ARS postures.

5) Fig 2B: the angles and body segments describing the head and head-bending angels should be unambiguously defined. The cartoon in 2B looks like they just measured nose movements.

6) Fig 3B: reorientation events are not sufficiently defined here. During ARS, worms frequently switch between forward-backward movement, perform post-reversal turns and in a continuous manner exhibit curved trajectories. From a trajectory like the red one in 3A, it is again not trivial to identify and discretize individual turning events with a start and an end and distinguish them from reversals and post reversal turns.

-- The procedure needs to be explained in greater detail with justification of parameter choice.

-- How did the authors validate that the procedure performed well, especially during the complex ARS behaviors?

-- Again, example trajectories and movies should be shown.

7) All histogram panels lack statistics, e.g. KS test or appropriate alternatives.

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 find your work very interesting and acknowledge its importance in understanding the role of cholecystokinin signaling in differentially controlling aspects of locomotion behavior in C. elegans. In its current form, it represents a near complete and well done behavioral genetics study that could improve further with addressing some of the comments below and also harmonizing the behavior metrics that were used for quantifications. The work could be brought to another level though if the authors performed new lines of experiments that give further mechanistic insights, e.g. via physiological methods, into how ckr-1 signaling controls SMD activity.

Reviewer #2:

In this paper, the authors mainly tested peripheral blood mononuclear cells (PBMCs) samples from pediatric cancer and healthy patients by CyTOF, and analyzed the phenotypes of NK, T cells and monocytes. Some scientists have reported these related phenotypes. There is a lack of mechanistic research and many of the conclusions are not yet supported by presented data.

Specific concerns:

1) The authors collected pediatric cancer samples including hepatoblastoma, neuroblastoma, wilms tumor, lymphoma and et al. These types of tumors are quite different. Whether it's appropriate to analyze together? Lymphoma is a disease of the blood system unlike any other types of tumors. Their systemic immunity must have changed.

2) No statistical analysis was performed in Fig2D and E. The conclusion of " Classical monocytes are enriched in pediatric cancer patients" is not supported.

3) Figure 3a is different from the conventional diagram. It was a surprise to see that it showed CD56-dim CD16- and CD56-CD16+ NK cells.

4) Figure 4 lacks statistical analysis.

5) Figure 7 lacks correlation analysis. The conclusion of "Pediatric cancer associated immune perturbations vary by age " is not supported. In addition, the presented correlation diagram is insufficient to prove the above conclusion and title.

Reviewer #1:

The immune status of pediatric cancer patients may differ from that of adult cancer patients and healthy children. Unraveling the distinct immunological features of pediatric cancers may provide novel therapeutic strategies. Dr. Murali Krishna and colleagues analyzed the composition and phenotype of peripheral immune cells in both pediatric cancer patients and age-matched healthy individuals, and they found some interesting alternations in NK cells, monocytes, and T cell subsets. In general, this descriptive study can be potentially interesting for clinicians, immunologists and cancer researchers. However, several major points remain to be addressed.

1) The incidence of hematologic tumors is relatively high in children. It is shown in supplemental table 2 that pediatric patients bearing solid tumor and hematologic malignancies were all included in this study. If solid tumors and lymphoma were analyzed separately, in comparison to healthy individuals, will the major conclusions remain the same?

2) The type, stage, and therapeutic regimens of cancer may affect the landscape of peripheral immune cells. It is not clear whether any of these factors influence the major conclusion. What were the standards to include healthy pediatric individuals as controls in this study?

3) The authors focused on immune cell-related differences between healthy and tumor-bearing children. To reveal typical immunological features of pediatric cancer patients, it is recommended to perform similar analyses with samples from adult cancer patients, particularly those bearing the same type of cancers.

4) The authors claimed that the frequency and cytotoxicity of peripheral NK cells were reduced in young pediatric cancer patients, compared with healthy controls, but these parameters returned to normal in older pediatric cancer patients (>8yrs). Can they separately compare young and old patients with age-matched controls?

5) The authors believe that diminished killing of tumor cells by NK cells from pediatric cancer patients was due to decreased cytotoxic capacity, rather than inefficient recognition or degranulation. More experimental evidence is needed to substantiate this conclusion. These NK cells were significantly shifted to an immunosuppressive/tolerant pattern (high in PD-1, NKG2A, but low in perforin and Granzyme-B), while Long-term (14 days) stimulation with IL-2 can improve their cytotoxicity. Can short-term IL-2 treatment achieve similar effects (e.g. increased cytotoxicity, elevated expression of lytic molecules and CD57)? Since the frequency and cytotoxicity of NK cells in older pediatric cancer patients (>8yrs) were actually similar to that in normal children, do serum IL-2 levels increase in older cancer patients?

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:

Dr Taylor and colleagues aimed to emphasize NK cell-related defects in pediatric cancer patients, in comparison to healthy children. This study was potentially interesting, although it was based on descriptive analyses, lacking mechanistic exploration. In addition, this study included a mixed cohort of pediatric patients bearing tumors of different types, stages, and perhaps distinct therapeutic regimens. Some conclusions were not strongly supported by current experimental evidence. It remains unknown whether similar differences can be found between adult cancer patients and age-matched healthy individuals. To address all these above points, a large amount of further work will be necessary.

Reviewer #2:

Kroll et al. presented a strategy to achieve biallelic knockout effects in the founder (F0) generation of zebrafish, by targeting three different loci within the same target gene, with injection of Cas9 RNP mixtures. They showed that in addition to target single genes, this method could be successfully used to create double knockouts of slc24a5 and tbx5a gene pair, or tyr and ta gene pair, in F0 embryos. Strikingly, they also demonstrated direct generation of triple gene knockouts of mitfa, mpv17 and slc45a2 in F0 larvae, which fully recapitulated the pigmentation defects of the crystal mutant. Furthermore, they provide evidence of the feasibility of their method in dissecting complex and multi-parameter behavioural traits in the biallelic F0 knockouts of trpa1b, csnk1db, scn1lab genes. Interestingly, they established a rapid sequencing-free method to evaluate the activity of Cas9 RNP by using headloop PCR, facilitating the selection of target sites. Finally, the authors proposed a three-step protocol for F0 knockout screens in zebrafish. The strategy described here is quite impressive, and represents evident improvements of the method published by Wu et al. (Developmental Cell, 2018), which was based on the administration of four Cas9/gRNA RNPs. Nevertheless, the manuscript could be further clarified and improved in the following aspects.

1) What are the essential differences in methodology of this method compared with that reported by Wu et al. in 2018 (Developmental Cell)? Or why and how the target sites could be reduced to three from four?

2) Several genes were tested in both work, such as slc24a5, tyr, tbx16, and tbx5a, did you use or compare the same target sites in these genes as reported by Wu et al.?

3) Is the dosage/amount of Cas9 or RNP used in this study different or comparable with Wu et al.? Does it account for the improvement of the method described in the study?

4) The authors propose to design the three target sites in distinct exon within each gene. Is it really important and/or necessary to achieve high efficient biallelic knockouts? Any evidence?

5) According to the section of MATERIALS AND METHODS, the synthetic gRNA was made of two components, i.e., crRNA and tracrRNA. Synthesis of gRNA as a single molecule by in vitro transcription is usually more popular and economic, is it really necessary to use crRNA and tracrRNA to achieve high efficient biallelic knockouts? Any evidence?

6) Could headloop PCR be used for the quantification of mutagenesis efficiency (indel-producing mutation rate) of Cas9/gRNA? How sensitive is this method? Could small indels (such as 1-bp insertion or deletion) be detected by the headloop PCR?

7) In addition to indels, deletions between two double strand breaks induced by two gRNAs are also important for the generation of biallelic knockouts of the target gene. The authors showed the analysis of mutations in each site (such as in Fig. 2A), is it possible to quantify the distribution and contribution of all the different deletions?

8) Fig. 1C and 1D: The authors compared the effects of the injection of 1, 2, 3, and 4 loci. How were the 1, 2, and 3 loci selected from the four target sites? Will each of the four loci give the same or different phenotypic ratio if tested individually? Will different combinations of 2 loci or 3 loci give the same or different phenotypic ratio? Or which combination of 2 loci or 3 loci will give the highest mutagenic effect? For example, in Fig. 1C, the 3-loci showed comparable effect with 4-loci, while the 2-loci is less effective; is it possible to find other 2-loci combinations which could show higher mutagenic efficiency than the current 2-loci, such that the effect of the new 2-loci combination is as good as the 3-loci or 4-loci combination? Conversely, in Fig. 1D, the 2-loci already showed the highest mutagenic effect, is it because of this particular 2-loci combination, or any 2-loci combination will show the same efficiency?

9) Figure 6: The phenotypes of scn1lab F0 knockouts are more severe than those of scn1lab-/- mutant. Any explanation?

Reviewer #1:

Kroll and colleagues describe an efficient strategy to reliably generate F0 zebrafish embryos with (multiple) genes knocked out using CRISPR/Cas9 RNPs. In their most dramatic and broadly applicable proof-of-principle experiment, authors demonstrate successful recapitulation of the triple mutant crystal phenotype in 9/10 F0 embryos. As the authors point out, their methodology is extremely likely to be adapted for candidate genes for traits which display a range of phenotypes among wild type embryos or larvae.

The manuscript points out a rather obvious but somehow underreported feature of NHEJ-based mutagenesis: assuming random size of indels, when 100% of DNA is mutated fewer than 50% (.67x.67) of cells in an embryo will contain frameshift mutations in both alleles. Thus, successful recapitulation of a mutant phenotype in an F0 embryo relies on mutagenesis of an essential part of the protein (not always as straightforward as it seems), utilization of other repair pathways such as MMEJ (not always reliable), or fortuitous help from largely unknown factors which skew the distribution of indel sizes (multiple guide would RNAs need to be tested without guarantee of success). Simultaneously designing several guide RNAs against the gene and co-injecting them, as the authors propose, seems to be an excellent and straightforward strategy.

My most significant criticism is that although new to zebrafish, the described strategies - use multiple guide RNAs and headloop PCR - have been successfully deployed in other systems. Adapting these strategies to the zebrafish model system offers tremendous value, but the distinction between development of new methods and adoption of existing methodologies must be considered.

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 4 of the manuscript.

Summary:

The authors describe a new efficient strategy to reliably generate F0 zebrafish embryos with (multiple) genes knocked out using CRISPR/Cas9 RNPs. They showed that in addition to target single genes, this method could be successfully used to create double knockouts of slc24a5 and tbx5a gene pair, or tyr and ta gene pair, in F0 embryos. Strikingly, they also demonstrated direct generation of triple gene knockouts of mitfa, mpv17 and slc45a2 in F0 larvae, which fully recapitulated the pigmentation defects of the crystal mutant. Their methodology is extremely likely to be adapted for candidate genes for traits which display a range of phenotypes among wild type embryos or larvae.

This is a new tool for the zebrafish community. Despite the presented data on several loci, it is not clear whether and how this method is better compared to a series of prior related F0 approaches. This question is the crux of this methods manuscript.

Reviewer #3:

In this manuscript, Chakravarti and colleagues analyzed the functions of several p53 isoforms in the Drosophila germline. They created novel isoform-specific alleles by CRISPR/Cas9 to untangle the functions of p53A and p53B isoforms. They made use of a Phid-GFP reporter line to follow p53 transcriptional activity. The role of p53 in the development of Drosophila germline has been published several times before with a focus on the silencing of retro-transposons (TEs) and meiotic DNA breaks response (Lu, 2010; Wylie, 2014; Wylie, 2016). Despite this published literature, the authors created novel and very valuable tools, which allowed them to make several novel and interesting observations. My main criticism is that most of these observations remain unexplained and the manuscript feels descriptive as it stands. However, this manuscript has great potential if it could follow up some of these novel observations. Some examples are the following:

1) In Figure 5C, the authors made the interesting observation that hid-GFP was stronger in region 1 of p53A-B+ than in the wild type p53A+B+. This activity of p53 cannot be explained by meiotic DSBs as previously published, since meiotic DSBs only occur later in region 2. This observation remains unexplained and is not explored further.

One possibility is that it could relate to transposable elements (TEs) activity in this region. TEs can create DSBs (thus non-meiotic) and p53 has been published to silence TEs in Drosophila (Wylie, 2014; Wylie, 2016). It is also particularly interesting that the silencing of TEs is known to be weakened in this specific region of the germarium even in wild type condition (Dufourt J, NAR, 2013; Theron E, NAR, 2018). Could p53A play a role in silencing TEs in this region when Piwi is downregulated? This would bring novel insights on when and where TEs are silenced in germ cells.

A transcriptomic analysis of p53A-B+ germ cells could show whether TEs are upregulated in this hid-GFP++ cells. It is probably out of the scope of this manuscript. Another possibility would be to perform FISH for TEs known to be expressed in p53 mutant, such as TAHRE (Wylie, 2016). In addition, do the authors detect DSBs in region 1 in p53A-B+?

2) On Figure 7 and 8, the authors analyzed the role of p53 in "persistent" meiotic DSBs. I am not convinced that these DSBs are only persistent meiotic DSBs. As discussed by the authors themselves (page 13), the origin of these DSBs could be TEs mobilization. I think it is a very important caveat for their conclusions. Another non-exclusive possibility for DSBs appearing in endoreplicating nurse cells is incomplete replication and associated DNA deletions during repair as shown in (Yarosh and Spradling, GD, 2014).

To distinguish between these possibilities and strengthen their conclusions, the authors should perform the same experiments in the absence of meiotic DSBs, such as in a meiW68 mutant background (meiW68, p53AB double mutant). meiW68, okra, p53 mutants may be hard to generate but shRNAs against meiW68 are publicly available and effective, while they may also exist for okra or other spindle genes, and could make this combination easier to generate.

3) The authors showed that p53A and p53B levels are developmentally regulated (Figure 6G): does overexpression of one or both of the isoforms have any phenotype?

4) I agree with the authors that karyosome defects are part of an array of phenotypes induced by the activation of DNA damage checkpoints. However, I would not equal it to the activation of a pachytene checkpoint and conclude that p53 is part of that checkpoint.

5) On Figure 7D, in p53A+B-, there seems to be a lot of DNA damages in follicular cells. Is this reproducible?

Reviewer #2:

The Drosophila genome encodes multiple p53 isoforms. P53 is an important factor in maintaining genome integrity and having multiple isoforms in flies raises an interesting evolutionary concept because humans have a gene family of p53 members. In this paper, the expression and function of the isoforms is compared in the germ line. There are two significant findings based on investigating these two isoforms. First, the apoptotic response depends on the A form, and both have roles in the response to meiotic DSBs. These results represent a significant and important extensions of previous work from another group that showed p53 suppresses transposon activity.

With one important exception, the data are solid and support the conclusions. The data regarding the apoptotic response is based on TUNEL and a hid-GFP reporter. This data shows that irradiation induces a response in the mitotic region but not later regions. Conversely, there is a milder induction in the meiotic region (region 2a). Both could be in response to DSBs. But it is amazing that there is no HID induction following IR in these meiotic regions. Thus, there is a satisfying correlation between the apoptosis and HID responses to IR, and both are diminished in the meiotic region.

The most significant concern with this paper is that conclusions that the p53 isoforms respond to meiotic DNA breaks. Indeed, this is the title of the section starting at the end of pg 7, but there are no experiments which lead to this conclusion. Similarly, the sentence "To determine whether p53A or p53B isoforms responds to meiotic DNA breaks" (pg 8), is followed by an experiment which does not do that (it compares HID expression in different p53 genotypes). The data in the paper are correlations between p53 expression and where DSBs occur in the germarium. Two experiments are needed. First, and most important, hid-GFP expression needs to be analyzed in a mei-W68 mutant. In addition, the germarium should be stained for both HID and gH2AV, the latter being the antibody the authors use in later Figures. It would also be satisfying to see the genotypes in Figure 7 performed in a mei-W68 mutant background, to determine if the persistent DNA damage in the p53 mutants depends on meiotic breaks.

Reviewer #1:

In this manuscript Chakravarti et al build on the previous work from the Calvi lab characterizing specific roles for the p53A isoform. In their 2015 paper Zhang et al showed, using isoform specific loss of function mutants, that p53A is primarily responsible for mediating the apoptotic response to ionizing radiation in the soma and that p53B is very lowly expressed in the cell types studied. They speculated that p53B might function in germline specific roles, such as meiotic checkpoints and DNA repair, identified in mammalian p53 studies.

Here Chakravarti et al, have further characterized the functions of the p53A and B isoforms in Drosophila. In the ovary, p53A mediates the apoptotic response to IR and is also required for meiotic checkpoint activation. p53B is both necessary and sufficient for repair of meiotic breaks in nurse cells but not oocytes. p53B is required for expression of a hid-GFP reporter in region 2a-2b cells which may be related to a loss of p53B detection in p53A/B nuclear bodies at that stage.

There are no substantive concerns with this manuscript.

Minor concerns: CRISPR/Cas9 was used to create isoform-specific mutants for both p53A and p53B. RT-PCR was used to show the mutant alleles are isoform specific and that neither disrupts the expression of the others endogenous protein. The RT-PCR assay can only assess the expression of isoforms, not their function as the authors state.

The authors noted that, even in the absence of IR, there was low level hid-GFP expression in late region 1/early region 2, the point when meiotic DSBs are induced by Mei-W68. Quantitation of hid-GFP expression in the various p53(A+/-,B+/-) mutant backgrounds showed that hid-GFP expression in the absence of IR requires p53 activity and that both isoforms are capable of activating hid-GFP expression. The authors suggest that the increased and earlier expression of hid-GFP seen in the p53A-/p53B+ mutant is due to precocious hyperactivation by p53B unrelated to meiotic breaks which have yet to occur. The authors then seem to contradict themselves saying that p53 reporter construct expression is dependent on Mei-W68, and both isoforms respond to DSBs. Since p53B is capable of precocious activation of at least one p53 target in the absence of p53A expression it is not clear that meiotic breaks themselves directly regulate p53B activity. From the data presented it seems plausible that p53A responding to DSBs might attenuate p53B activity. Quantitation of p53A and p53B levels across oogenesis shows a transient reduction in p53B levels in regions 2a-2b which coincides with the timing of meiotic breaks. Again, it is unclear whether this is a direct response of p53B to meiotic breaks. The authors suggest this change in p53B concentration in the p53A/B body might be due to transient relocalization from the p53A/B body to the nucleoplasm and back but that variation in fluorescence intensity makes it impossible to accurately assess levels in the nucleoplasm to confirm this. While p53B is undetectable in region 2a-2b cells, its presence is required there for expression of hid-GFP, thus translocation from the p53A/B body to fulfill this function is plausible.

The figures are well done and appropriate to the message, however, in the fluorescent images the high background in the mCh channel makes it difficult to see the true signal and it is often completely lost in the merged images. Perhaps use of a greyscale panel would be more informative.

In 2019 Park et al, using Gal4/UAS transgenes in a p53 null background concluded that both p53A and p53B mediated the apoptotic response to IR in the Drosophila ovary. I feel the authors adequately addressed this issue in stating that their current results using loss of function, isoform-specific alleles at the endogenous locus better reflects the true physiological response. Thus, I feel their conclusions on the role of p53 in the ovary have more merit.

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:

The authors have generated new and useful p53 reagents, which they have employed in four functional assays: apoptosis (TUNEL after 40 Gy irradiation (Figures 2-3), transcriptional induction (monitored by hid-GFP (Figures 4-5)), double stranded DNA breaks (DSB) (monitored by gammaH2AV (Figures 7-8)) and activation of pachytene checkpoint (monitored by synaptonemal complex protein C(3)G (Figure 8F-K)).

The main findings are: 1) the apoptotic response to ionizing radiation (IR) depends on p53A; 2) expression of hid-GFP in region 2a-2b germ cells requires p53B; 3) DSBs occur at higher rates in both the p53A and the p53B mutants; and 4) p53B can repair of meiotic breaks in nurse cells but in not oocytes.

Despite the generation of high-quality, new reagents, this paper is currently fairly descriptive. Of 8 figures, two show the expression pattern of the tagged p53 isoforms in various parts of the germarium (Figs 1 and 6). Some of the observations based on functional assays remain unexplained and need further experiments, including points 1 and 2 below.

1) The authors conclude that the p53 isoforms respond to meiotic DNA breaks, but there are no experiments which lead to this conclusion. If the authors want to conclude this, they need (a) to analyze hid-GFP expression a mei-W68 mutant and (b) stain the germarium with both HID and gammaH2AV. The authors should also examine meiotic breaks in p53A+B+, p53A-B-, p53A-B+ and p53A+B- in a background that is also mei-W68 mutant.

2) The authors are missing a more detailed analysis of the interesting observation that hid-GFP is stronger in region 1 of p53A-B+ than in the wild type p53A+B+. This observation cannot be explained by meiotic DSBs (which occurs in region 2), but the authors do not provide a mechanism. Is this due to transposable elements? The authors need to supply new data to provide a mechanistic understanding of this observation.

3) The authors are encouraged to provide better data to support the conclusion that the DNA damage phenotypes of p53 and okra mutants are comparable. The images in Figs. 7, 8B and B' are not sufficient to assess this. The authors could quantify the number of gammaH2AV foci or intensity (rather than measure the number of positive cells). Related to this, it is surprising that p53 mutants lack the DV defects seen in okra mutants, particularly since defects in DSB repair should cause nondisjunction. Okra mutants are sterile. The authors should comment upon the fertility of p53 mutants.

4) Some experiments have only 2 biological replicates (Figs 4 and 8K). Figs 7 and 8 have "2-3 replicates". The authors need to state specifically for each experiment how many replicates were scored. Ideally, they should have at least 3 replicates for each experiment or explain why that is not necessary.

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

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Reply to the reviewers

Reviewer #1 (Evidence, reproducibility and clarity (Required)): **Summary:** This interesting study by Putker et al. showed that circadian rhythmicity persists in several typical circadian assay systems lacking Cry, including Cry knockout mouse behavior and gene expression in Cry knockout fibroblasts. They further demonstrated weak but significant circadian rhythmicity in Cry- and Per- knockout cells. Cry- (and potentially Per-)-independent oscillations are temperature compensated, and CKId/e still has a role in the period regulation of Cry-independent oscillations. **Major comments:** 1) The authors propose that the essential role of mammalian Cryptochrome is to bring the robust oscillation. As the authors analyze in many parts, the robustness of oscillation can be validated by the (relative) amplitude and phase/period variation, both of which should be affected significantly by the method for cell synchronization. Unfortunately, the method for synchronization is not adequately written in this version of supplementary information. This reviewer has no objection to the "iterative refinement of the synchronization protocol" but at least the correspondence between which methods were used in which experiments needs to be clearly explained. The detailed method may be found in the thesis of Dr. Wong, but the methods used in this manuscript need to be detailed within this manuscript.

We thank the reviewer for recognising the importance of different synchronisation protocols. In experiments where bioluminescent CKO rhythms were observed, different synchronisation protocols resulted in similar results when comparing WT with CKO cells. The different synchronisation methods used in each experiment are now specified in the supplementary methods.

2) The authors revealed that CKO mice have apparent behavioral rhythmicity under the condition of LL>DD. This is an intriguing finding. However, it should be carefully evaluated whether this rhythmicity (16 hr cycle) is the direct consequence of circadian rhythmicity observed in CKO and CPKO cells (24 hr cycle) because the period length is much different. Is it possible to induce the 16 hr periodicity in CKO mice behavior by 16 hr-L:16 hr-D cycle? Would it be a plausible another possibility that the 16 hr rhythmicity is the mice version of internal desynchronization or another type of methamphetamine-induced-oscillation/food-entrainable-oscillattion?

The reviewer makes an excellent suggestion. As described in the manuscript text (page 13), CKO mice have already been shown to entrain to restricted feeding cycles (Iijima et al., 2005) and we therefore assessed whether CKO rhythms would entrain to a 16h day as suggested. Whilst CKO (but not WT) mice showed 16h behavioural rhythms during entrainment, they were arrhythmic under constant darkness thereafter (Revised Figure S2A). CKO cellular rhythms show reduced robustness under constant conditions ex vivo, and our other work has revealed that CRY-deficiency renders cells much more susceptible to stress (Wong et al, 2020, BioRxiv). The parsimonious explanation, therefore, is that whilst the cellular timing mechanism remains functional when CRY is absent, the amplitude of cellular clock outputs is severely attenuated (as we showed previously in Hoyle et al., Sci Trans Med, 2017) in a fashion that impairs the fidelity of intercellular synchronisation under most conditions in vivo, as well as the molecular mechanisms of entrainment to light-dark cycles.

With respect to the apparent discrepancy between mean periods of CKO cultured cells (~21h), SCN (~19h) and mice (~17h). This is also observed in WT cells (~26h), SCN (~25h) and mice (~24h), simply with a smaller effect size and longer intrinsic period.

We believe this difference in effect size can adequately be explained by differences in oscillator coupling, combined with the reduced robustness of CKO timekeeping. In Figure 1F we show that the range of rhythmic periods expressed by cultured CKO fibroblasts (14-30h) is much greater than for their WT counterparts (range of 22-26h), or that which is observed when cellular oscillators are coupled in CKO SCN (19h). Thus period of CKO oscillations is demonstrably more plastic (less robust) than WT, and with a cell-intrinsic tendency towards shorter period which is revealed more clearly when oscillators are coupled.

In vivo there is more oscillator coupling in the intact SCN than in an isolated slice, from which communication with the caudal and rostral hypothalamus has been removed. Thus it seems plausible that increased coupling in vivo, combined with positive feedback via behavioural cycles of feeding and locomotor activity, resonate with a common frequency which is shorter than in isolated tissue.

Critically, for both WT and CKO mice/SCN, the circadian period lies within the range of periods observed in isolated fibroblasts. To communicate this rather nuanced point we have inserted the following text into the supplementary discussion:

“Circadian timekeeping is a cellular phenomenon. Co-ordinated ~24h rhythms in behaviour and physiology are observed in multi-cellular mammals under non-stressed conditions when individual cellular rhythms are synchronised and amplified by appropriate extrinsic and intrinsic timing cues. In light of short period (~16.5h) locomotor rhythms observed in CKO mice after transition from constant light to constant dark, but failure to entrain to 12h:12h light:dark cycles, it seemed plausible that either CKO mice might entrain to an short 8h:8h light:dark (16h day) or else have a general deficiency to entrainment by light:dark cycles. The data in Figure S2 supports the latter possibility, in that neither WT nor CKO mice stably entrained to 16h cycles whereas WT but not CKO mice entrained to 24h days. The bioluminescence oscillations observed in CKO cells conform to the long-established definition of a circadian rhythm (temperature-compensated ~24h period of oscillation with appropriate phase-response to relevant environmental stimuli). Whereas the locomotor rhythms observed in CKO mice under quite specific environmental conditions correlates with both the cellular and SCN data to suggest the persistence of capacity to maintain behavioural rhythms close to the circadian range, but which is masked under most circumstances. We suggest that in vivo the (pathophysiological) stress of CRY-deficiency is epistatic to the expression of daily rhythms in locomotor activity following standard entrainment by light:dark cycles and thus, whilst not arrhythmic, also cannot be described as circadian in the strictest sense.”

3) The authors proposed that CKId/e at least in part is the component of cytoscillator (Fig. 5D), and turnover control of PER (likely to be controlled by CKId/e) may be an interaction point between cytoscillator and canonical circadian TTFL (Fig. 4). Strictly speaking, this model is not directly supported by the experimental setting of the current manuscript. The contribution of CKId/e is evaluated in the presence of PER by monitoring the canonical TTFL output (i.e. PER2::LUC); thus it is not clear whether the kinase determines the period of cytoscillator. It would be valuable to ask whether the PF and CHIR have the period-lengthening effect on the Nrd1:LUC in the CPKO cell.

Another excellent suggestion, thanks. The experiment, showing similar results in CKO and CPKO cells, was performed and is now reported in Revised Figure S5D. The text was amended as follows: “We found that inhibition of CK1d/e and GSK3-α/β had the same effect on circadian period in CKO cells, CPKO cells, and WT controls (Figure 5A, B, S5A, B, D).”

Moreover, our data are further supported by findings in RBCs, where CK1 inhibition affects circadian period in a similar manner as in WT and CKO cells (Beale et al, JBR 2019).

**Minor comments:**

4) The authors argue that the CKO cells' rhythmicity is entrained by the temperature cycle (Fig. 2C). Because the data of CKO cell only shows one peak after the release of constant temperature phase, it is difficult to conclude whether the cell is entrained or just respond to the final temperature shift.

We agree with the reviewer and have replaced the original figure with another recording that includes an extra circadian cycle in free-running conditions (Revised Figure 2C).

5) It would be useful for readers to provide information on the known phenotype of TIMELESS knockout flies; TIM is widely accepted as an essential component of the circadian clock in flies; are there any studies showing the presence of circadian rhythmicity in Tim-knockout flies (even if it is an oscillation seen in limited conditions, such as the neonatal SCN rhythm in mammalian Cry knockout)?

The reviewer is correct that TIM is widely accepted as an essential component of the circadian clock in flies. Using more sensitive modern techniques however, ~50% of classic Tim01 mutant flies exhibit significant behavioural rhythms in the circadian range under constant darkness, as reported:

https://opus.bibliothek.uni-wuerzburg.de/frontdoor/index/index/year/2015/docId/11914

For this reason we employed a full gene knockout of the Timeless gene (Lamaze et al., Sci Rep, 2017), where the majority of flies are behaviourally arrhythmic under constant conditions following standard entrainment by light cycles and therefore represents a more appropriate model for CRY-deficient cells.

We have revised the legend of Figure S2 to include the following:

“N.B. The generation of Timout flies is reported in Lamaze et al, Sci Rep, 2017. Similar to CRY-deficient mice, whole gene Timeless knockout flies are characterised as being behaviourally arrhythmic under constant darkness following entrainment by light:dark cycles: https://opus.bibliothek.uni-wuerzburg.de/frontdoor/index/index/year/2015/docId/11914”

5) Figure 3C shows that the amount of PER2::LUC mRNA changes ~2 fold between time = 0 hr and 24 hr in the CKO cell. This amplitude is similar to that observed in WT cell although the peak phase is different. Does the PER2::LUC mRNA level show the oscillation in CKO cells?

No, we think we have shown convincingly this is not the case. We argue the data in figure 3C show that: (a) there is no circadian variation in mRNA PER2::LUC expression (mRNA levels increase but no trough is observed) and (b) that the temporal relationship between protein and mRNA as observed in WT is broken; i.e. the CRY-independent circadian variation in protein levels cannot be “driven by” changes in transcript levels. Similar results were obtained using transcriptional reporters Per2:LUC and Cry1:LUC (Figure S3E and F). Moreover, our findings are also in line with previous reports, such as Nangle et al. (2014, eLife) and Ode et al. (Mol Cell, 2017).

6) Figure 3D: the authors discuss the amplitude and variation (whether the signal is noisier or not) of reporter luciferase expression between different cell lines. However, a huge difference in the luciferase signal can be observed even in the detrended bioluminescence plot. This reviewer concerns that some of the phenotypes of CKO and CPKO MEF reflect the lower transfection efficiency of the reporter gene, not the nature of circadian oscillators of these cell lines.

As reported in the methods, these are stable cell lines rather than transiently transfected cells. The detrended luciferase data presented here do not actually reflect raw levels of luciferase protein expression, but rather reflect the amount of deviation from the 24 hour average. To make it easier to compare expression levels of Per2:LUC and Nr1d1:LUC between the different cell lines we have added figure S3H, presenting the average raw bioluminescence levels over 24 hours (after 24 hours of recovery from media change; ie from 24-48 hours). Using these data one can appreciate that expression levels of the Per2 reporter are never lower in CRY KO cells when compared to WT. We hope these data can take away the reviewer’s concerns about expression levels causing the differences observed.

Reviewer #1 (Significance (Required)): Although Cryptochrome (Cry) has been considered a central component of the mammalian circadian clock, several studies have shown that circadian rhythms are maintained in the absence of Cry, including in the neonate SCN and red blood cells. Thus, although the need for Cry as a circadian oscillator has been debated, its essential role as a circadian oscillator remains established, at least in the cell-autonomous clock driven by the TTFL. This study provides additional evidence that the circadian rhythmicity can persist in the absence of Cry. More general context, the presence of a non-TTFL circadian oscillator has been one of the major topics in the field of circadian clocks except for the cyanobacteria. In mammals, the authors’ and other groups lead the finding of circadian oscillation in the absence of canonical TTFL by showing the redox cycle in red blood cells (O’Neil, Nature 2011). The presence of circadian oscillation in the absence of Bmal1 is also reported recently(Ray, Science 2020). Bmal1(-CLOCK), CRY, and PER compose the core mechanism of canonical circadian TTFL; thus, this manuscript put another layer of evidence for the non-TTFL circadian oscillation in mammals. Overall, the manuscript reports several surprising results that will receive considerable attention from the circadian community. This reviewer has expertise in the field of mammalian circadian clocks, including genomics, biochemistry, and mice's behavior analysis.

Reviewer #2 (Evidence, reproducibility and clarity (Required)): In the canonical model of the mammalian circadian system, transcription factors, BMAL1/CLOCK, drive transcription of Cry and Per genes and CRY and PER proteins repress the BMAL1/CLOCK activity to close the feedback loop in a circadian cycle. The dominant opinion was that CRY1 and CRY2 are essential repressors of the mammalian circadian system. However, this was challenged by persistent bioluminescence rhythms observed in SCN slices derived from Cry-null mice (Maywood et al., 2011 PNAS) and then by persistent behavior rhythms shown by the Cry1 and Cry2 double knockout mice if they are synchronized under constant light prior to free running in the dark (Ono et al., 2013 PLOS One). In the manuscript, the authors first confirmed behavioral and molecular rhythms in the Cry1/Cry2- deficient mice and then provided evidence to suggest the rhythms of Per2:LUC and Nr1d1:LUC in CKOs are generated from the cytoplasmic oscillator instead of the well-studied transcription and translation feedback loop: Constant Per2 transcription driven by BMAL1/CLOCK plus rhythmic degradation of the PER protein result in a rhythmic PER2 level in the absence of both Cry1 and Cry2, which suggests a connection between the classic transcription- and translation-based negative feedback loops and non-canonical oscillators. **Major points:** Line 38-39, "Challenging this interpretation, however, we find evidence for persistent circadian rhythms in mouse behavior and cellular PER2 levels when CRY is absent." The rhythmic behavioral phenotype of cry1 and cry2 double knockout mice was first documented by Ono et al., 2013 PLOS ONE, in which eight cry1 and cry2 double knockout mice after synchronization in the light displayed circadian periods with different lengths and qualities. The paper reported two period lengths from the Cry mutant mice: "An eye-fitted regression line revealed that the mean shorter period was 22.86+/-0.4 h (n= 8) and the mean longer period was 24.66+/-0.2 h (n =9). The difference of two periods was statistically significant (p, 0.01).", either of which is quite different from the ~16.5 hr period in Figure 1B of the manuscript. A brief discussion on the period difference between studies will be helpful for readers to understand. Period information from the individual mouse should be calculated and shown since big period variations exist among CKO mice (Ono et al., 2013 PLOS One).

Thanks for this suggestion. The mice used by Ono et al were raised from birth in constant light, whereas we used mice that were weaned and raised in normal LD cycles before being subject to constant light then constant dark as adults. Instead of the somewhat subjective fitting of regression lines by eye performed by Ono et al, our analysis was performed using the periodogram analysis routine of ClockLab 6.0 with a significance threshold for rhythmicity of p=0.0001. We have now repeated this experiment with 10 adult CKO mice (male and female), and found no evidence for two period lengths in that the second most significant period was consistently double that of the first. As the reviewer suggests, there is a much broader distribution of CKO mouse periods compared with WT, as we also found in cultured cells and SCN. These new data are now reported in revised Figure S1B & C. We have also included a statement about how our study differs from Ono et al in the supplementary discussion.

The behavioral phenotype of Cry-null mice and luminescence from their SCNs are robustly rhythmic while fibroblasts derived from these mice only produce rhythms with very low amplitudes compared with those in WT, which may reflect the difference between the SCN’s rhythm and peripheral clocks. The behavioral phenotype is supposed to be controlled mainly by SCN. However, most molecular analyses in the work were done with MEF and lung fibroblasts. These tissues may not be the best representative of the behavioral phenotype of the CKO mice.

Behavioural rhythms of CKO mice are significantly less robust than WT, with mean amplitude less than 50% of WT controls (Figures 1A & B, revised S1B. Furthermore, as reported, 40% of CKO SCN slices exhibited PER2::LUC rhythms, compared with 100% of WT SCN slices (as also observed by Maywood et al., PNAS, 2013), and therefore are also less robust by the definition used in this manuscript.

As now discussed in the revised supplementary discussion:

“Circadian timekeeping is a cellular phenomenon. Co-ordinated ~24h rhythms in behaviour and physiology are observed in multi-cellular mammals under non-stressed conditions when individual cellular rhythms are synchronised and amplified by appropriate extrinsic and intrinsic timing cues.”

The objective of this study was to understand the fundamental determinants that allow mammalian cells to generate a circadian rhythm, which we find does not include an essential role for CRY genes/proteins. Thus the cell is the appropriate level of biological abstraction at which to investigate the phenomenon, whereas the SCN and behavioural recordings simply serve to illustrate the competence of CRY-independent timing mechanisms to co-ordinate biological rhythms at higher levels of biological scale which are manifest under some conditions. To reiterate, the behavioural data supports the cellular observations, not the converse.

Stronger evidence is needed to fully exclude the possibility that in CKO cells, the rhythm is not generated by PERs' compensation for the loss of Crys to repress BMAL1 and CLOCK. Since the rhythms of Per:LUC or Nr1d1:LUC (Figures 3D and S3E) are much weaker than those in WT, molecular analyses might not be sensitive enough to reflect the changes across a circadian cycle in the CKOs if the TTFL still occurs. CLOCKΔ19 mutant mice have a ~4 hr longer period than WT (Antoch et al., 1997 Cell; King et al., 1997 Cell). CLOCKΔ19; CKO cells or mice should be very helpful to address the question. Periods of Per:LUC and Nr1d1:LUC from the CLOCKΔ19; CKO should be similar to those in the CKO alone if the transcription feedback does not contribute to their oscillations.

We agree this would be an interesting experiment, however the data in this manuscript and Wong et al. (BioRxiv, 2020), whilst not disputing the existence of the TTFL, strongly suggest that it fulfils a different function to that which is currently accepted and is not the mechanism that ultimately confers circadian periodicity upon mammalian cells. CLOCKΔ19 is an antimorphic gain-of-function mutation with many pleiotropic effects. Therefore, if the TTFL is not the basis of circadian timekeeping in mammalian cells, it follows that the CLOCKΔ19 mutation may not elicit its effects on circadian rhythms through delaying the timing of transcriptional activation, as was proposed. As such, whether or not CLOCKΔ19 alters circadian period of CKO cells/mice would not allow the two models to be distinguished in the way that the reviewer envisions.

Secondly, we cannot detect any interaction between PER2 and BMAL1 in the absence of CRY using an extremely sensitive assay.

Thirdly, very strong biochemical evidence suggests that PER has no repressive function in the absence of CRY (Chiou et al., 2016; Kume et al., 1999; Ode et al., 2017; Sato et al., 2006).

Finally, in several figures particularly 3C and 4A, we show that PER2 peaks at the same time CKO and WT cells, but in CKO cells this is not accompanied by a coincident peak in the mRNA. Thus, even if PER were able to repress BMAL1/CLOCK without CRY, rhythms in PER2 protein level could not be explained by some residual PER/BMAL1-dependent TTFL mechanism.

To address the reviewer’s concern however, we have employed mouse red blood cells which offer unambiguous insight into the causal determinants of circadian timing, as we can be absolutely confident that there is no transcriptional contribution to cellular timekeeping. Briefly, we took fibroblasts and RBCs from WT, short period Tau/Tau and long period Afh/Afh mutant mice. The basis of the circadian phenotype of these mutations is quite well established as occurring through the post-translational regulation of PER and CRY proteins respectively, and result in short and long period PER2::LUC rhythms compared with WT fibroblasts. RBCs do not express PER or CRY proteins, and commensurately no genotype-dependent differences of RBC circadian period were observed (Beale et al, 2020, in submission). In contrast, RBC circadian rhythms are sensitive to pharmacological inhibition of casein kinase 1 (Beale et al., JBR, 2019).

Lines 51-52, "PER/CRY-mediated negative feedback is dispensable for mammalian circadian timekeeping" and lines 310-311, "We found that transcriptional feedback in the canonical TTFL clock model is dispensable for cell-autonomous circadian timekeeping in animal and cellular models." The authors have not excluded the possibility that the rhythmic behaviors of the CKO mice are derived from the PERs' compensation for the role of Crys in the feedback loop of the circadian clock in the SCN. In the fibroblasts, only two genes, Per2 and Nr1d1, have been studied in the work, which cannot be simply expanded to the thousands of circadian controlled genes. Also amplitudes of PER2:LUC and NR1D1:LUC in the CKOs are much lower than those in WT and no evidence has been provided to show that their weak rhythms are biologically relevant.

The definition of a circadian rhythm (Pittendrigh, 1960) does not mention biological relevance or stipulate any lower threshold for amplitude. As now stated in the revised text (page 6):

“PER2::LUC rhythms in CKO cells were temperature compensated (Figure 2A, B) and entrained to 12h:12h 32°C:37°C temperature cycles in the same phase as WT controls (Figures 2C), and thus conform to the classic definition of a circadian rhythm (Pittendrigh, 1960) – which does not stipulate any lower threshold for amplitude or robustness.”

We make no claims about biological relevance or amplitude in this manuscript, which are addressed in our related manuscript (Wong et al., BioRxiv, 2020). In this related manuscript, we explicitly address whether CRY is necessary for mammalian cells to maintain a circadian rhythm in the abundance of clock-controlled proteins and find that it is not. Indeed, twice as many rhythmically abundant proteins are observed in CKO cells than WT controls, which suggests that, if anything, CRY functions to suppress rhythms in protein abundance rather than to generate them.

We observe circadian rhythms in the activity of two different bioluminescent reporters, which have already been extensively characterised. The mouse and SCN data in figure 1 are correlative, and simply show that previous published observations are reproducible. PER2::LUC oscillations are not accompanied by Per2 mRNA oscillations. This, together with the absence of a BMAL1-PER2::LUC complex strongly argues against a model where PER2 oscillations are driven by residual (PER2-driven) transcriptional oscillations.

We therefore concede the reviewer’s point that we “cannot exclude rhythmic behaviors of the CKO mice are derived from the PERs' compensation for the role of Crys in the feedback loop of the circadian clock in the SCN”. The reviewer will agree however, that there exists very strong biochemical evidence suggests that PER has no repressive function in the absence of CRY (Chiou et al., 2016; Kume et al., 1999; Ode et al., 2017; Sato et al., 2006); that there exists no experimental evidence to suggest that PERs can fulfil this function in the absence of CRY in any mammalian cellular context; and finally that our observations are not consistent with the canonical model for the generation of circadian rhythms in mammals.

We have therefore amended the text to focus on CRY specifically, as follows:

“PER/CRY-mediated negative feedback is dispensable for mammalian circadian timekeeping”

Page 12. “We found that CRY-mediated transcriptional feedback in the canonical TTFL clock model is dispensable for cell-autonomous circadian timekeeping in cellular models. Whilst we cannot exclude the possibility that in the SCN, but not fibroblasts, PER alone may be competent to effect transcriptional feedback repression in the absence of CRY, we are not aware of any evidence that would render this possibility biochemically feasible.”

**Minor points:** Lines 66-67, "...(Dunlap, 1999; Reppert and Weaver, 2002; Takahashi, 2016)." to "... (reviewed in Dunlap, 1999; Reppert and Weaver, 2002; Takahashi, 2016)."

Thanks, changed as requested.

Line 70, "...((Liu et al., 2008..." to "...(Liu et al., 2008..."

Thanks, changed as requested.

Lines 174-175, "Considering recent reports that transcriptional feedback repression is not absolutely required for circadian rhythms in the activity of FRQ...". Larrondo et al., 2015 paper says "however, in such ∆fwd-1 cells, the amount of FRQ still oscillated, the result of cyclic transcription of frq and reinitiation of FRQ synthesis." The point of the paper is "we unveiled an unexpected uncoupling between negative element half-life and circadian period determination." instead of "...transcriptional feedback repression is not absolutely required for circadian rhythms in the activity of FRQ,"

This is a good point which, following discussion with Profs Dunlap and Larrondo, we have revised into “no obligate relationship between clock protein turnover and circadian regulation of its activity” – a more accurate summary of their findings.

Lines 249-252, "CKO cells exhibit no rhythm in Per2 mRNA (Figure 3C, D), nor do they show a rhythm in global translational rate (Figure S4A, B), nor did we observe any interaction between BMAL1 and S6K/eIF4 as occurs in WT cells (Lipton et al, 2015) (Figure S4C)." In figures 3D and S3E, in CKO and CPKO cells the Per2:LUC data without fitting look better than that of Nr1d1:LUC. But the Nr1d1:LUC rhythm became clear after fitting the raw data. So to better visualize the low amplitude rhythm, if any, of Per2:LUC and compare with Nr1d1:LUC, fitted the Per2:LUC data in CKOs and CPKOs in Figure 3D and S3E should be shown as what has been done to Nr1d1:LUC.

Thanks, these data can be found in Figure S3F. The detrended Per2:Luc CKO and CPKO bioluminescence traces were better fit by the null hypothesis (straight line) than a damped sine wave (p>0.05) and so were not significantly rhythmic by the criteria used in this manuscript.

Lines 258-259, "much less than the half-life of luciferase expressed in fibroblasts under a constitutive promoter" In figure S4D, the y-axis of the PER2::LUC is ~800 while the y-axis of the SV40::LUC is ~600000. The over-expressed LUC by the SV40 promoter might saturate the degradation system in the cell so the comparison is not fair. A weaker promoter with the level similar to Per2 should be used to make the comparison.

Thank you for this suggestion. In our experience, the SV40 promoter is actually a rather weak promoter compared with CMV, and faithfully facilitates the constitutive (non-rhythmic) expression of heterologous proteins such as Luciferase (Feeney et al., JBR, 2016). It has been shown previously that constitutive over-expression of heterologous proteins such as GFP or even CRY1 does not affect circadian rhythms in fibroblast cells (e.g. Chen et al., Mol Cell, 2009). To address the reviewer’s reasonable concern however, multiple stable SV40:Luc fibroblast lines were generated by puromycin selection, grown to confluence in 96-well plates, then treated with 25 μg/mL CHX at the beginning of the recording. Random genomic integration of SV40:Luc leads to a broad range of different levels of luciferase expression, evident from the broad range of initial luciferase activities. For each line the decline in luciferase activity was fit with a simple one-phase exponential decay curve (R2≥0.98) to derive the half-life of luciferase in each cell line. There was no significant relationship between the level of luciferase expression and luciferase stability (straight line vs. horizontal line fit p-value = 0.82). Therefore constitutive expression of SV40:Luc in fibroblasts does affect the cellular protein degradation machinery within the range of expression used for our half-life measurements. These new data are reported in Revised Figure S3H.

Line 430, "sigma" to "Sigma".

Changed

In figure S2, the classification of rhythms in Drosophila is not clear since even the "Robustly rhythmic" ones have high background noise. Detrending or fitting the data might be able to improve the quality of the rhythms prior to classification.

These are noisy data as they come from freely behaving flies. The mean data was shown in Figure S3A and individual examples in S3B, and look very similar to previous bioluminescence fly recordings of XLG-LUC flies in papers from the Stanewsky lab who have published extensively using this model. The classifications arose from double-blinded analysis of the bioluminescence traces by several individuals, but we agree that this was not clearly communicated in our original submission. In Revised figure S2 we now present the mean bioluminescence traces, with and without damped sine wave vs. straight line fitting, as suggested, which is more consistent with the mammalian cellular data presented elsewhere.

In figure S3B, the original blots for Per2 including Input and IP should be shown.

The original blots for BMAL1 are shown in figure S3I. PER2::LUC levels were assessed by measuring bioluminescence levels present on the anti-bmal1-beads, as described in the figure 3B legend.

Supplemental information Line 44, "...(reviewed in (Lakin-Thomas,..." to "...(reviewed in Lakin-Thomas,..."

Changed

Line 188, "Period CDS", the full name of CDS should be provided the first time it appearances.

Changed to “coding sequence”.

Reviewer #2 (Significance (Required)): The work suggests a link between the TTFL and non-canonical oscillators, which should be interesting to the circadian field.

Reviewer #3 (Evidence, reproducibility and clarity (Required)): **Summary:** The paper "CRYPTOCHROMES confer robustness, not rhythmicity, to circadian timekeeping" by Putker et al. answers the question of whether or not the rhythmic abundance of clock proteins is a prerequisite for circadian timekeeping. They addressed this by monitoring PER2::LUC rhythms in WT and CRY KO (CKO) cells. CRY forms a complex with PER, which in turn represses the ability of CLOCK/BMAL1 to drive the expression of clock-controlled genes, including PER and CRY. Consistent with previous observations, the authors found residual PER2::LUC rhythms in CKO SCN slices, fibroblasts and in a functional analogue KO of CRY in Drosophila, even in the absence of rhythmic Per2 transcription due to the loss of CRY as a negative regulator of the oscillation. They have shown that these rhythms, in the absence of CRY, follow the formal definition of circadian rhythms. They attributed these residual PER2::LUC rhythms to the maintenance of oscillation in PER2::LUC stability independent of CRY, by testing the decay kinetics of luciferase activity when translation is inhibited. Moreover, they implicated the kinases CK1d/e and GSK3 to be involved in regulating PER2::LUC post-translational rhythms through kinase inhibitor studies. They concluded that CRY is not necessary for maintaining PER2::LUC rhythms, but plays an important role in reinforcing high-amplitude rhythms when coupled to a proposed "ctyoscillator" likely composed of CK1d/e and GSK3. **Major comments:** The authors have shown sufficient data that under different testing conditions (mice locomotor activity, SCN preps or fibroblasts), behavioral rhythms and PER2::LUC rhythms are still observed in the CRY KO (CKO) cells, contrary to a previous study (Liu et al., 2007). They also indicated limitations to some of the.experimental work. However, there are some parts of the paper that need clarification to support their conclusions. 1.In Fig. 1A, the x-axes of the actograms for WT and CKO are different. While they mentioned this in the figure legend, and described the axis transformation in Fig. S1A, they need a justification statement about why they did this in the results.

Thanks, we have included the following sentence in the results section as requested:

“Figure 1 representative actograms are plotted as a function of endogenous tau (**t) to allow the periodic organisation of rest-activity cycles to be readily discerned; 24h-plotted actograms are shown in Figure S1A and S2A”

2.In an attempt to show conservation of their proposed role for CRY, they tested the model system Drosophila melanogaster where TIMELESS serves as the functional analogue of CRY. While they showed in the figures and described in the text that rhythms still persisted with lower relative amplitude in the TIMELESS-deficient flies, they did not describe any period differences between WT and mutant. Showing the period quantification in Supp. Fig. S2 using the robustly rhythmic datasets, and describing this data in the text, will strengthen their claim.

These analyses are now reported in revised Figure S2 as requested. As described in our response to reviewer 2, the “robustly rhythmic” flies were scored as such through double-blinded analysis by several individuals. We hope the reviewer will appreciate our concern that exclusion of the majority of TIMELESS-deficient flies that were not robustly rhythmic might skew their apparent period by unconscious bias towards favouring traces that most clearly resemble robustly rhythmic WT controls. To avoid any potential bias we therefore included all flies of both genotypes in the analysis of circadian period for the revised figure, as suggested by our other reviewers.

In Fig. S2B, there is no clear distinction between the representative datasets shown for poorly rhythmic and arrhythmic, i.e. they all appear arrhythmic, without an indicated statistical test. The authors could present better representative data to better reflect the categories.

As described above, we now show the grouped mean with and without fitting for all flies of both genotypes. The statistical test for rhythmicity and analysis of circadian period is now the same as was performed for the cellular data presented elsewhere.

3.In Fig. 2A, the authors note the lack of rhythmicity in the CKO fibroblasts in the 1st three days at 37oC. How are the conditions here different from fibroblasts in Fig. 1E, where rhythms are seen during the 1st three days in CKO fibroblasts?

As discussed in the manuscript, PER2::LUC rhythms in CKO cells and SCN are observed stochastically between recordings i.e. if one dish in a recording showed rhythms, all dishes showed rhythms and vice versa. The media change that occurred after 3 days in Fig 2A, in this case, was sufficient to initiate clear rhythms of PER2::LUC in all experimental replicates. In other experiments, media change did not have this effect. Herculean efforts by multiple lab members over many years, including the PI, have been unable to delineate the basis of this variability – which is discussed at length in the thesis of Dr. David Wong https://www.repository.cam.ac.uk/handle/1810/300610. As such, we clearly state in the discussion:

“We were unable to identify all of the variables that contribute to the apparent stochasticity of CKO PER2::LUC oscillations, and so cannot distinguish whether this variability arises from reduced fidelity of PER2::LUC as a circadian reporter or impaired timing function in CKO cells. In consequence, we restricted our study to those recordings in which clear bioluminescence rhythms were observed, enabling the interrogation of TTFL-independent cellular timekeeping.”

1. The authors claimed in the results section- "in contrast and as expected, Per2 mRNA in WT cells varied in phase with co-recorded PER2::LUC oscillations." but Fig. 3C does not show this expected lag between mRNA and protein levels. This needs to be explained

No lag is expected in vitro. A lag between PER protein levels and Per mRNA does occur in vivo and is very likely to attributable to daily rhythms in feeding (Crosby et al, Cell, 2019), where increased insulin signalling elicits an increase in PER protein production 4-6h after E-box and GRE-stimulated increase in Per transcription.

When luciferin is saturating intracellularly, PER2::LUC activity correlates most closely with the amount of PER2::LUC protein that was translated during the preceding 1-2h, rather than the total amount of PER2, due to the enzymatic inactivation of the luciferase protein (Feeney et al, JBR, 2016). Consistent with many previous observations, under constant conditions, the rate of nascent PER protein synthesis is largely determined by the level of Per2 mRNA, and thus more similar phases are observed between protein and mRNA in vitro than in vivo.

We have inserted an additional citation of Feeney et al at this point in the text to make this clear.

5.In Figs. 5A-B, the PER2::LUC periods in the CKO untreated cells seem to vary significantly between A, B, and C. While this could be due to the high variability in the rhythms that were previously described by the authors, the average periods here seem to be longer than the one reported in Fig. 1F. Are there specific condition differences?

There are no specific condition differences. As reported in Figure S1B, D & E, the range of CKO cellular periods is simply much broader than for WT cells. Over several dozen experiments the average period was significantly shorter, but the period variance is an equally striking feature of rhythms in these cells which we take as evidence for their lack of robustness.

*Would additional experiments be essential to support the claims of the paper?*

1. There is sufficient experimental data to support the major claims; however some suggested experiments are listed below.

   a. If CKO exhibits residual rhythms in PER::LUC, it would be interesting to know how CRY overexpression influences PER2::LUC rhythms, or point to previous reference papers which may have already shown such effects. The prediction would be PER2::LUC levels will still be rhythmic when CRY is overexpressed. What would be the extent of "robustness" conferred by CRY on PER2::LUC rhythms based on CRY KO and overexpression studies?

These experiments have largely already been performed (see Chen et al., Mol Cell; Nangle et al., eLife, 2014; Fan et al., Curr Biol, 2007; Edwards et al., PNAS, 2016) and are cited in this manuscript. As suggested, PER2 rhythms remain intact under CRY1 over-expression, though are clearly perturbed, but their robustness was not investigated in any detail. We hope to be able to address this important question in our subsequent work

The authors found that CK1d/e and GSK3 contribute to CRY-independent PER2 oscillations by showing that addition of kinase inhibitors affect the PER2::LUC period lengths in WT and CKO in the same manner. It would be interesting to know if a) PER2::LUC stability and b) PER2 phosphorylation status, is affected in WT and CKO in the presence of the inhibitors, or point to previous reference papers which may already have shown such effects.

As the reviewer points out, PER2 stability is already reported to be regulated via phosphorylation by GSK3 and CK1. We have made explicit reference to this in the revised manuscript as follows:

“In contemporary models of the mammalian cellular clockwork CRY proteins are essential for rhythmic PER protein production, however, the stability and activity of PER proteins are also regulated post-translationally (Lee et al., 2009; Philpott et al., 2020; Iitaka et al, 2005).”

*Are the data and the methods presented in such a way that they can be reproduced?*

1. The protocol for the inhibitor treatments are not in the main or supplemental methods.

In the main text methods, section luciferase recordings we state: “For pharmacological perturbation experiments (unless stated otherwise in the text) cells were changed into drug-containing air medium from the start of the recording. Mock-treatments were carried out with DMSO or ethanol as appropriate.”

*Are the experiments adequately replicated and statistical analysis adequate?*

1. All experiments had the sufficient number of technical and biological replicates to make valid statistical analyses. For Fig. S2, the authors used RAIN to assess rhythmicity in WT and mutant flies, but it is not clear whether the different categories (rhythmic, poorly rhythmic, and arrhythmic) were based on amplitude differences alone, or a combination of amplitude and p-values as determined by RAIN.

As reported above, we have revised the analysis of the fly data to be consistent with the cellular data reported elsewhere in the manuscript.

**Minor comments:** *1. Are prior studies referenced appropriately?* Authors may wish to include Fan et al., 2007, Current Biology which demonstrated that cycling of CRY1, CRY2, and BMAL1 is not necessary for circadian-clock function in fibroblasts.

Apologies for the omission of citation to this excellent paper. Now referenced in the introduction.

*2. Are the text and figures clear and accurate?* Figures were clear and illustrated well. See minor comments on text below:

1. Other minor comments

Main Text: p3, line 62; p12, line l32: It doesn't seem necessary or appropriate to cite the dictionary for the definition of robust.

Thanks for this suggestion. During preparation of the manuscript we found that there was some disagreement between authors as to the meaning of robustness in a circadian context. We therefore feel it most necessary to define clearly what we mean by the use of this word to avoid any potential ambiguity.

p4, line l87: "~20 h" rhythms instead of "~20h-hour" p3, line 70; p5, line 121; p14, line 380; p16, line 416 and p18, line 458: Close parentheses have been doubled in parenthetical references. p14, line 363: "crassa" instead of "Crassa" p17, line 430: "Sigma" instead of "sigma" p18, lines 464 and 483; p20, line 521: put a space between numerical values and units, to be consistent with other entries p19, line 488: "luciferase" instead of Luciferase p20, line 512: "Cell Signaling" instead of "cell signalling" p20, line 526: "single" instead of "Single"

We thank the reviewer for his/her thoroughness, all of the above have been changed.

Main figures: Fig. 2 p37, line 921: close parenthesis was doubled on "red"

This was actually correct.

Fig. 4 p41, line 989: "0.1 mM" instead of "0.1 mM" for consistency throughout text Supplementary text: line 171: "30 mM HEPES" instead of "30mM HEPES" line 184: "Cell Signaling" instead of "cell signalling" Supplementary figures: Fig. S2A "Drosophila melanogaster" instead of "Drosophila Melanogaster"

All of the above have been changed.

Reviewer #3 (Significance (Required)): This paper revisits the previously proposed idea that rhythmic expression of central TTFL components is not essential for circadian timekeeping to persist. However, this paper does not add a significant advance in the understanding of the underlying reasons behind sustained clock protein rhythmicity like PER in the absence of CRY, since such mechanisms in functional analogs have been shown in other systems, like Neurospora (Larrondo et al., 2015). However, this paper does clarify some issues in the field, such as discrepancies between behavioral and cellular rhythms observed in CKO mice, leading future researchers to examine closely the conditions of their CKO rhythmic assays before making conclusions pertaining to rhythmicity. The identification of the kinases as components of the proposed cytosolic oscillator (cytoscillator) needs further validation, but this is perhaps beyond the scope of the paper. The data provides incremental evidence for the existence of a cytoscillator, but opens up opportunities to identify other players, like phosphatases, to establish the connection between the central TTFL and the proposed cytoscillator.

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Referee #3

Evidence, reproducibility and clarity

Summary:

The paper "CRYPTOCHROMES confer robustness, not rhythmicity, to circadian timekeeping" by Putker et al. answers the question of whether or not the rhythmic abundance of clock proteins is a prerequisite for circadian timekeeping. They addressed this by monitoring PER2::LUC rhythms in WT and CRY KO (CKO) cells. CRY forms a complex with PER, which in turn represses the ability of CLOCK/BMAL1 to drive the expression of clock-controlled genes, including PER and CRY. Consistent with previous observations, the authors found residual PER2::LUC rhythms in CKO SCN slices, fibroblasts and in a functional analogue KO of CRY in Drosophila, even in the absence of rhythmic Per2 transcription due to the loss of CRY as a negative regulator of the oscillation. They have shown that these rhythms, in the absence of CRY, follow the formal definition of circadian rhythms. They attributed these residual PER2::LUC rhythms to the maintenance of oscillation in PER2::LUC stability independent of CRY, by testing the decay kinetics of luciferase activity when translation is inhibited. Moreover, they implicated the kinases CK1and GSK3 to be involved in regulating PER2::LUC post-translational rhythms through kinase inhibitor studies. They concluded that CRY is not necessary for maintaining PER2::LUC rhythms, but plays an important role in reinforcing high-amplitude rhythms when coupled to a proposed "ctyoscillator" likely composed of CK1and GSK3.

Major comments:

The authors have shown sufficient data that under different testing conditions (mice locomotor activity, SCN preps or fibroblasts), behavioral rhythms and PER2::LUC rhythms are still observed in the CRY KO (CKO) cells, contrary to a previous study (Liu et al., 2007). They also indicated limitations to some of the.experimental work. However, there are some parts of the paper that need clarification to support their conclusions.

1.In Fig. 1A, the x-axes of the actograms for WT and CKO are different. While they mentioned this in the figure legend, and described the axis transformation in Fig. S1A, they need a justification statement about why they did this in the results.

2.In an attempt to show conservation of their proposed role for CRY, they tested the model system Drosophila melanogaster where TIMELESS serves as the functional analogue of CRY. While they showed in the figures and described in the text that rhythms still persisted with lower relative amplitude in the TIMELESS-deficient flies, they did not describe any period differences between WT and mutant. Showing the period quantification in Supp. Fig. S2 using the robustly rhythmic datasets, and describing this data in the text, will strengthen their claim.

In Fig. S2B, there is no clear distinction between the representative datasets shown for poorly rhythmic and arrhythmic, i.e. they all appear arrhythmic, without an indicated statistical test. The authors could present better representative data to better reflect the categories.

3.In Fig. 2A, the authors note the lack of rhythmicity in the CKO fibroblasts in the 1st three days at 37oC. How are the conditions here different from fibroblasts in Fig. 1E, where rhythms are seen during the 1st three days in CKO fibroblasts?

1. The authors claimed in the results section- "in contrast and as expected, Per2 mRNA in WT cells varied in phase with co-recorded PER2::LUC oscillations." but Fig. 3C does not show this expected lag between mRNA and protein levels. This needs to be explained

5.In Figs. 5A-B, the PER2::LUC periods in the CKO untreated cells seem to vary significantly between A, B, and C. While this could be due to the high variability in the rhythms that were previously described by the authors, the average periods here seem to be longer than the one reported in Fig. 1F. Are there specific condition differences?

Would additional experiments be essential to support the claims of the paper?

1. There is sufficient experimental data to support the major claims; however some suggested experiments are listed below.

a. If CKO exhibits residual rhythms in PER::LUC, it would be interesting to know how CRY overexpression influences PER2::LUC rhythms, or point to previous reference papers which may have already shown such effects. The prediction would be PER2::LUC levels will still be rhythmic when CRY is overexpressed. What would be the extent of "robustness" conferred by CRY on PER2::LUC rhythms based on CRY KO and overexpression studies?

b. The authors found that CK1and GSK3 contribute to CRY-independent PER2 oscillations by showing that addition of kinase inhibitors affect the PER2::LUC period lengths in WT and CKO in the same manner. It would be interesting to know if a) PER2::LUC stability and b) PER2 phosphorylation status, is affected in WT and CKO in the presence of the inhibitors, or point to previous reference papers which may already have shown such effects.

Are the data and the methods presented in such a way that they can be reproduced?

1. The protocol for the inhibitor treatments are not in the main or supplemental methods.

Are the experiments adequately replicated and statistical analysis adequate?

1. All experiments had the sufficient number of technical and biological replicates to make valid statistical analyses. For Fig. S2, the authors used RAIN to assess rhythmicity in WT and mutant flies, but it is not clear whether the different categories (rhythmic, poorly rhythmic, and arrhythmic) were based on amplitude differences alone, or a combination of amplitude and p-values as determined by RAIN.

Minor comments:

1. Other minor comments

Main Text:

p3, line 62; p12, line l32: It doesn't seem necessary or appropriate to cite the dictionary for the definition of robust.

p4, line l87: "~20 h" rhythms instead of "~20h-hour"

p3, line 70; p5, line 121; p14, line 380; p16, line 416 and p18, line 458: Close parentheses have been doubled in parenthetical references.

p14, line 363: "crassa" instead of "Crassa"

p17, line 430: "Sigma" instead of "sigma"

p18, lines 464 and 483; p20, line 521: put a space between numerical values and units, to be consistent with other entries

p19, line 488: "luciferase" instead of Luciferase

p20, line 512: "Cell Signaling" instead of "cell signalling"

p20, line 526: "single" instead of "Single"

Main figures:

Fig. 2 p37, line 921: close parenthesis was doubled on "red"

Fig. 4 p41, line 989: "0.1 mM" instead of "0.1 mM" for consistency throughout text

Supplementary text:

line 171: "30 mM HEPES" instead of "30mM HEPES"

line 184: "Cell Signaling" instead of "cell signalling"

Supplementary figures:

Fig. S2A "Drosophila melanogaster" instead of "Drosophila Melanogaster"

Significance

This paper revisits the previously proposed idea that rhythmic expression of central TTFL components is not essential for circadian timekeeping to persist. However, this paper does not add a significant advance in the understanding of the underlying reasons behind sustained clock protein rhythmicity like PER in the absence of CRY, since such mechanisms in functional analogs have been shown in other systems, like Neurospora (Larrondo et al., 2015). However, this paper does clarify some issues in the field, such as discrepancies between behavioral and cellular rhythms observed in CKO mice, leading future researchers to examine closely the conditions of their CKO rhythmic assays before making conclusions pertaining to rhythmicity. The identification of the kinases as components of the proposed cytosolic oscillator (cytoscillator) needs further validation, but this is perhaps beyond the scope of the paper. The data provides incremental evidence for the existence of a cytoscillator, but opens up opportunities to identify other players, like phosphatases, to establish the connection between the central TTFL and the proposed cytoscillator.

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

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Referee #2

Evidence, reproducibility and clarity

In the canonical model of the mammalian circadian system, transcription factors, BMAL1/CLOCK, drive transcription of Cry and Per genes and CRY and PER proteins repress the BMAL1/CLOCK activity to close the feedback loop in a circadian cycle. The dominant opinion was that CRY1 and CRY2 are essential repressors of the mammalian circadian system. However, this was challenged by persistent bioluminescence rhythms observed in SCN slices derived from Cry-null mice (Maywood et al., 2011 PNAS) and then by persistent behavior rhythms shown by the Cry1 and Cry2 double knockout mice if they are synchronized under constant light prior to free running in the dark (Ono et al., 2013 PLOS One). In the manuscript, the authors first confirmed behavioral and molecular rhythms in the Cry1/Cry2- deficient mice and then provided evidence to suggest the rhythms of Per2:LUC and Nr1d1:LUC in CKOs are generated from the cytoplasmic oscillator instead of the well-studied transcription and translation feedback loop: Constant Per2 transcription driven by BMAL1/CLOCK plus rhythmic degradation of the PER protein result in a rhythmic PER2 level in the absence of both Cry1 and Cry2, which suggests a connection between the classic transcription- and translation-based negative feedback loops and non-canonical oscillators.

Major points:

Line 38-39, "Challenging this interpretation, however, we find evidence for persistent circadian rhythms in mouse behavior and cellular PER2 levels when CRY is absent." The rhythmic behavioral phenotype of cry1 and cry2 double knockout mice was first documented by Ono et al., 2013 PLOS ONE, in which eight cry1 and cry2 double knockout mice after synchronization in the light displayed circadian periods with different lengths and qualities. The paper reported two period lengths from the Cry mutant mice: "An eye-fitted regression line revealed that the mean shorter period was 22.86+/-0.4 h (n= 8) and the mean longer period was 24.66+/-0.2 h (n =9). The difference of two periods was statistically significant (p, 0.01).", either of which is quite different from the ~16.5 hr period in Figure 1B of the manuscript. A brief discussion on the period difference between studies will be helpful for readers to understand. Period information from the individual mouse should be calculated and shown since big period variations exist among CKO mice (Ono et al., 2013 PLOS One).

The behavioral phenotype of Cry-null mice and luminescence from their SCNs are robustly rhythmic while fibroblasts derived from these mice only produce rhythms with very low amplitudes compared with those in WT, which may reflect the difference between the SCN's rhythm and peripheral clocks. The behavioral phenotype is supposed to be controlled mainly by SCN. However, most molecular analyses in the work were done with MEF and lung fibroblasts. These tissues may not be the best representative of the behavioral phenotype of the CKO mice.

Stronger evidence is needed to fully exclude the possibility that in CKO cells, the rhythm is not generated by PERs' compensation for the loss of Crys to repress BMAL1 and CLOCK. Since the rhythms of Per:LUC or Nr1d1:LUC (Figures 3D and S3E) are much weaker than those in WT, molecular analyses might not be sensitive enough to reflect the changes across a circadian cycle in the CKOs if the TTFL still occurs. CLOCKΔ19 mutant mice have a ~4 hr longer period than WT (Antoch et al., 1997 Cell; King et al., 1997 Cell). CLOCKΔ19; CKO cells or mice should be very helpful to address the question. Periods of Per:LUC and Nr1d1:LUC from the CLOCKΔ19; CKO should be similar to those in the CKO alone if the transcription feedback does not contribute to the their oscillations.

Lines 51-52, "PER/CRY-mediated negative feedback is dispensable for mammalian circadian timekeeping" and lines 310-311, "We found that transcriptional feedback in the canonical TTFL clock model is dispensable for cell-autonomous circadian timekeeping in animal and cellular models." The authors have not excluded the possibility that the rhythmic behaviors of the CKO mice are derived from the PERs' compensation for the role of Crys in the feedback loop of the circadian clock in the SCN. In the fibroblasts, only two genes, Per2 and Nr1d1, have been studied in the work, which cannot be simply expanded to the thousands of circadian controlled genes. Also amplitudes of PER2:LUC and NR1D1:LUC in the CKOs are much lower than those in WT and no evidence has been provided to show that their weak rhythms are biologically relevant.

Minor points:

Lines 66-67, "...(Dunlap, 1999; Reppert and Weaver, 2002; Takahashi, 2016)." to "... (reviewed in Dunlap, 1999; Reppert and Weaver, 2002; Takahashi, 2016)."

Line 70, "...((Liu et al., 2008..." to "...(Liu et al., 2008..."

Lines 174-175, "Considering recent reports that transcriptional feedback repression is not absolutely required for circadian rhythms in the activity of FRQ...". Larrondo et al., 2015 paper says "however, in such ∆fwd-1 cells, the amount of FRQ still oscillated, the result of cyclic transcription of frq and reinitiation of FRQ synthesis." The point of the paper is "we unveiled an unexpected uncoupling between negative element half-life and circadian period determination." instead of "...transcriptional feedback repression is not absolutely required for circadian rhythms in the activity of FRQ,"

Lines 249-252, "CKO cells exhibit no rhythm in Per2 mRNA (Figure 3C, D), nor do they show a rhythm in global translational rate (Figure S4A, B), nor did we observe any interaction between BMAL1 and S6K/eIF4 as occurs in WT cells (Lipton et al, 2015) (Figure S4C)." In figures 3D and S3E, in CKO and CPKO cells the Per2:LUC data without fitting look better than that of Nr1d1:LUC. But the Nr1d1:LUC rhythm became clear after fitting the raw data. So to better visualize the low amplitude rhythm, if any, of Per2:LUC and compare with Nr1d1:LUC, fitted the Per2:LUC data in CKOs and CPKOs in Figure 3D and S3E should be shown as what has been done to Nr1d1:LUC.

Lines 258-259, "much less than the half-life of luciferase expressed in fibroblasts under a constitutive promoter" In figure S4D, the y-axis of the PER2::LUC is ~800 while the y-axis of the SV40::LUC is ~600000. The over-expressed LUC by the SV40 promoter might saturate the degradation system in the cell so the comparison is not fair. A weaker promoter with the level similar to Per2 should be used to make the comparison.

Line 430, "sigma" to "Sigma".

In figure S2, the classification of rhythms in Drosophila is not clear since even the "Robustly rhythmic" ones have high background noise. Detrending or fitting the data might be able to improve the quality of the rhythms prior to classification.

In figure S3B, the original blots for Per2 including Input and IP should be shown.

Supplemental information

Line 44, "...(reviewed in (Lakin-Thomas,..." to "...(reviewed in Lakin-Thomas,..."

Line 188, "Period CDS", the full name of CDS should be provided the first time it appearances.

Significance

The work suggests a link between the TTFL and non-canonical oscillators, which should be interesting to the circadian field.

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:

This interesting study by Putker et al. showed that circadian rhythmicity persists in several typical circadian assay systems lacking Cry, including Cry knockout mouse behavior and gene expression in Cry knockout fibroblasts. They further demonstrated weak but significant circadian rhythmicity in Cry- and Per- knockout cells. Cry- (and potentially Per-)-independent oscillations are temperature compensated, and CKId/e still has a role in the period regulation of Cry-independent oscillations.

Major comments:

1) The authors propose that the essential role of mammalian Cryptochrome is to bring the robust oscillation. As the authors analyze in many parts, the robustness of oscillation can be validated by the (relative) amplitude and phase/period variation, both of which should be affected significantly by the method for cell synchronization. Unfortunately, the method for synchronization is not adequately written in this version of supplementary information. This reviewer has no objection to the "iterative refinement of the synchronization protocol" but at least the correspondence between which methods were used in which experiments needs to be clearly explained. The detailed method may be found in the thesis of Dr. Wong, but the methods used in this manuscript need to be detailed within this manuscript.

2) The authors revealed that CKO mice have apparent behavioral rhythmicity under the condition of LL>DD. This is an intriguing finding. However, it should be carefully evaluated whether this rhythmicity (16 hr cycle) is the direct consequence of circadian rhythmicity observed in CKO and CPKO cells (24 hr cycle) because the period length is much different. Is it possible to induce the 16 hr periodicity in CKO mice behavior by 16 hr-L:16 hr-D cycle? Would it be a plausible another possibility that the 16 hr rhythmicity is the mice version of internal desynchronization or another type of methamphetamine-induced-oscillation/food-entrainable-oscillattion?

3) The authors proposed that CKId/e at least in part is the component of cytoscillator (Fig. 5D), and turnover control of PER (likely to be controlled by CKId/e) may be an interaction point between cytoscillator and canonical circadian TTFL (Fig. 4). Strictly speaking, this model is not directly supported by the experimental setting of the current manuscript. The contribution of CKId/e is evaluated in the presence of PER by monitoring the canonical TTFL output (i.e. PER2::LUC); thus it is not clear whether the kinase determines the period of cytoscillator. It would be valuable to ask whether the PF and CHIR have the period-lengthening effect on the Nrd1:LUC in the CPKO cell.

Minor comments:

4) The authors argue that the CKO cells' rhythmicity is entrained by the temperature cycle (Fig. 2C). Because the data of CKO cell only shows one peak after the release of constant temperature phase, it is difficult to conclude whether the cell is entrained or just respond to the final temperature shift.

5) It would be useful for readers to provide information on the known phenotype of TIMELESS knockout flies; TIM is widely accepted as an essential component of the circadian clock in flies; are there any studies showing the presence of circadian rhythmicity in Tim-knockout flies (even if it is an oscillation seen in limited conditions, such as the neonatal SCN rhythm in mammalian Cry knockout)?

5) Figure 3C shows that the amount of PER2::LUC mRNA changes ~2 fold between time = 0 hr and 24 hr in the CKO cell. This amplitude is similar to that observed in WT cell although the peak phase is different. Does the PER2::LUC mRNA level show the oscillation in CKO cells?

6) Figure 3D: the authors discuss the amplitude and variation (whether the signal is noisier or not) of reporter luciferase expression between different cell lines. However, a huge difference in the luciferase signal can be observed even in the detrended bioluminescence plot. This reviewer concerns that some of the phenotypes of CKO and CPKO MEF reflect the lower transfection efficiency of the reporter gene, not the nature of circadian oscillators of these cell lines.

Significance

Although Cryptochrome (Cry) has been considered a central component of the mammalian circadian clock, several studies have shown that circadian rhythms are maintained in the absence of Cry, including in the neonate SCN and red blood cells. Thus, although the need for Cry as a circadian oscillator has been debated, its essential role as a circadian oscillator remains established, at least in the cell-autonomous clock driven by the TTFL. This study provides additional evidence that the circadian rhythmicity can persist in the absence of Cry.

More general context, the presence of a non-TTFL circadian oscillator has been one of the major topics in the field of circadian clocks except for the cyanobacteria. In mammals, the authors' and other groups lead the finding of circadian oscillation in the absence of canonical TTFL by showing the redox cycle in red blood cells (O'Neil, Nature 2011). The presence of circadian oscillation in the absence of Bmal1 is also reported recently(Ray, Science 2020). Bmal1(-CLOCK), CRY, and PER compose the core mechanism of canonical circadian TTFL; thus, this manuscript put another layer of evidence for the non-TTFL circadian oscillation in mammals.

Overall, the manuscript reports several surprising results that will receive considerable attention from the circadian community.

This reviewer has expertise in the field of mammalian circadian clocks, including genomics, biochemistry, and mice's behavior analysis.

Reviewer #3:

Unlike other ionotropic glutamate receptors, GluD2 is not gated by glutamate. No specific or high-affinity chemical modulators that induce channel activity exist for this receptor--as such, it’s role as a functional channel has been questioned. To address this challenge, the authors have utilized a previously characterized photoswitchable tethered ligand (PTL) called MAGu to target a very non-specific blocker (pentamidine) to a new ion channel target (the GluD2 receptor). This approach (using this exact PTL) has been used to target knock-in cysteine mutants of the GABAA receptor in mouse brain slices and in vivo in an awake, behaving mouse. Based on this precedent, it is not unreasonable to believe that this tool could similarly be used for the GluD2 receptor (which would be a significant advance in the field for understanding the physiological role of this protein in disease), although the authors only characterized MAGu response against GluD2 in heterologous cell culture within this manuscript. Because the GluD2 receptor is not ligand-activated in the traditional sense, the authors have exploited a previously characterized constitutively open point mutant (L654T) as a background to test different photoactivatable GluD2 cysteine mutants and have nicely demonstrated a reversible current block response in the presence of purple (380 nm = "cis-" = channel "on") and green (535 nm = "trans-" = channel "off") light. The authors have numerous publications and experience in the photopharmacology of ion channels, and the characterization data here look solid.

That said, there are a few questions that should potentially be addressed:

1) How does MAGu work on the cysteine-engineered receptor that would presumably be used for future in vivo studies? Because the GluD2-I677C point mutant (lacking the L654T background) does not show current, the authors use the known effect of mGlu1 receptor agonism as a readout of GluD2-I677C activity in response to light and only see a 23% decrease in mGlu1 current - is this very small effect physiologically significant or to be expected? It seems like MAGu might be a useful tool to modulate GluD2 in Lurcher mice (which harbor the L654T mutation), but it is hard to know what the probe efficacy and usefulness is for evaluating the physiology of the WT GluD2 receptor in the absence of a way to measure a direct functional effect on the channel. How else might this be addressed?

2) PTLs have been shown to generate a high local concentration of ligand to accelerate pharmacological response (and in this case, provide some level of specificity for a very non-specific, greasy cation), but it is hard to rationalize "absolute" pharmacological specificity claimed by the authors (line 35, 211). At the mid-micromolar concentrations required to elicit response, it seems unlikely that MAGu will not react with any other extracellular cysteines present in cells. Further, the guanidinium group by itself will certainly not direct the maleimide reactivity towards GluD2 over any other cation channel or electronegative protein surface. The language of this claim should be modified in the absence of other types of specificity assays.

Minor Comments:

1) Provide description of the step-by-step protocol for Fig. 2C (or label "washout" of pentamidine)

2) Why does normalized current plateau at 80% for 535 nm (Fig. 4B)?

3) There is a current biorxiv paper reporting the GluD2 structure. https://www.biorxiv.org/content/10.1101/2020.01.10.902072v2.full.pdf If this is published during the course of this review, it would be interesting for the authors to comment on how this compares to their homology model and if it makes sense with respect to their mutagenesis experiments.

Reviewer #2:

The present manuscript investigates the development of a photo-activatable pore blocker to block the glutamate receptor delta receptor (GluD) ion channel as a potential tool to study this receptor in vitro and in vivo. GluD shares structural homology to other members of the family and plays key roles in synapse formation and signaling. However, in contrast to other members of the family, it does not have a clear ionotropic function - complicating defining how it contributes to synaptic function in vivo. Many labs have studied GluD and have provided key insights into its function and role. Still, the availability of new a tool to study and clarify its function has high potential.

The manuscript lays out quite well, with some minor quibbles (see below), the issues. Proper controls are carried out to define the specificity of the action of the photo-switchable MAGu and how it can alter membrane currents and how it might work. The potential for a photo-switchable pore blocker to study the role of the ion channel in GluD is extremely high. I do have some concerns about signal-to-noise, since the pore block by trans-MAGu is only a fraction of total presumed current through GluD. In addition, how to introduce a specific cysteine in vivo will not be trivial. Still, overall this is an important manuscript that introduces an interesting strategy to study and further clarify GluD in the brain.

1) Abstract/Introduction. It would be helpful to define early and explicitly what the photoswitchable functional strategy is - that it is working via a pore block mechanism. In the Abstract, for example, instead of calling it '...a photoswitchable ligand.' how about just '...a photoswitchable pore blocker." Once I realized the general functional strategy (at the beginning of description of results, where it was explicitly stated), everything became clearer. The functional strategy, that you are generating a photoswitchable pore blocker, should also be explicitly stated in the Introduction, where right now it is touched on but not explicitly stated.

2) Figure 2C. The extent of block for photoswitching is being quantified relative to that for pentamidine, which is reasonable. However, for pentamidine, what is the concentration used for the experiments? Where is it at on the concentration-block curve for pentamidine? Presumably, if a complete block the leak current should go to zero and hence the efficacy of the photoswitching blocker would be less (e.g., Figure 4B). Please clarify.

3) Figure 4A. Would be nice to see difference currents and perhaps to contrast to what is shown in Figure 2A. This would clarify the 'voltage-independence' of action for those unfamiliar.

4) Figure 4D. Not clear how the 'ion channel' or red/green pore was generated? Is this from the structure or from some modeling? Please add details. This is an interesting figure but it is also somewhat speculative, I think, but needs more details to understand its basis. One question is what is driving the positioning of the trans MAGu? Is it being fixed? And what is driving the change in the coloration - presumed pore blocking by trans MAGu?

Minor Comments:

1) Figure 1. Minor point. Technically, there is no transmembrane segment 2 (TM2) in iGluRs. M2 is a pore loop, like the P loop in K+ channels, and enters and exits on the same side of the membrane - and does not span the membrane (and hence not a transmembrane segment). Simple solution would be to just rename TM2 to M2 leaving TM1, TM3, and TM4 as is and just noting somewhere in Figure legend that M2 is a non-membrane spanning pore loop.

2) Figure 2D. Minor point. Although I understand the intent of figure, it is Very hard to discern what is being shown. Might be helpful to remove the 'red' subunit?

Reviewer #1:

The study by Lemoine and colleagues demonstrates a novel chemogenetic tool to probe ion channel function of GluD2 in HEK cells. By introducing cysteine mutations and engineering a photoswitchable ligand, ionic current carried by constitutively-open GluD2 mutant channels was reversibly decreased by light. Further, GluD2 current produced by activation of mGluRs was partially reduced by light. This tool has the potential to be very powerful to advance the understanding of GluD2 channel function in neurons.

Major:

1) The introduction and abstract are rather general and antiquated, to the disservice of the readers. It may be time to move away from the notion that the ion channel function of GluD is debated. The authors have published many elegant studies demonstrating ion channel function. By appearances of the literature, the interpretation of these studies are not contested. In addition to pharmacology, ion channel function of GluD has been demonstrated using selective genetic strategies (e.g. Ady et al., 2013; Benamer et al., 2018; Gantz et al., 2020). To this end, lines 28-29, 51, 55, & 73-75 should be changed. It does not seem fitting to state "direct evidence for ionotropic activity of GluD in neuronal setting [sic] is lacking" provided the studies referenced above. Broadly, the readers would benefit from restructuring of the introduction and abstract to state the specific issue addressed by the present study (i.e. the lack of specific antagonists/pore blockers to study GluD without affecting other iGluRs) and highlight the potential application of the ligand.

2) This photoswitchable ligand MAGu has great potential to probe GluD channel function in neurons, although the present study stops short of demonstrating its utility in neurons. Lines 211-212 state that the WT receptor is insensitive to MAGu, but it is not clear where those data are presented. It would be beneficial to show the magnitude of the DHPG-induced current in WT GluD2-expressing cells before and after addition of MAGu to address the possibility that MAGu affects the current irrespective of trans- or cis- conformation. It is also not clear how MAGu will be selective for site-specific conjugation when introduced in a neuronal setting. Is it expected MAGu will react with any available cysteine? It would be helpful to discuss possible limitations going forward towards use in neurons.

3) The data show convincingly that 380 nm light unblocks MAGu-induced GluD2 block by darkness or 535 nm light. But it is not clear how trans-MAGu affected leak current from GluD2 Lurcher mutant channels. In Figure 2C I677C, there is still substantial leak in 535 nm. The quantification in Figure 2C (% photoswitching) shows the % of I-Blockphoto over I-Blockpenta, but the arrows in the right-hand trace, it would appear I-Blockphoto is actually the current unblocked. It would be helpful to quantify the amount of leak current blocked by trans-MAGu. Additional discussion as the structural basis for incomplete block may also be helpful.

Minor:

1) Recommendation to include model system in the title ("in expression systems" or "in HEK cells", vel sim)

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.

This manuscript was assessed by three reviewers. After the completion of their reviews, the editor and reviewers discussed the paper and arrived at the following consensus review. For transparency, the individual reviews are also presented.

Summary:

Unlike other ionotropic glutamate receptors, GluD2 is not gated by glutamate. No specific or high-affinity chemical modulators that induce channel activity exist for this receptor. To address this challenge, the authors used a previously characterized photoswitchable tethered ligand (PTL) called MAGu to target a very non-specific blocker (pentamidine) to a new ion channel target (the GluD2 receptor). This approach (using this exact PTL) has been used to target knock-in cysteine mutants of the GABAA receptor in mouse brain slices and in vivo in an awake, behaving mouse. Based on this precedent, it is not unreasonable to believe that this tool could similarly be used for the GluD2 receptor, which would be a significant advance in the field for understanding the physiological role of this protein in disease.

The original reviews, below, reflect the reviewers’ initial enthusiasm for the potential of the approach to study GluD2 channels. In the discussion, all reviewers agreed that the issue of signal-to-noise is critical and that additional experiments are essential to demonstrate that the MAGu response will be sufficient for physiological studies in vivo.

Reviewer #2:

I very much like the general idea of this paper, but my opinion is that this is not an idea that can/should be applied to these data. As elaborated below, the ABIDE data are from numerous sites with different scanners, imaging acquisition sequences and parameters, sample ascertainment, etc, The methods used in the current paper rely on there not being such heterogeneity; and its presence can either render true ASD-related deviance invisible, or create an illusion of ASD-related deviance where there is none. Such heterogeneity is, of course, problematic for more conventional approaches; but is far more problematic for the methods proposed here.

Major Issues and Questions:

1) The authors are critical of case-control models but do not present an alternative to dealing with the heterogeneity in the data. Indeed, linear models are inadequate to deal with the heterogeneity in the ABIDE data given the lack of overlap in the data for different sites. But the normative approach presented here seems to not deal with the problem at all, potentially transforming what would be taken out by a nuisance variable into an alteration in ASD-related deviance.

2) The sparsity of the data beyond childhood is extremely problematic for this approach. The approach of taking data in one-year bins requires large amounts of data within each bin to make the means and standard deviations reliable. By the teenage years, this is clearly not the case. The authors limit age bins to having at least 3 control points; this is clearly wildly insufficient, and would be even if there were no issues with site heterogeneity. Conventional linear models are to be preferred to normative models under these conditions.

3) The comparison of results from a case-control model versus a normative model seems misleading. A case-control model approach requires a specification of the age at which the comparison is made. This is not provided, leading one to suspect that the age data were not centered, but were absolute, and thus the differences were essentially projecting backwards to birth. (This is, I believe, a common mistake.) The model specification is also completely lacking. Moreover, a case-control approach does not preclude the possibility of centering the data at different ages (as in e.g. Khundrakpam et al. (2017)). Between this and the problems with heterogeneity for the normative models, it is unclear how to interpret these results.

4) The idea that individuals that are more than 2 stddevs away from the mean of the controls are outliers and should be eliminated from the analysis seems mistaken. If all individuals with ASD are substantially far from the mean of the controls, they are clearly not to be treated as outliers.

5) The impact statement claims that "normative modelling has the potential to isolate specific highly deviant subsets of individuals with ASD, which will have implications for understanding the underlying mechanisms and bring clinical impact closer"; there is no indication that that is the case. The normative model has identified primarily children, and has identified nothing in particular about those children. Case-control models have done the same.

6) It appears to this reviewer that this paper outlines an approach which could be worthwhile in a data set without massive heterogeneity, but within the context of the ABIDE data actually seems harmful.

Reviewer #1:

This paper describes the impact of outliers in normative cortical thickness (CT) measurements when examining those suffering from autism spectrum disorder (ASD). The authors used the ABIDE sample and binned subjects by age, and assessed outliers as a function of a "w-score" which they estimated across CT parcellations across the entire cortex. They then demonstrate that cortical thickness differences that can ascribed to ASD can essentially be attributed to a small number of outliers within the sample. They also demonstrate that this w-score may be sensitive to clinical variables as well.

Overall, it is unclear to me what the exact goal of the work is: To describe the anatomy of ASD better? To subtype? Or is there another "take-home" message of this paper? I would imagine that the case-control differences in most neurodevelopmental disorders with high heterogeneity and high variability would demonstrate a similar kind of trend. And thus, at the end of the day, I am not sure how much this technique advanced our understanding of ASD.

Issues and Questions:

1) It is unclear from the methods how the authors deal with motion and image quality. Recent work by Pardoe and Bedford demonstrate the importance of dealing with this issue, particularly in the context of the ABIDE sample. This would likely have a significant impact on any of the results. It's unclear if the use of the Euler index at the extremes of the distribution of the dataset being used is sufficient. How did the authors come up with their Euler number cut-off?

2) The W-score could use a much better explanation. It is not clear to me as to what it is and how this should be interpreted. The lack of information regarding the number of age-bins used also makes interpreting these findings confusing in my mind.

3) The authors report that, "The median number of brain regions per subject with a significant p-value was 1 (out of 308), indicating that the w-score provides a robust measure of atypicality." I guess this could be true, but given the variation in normative ageing and development, I suspect this would also be true of a large number of TD children. That being the case, would it be worth doing a permutation test to determine the threshold of how man "atypical" areas one could expect by chance?

4) The authors note "Unfortunately, despite a significant female subgroup, the age-wise binning greatly reduced the number of bins with enough data-points in the female group." I understand that this could indeed be a problem. However, I think it would be good for the authors to provide more details. Potentially a histogram to demonstrate the issue. My feeling is that with sex difference with respect to ASD, the more information that could be provided the better. Overall, it is unclear to me as to how useful a sex-specific analysis may be in this particular context given the sample sizes available in ABIDE.

5) Results, page 8: "Because we also had computed w-scores from our normative age-modelling approach, we identified specific 'statistical outlier' patients for each individual region with w-scores > 2 standard deviations from typical norms and excluded them from the case-control analysis."

I'm not sure I agree with the premise of this statement. First, it is hard to know without seeing all of the data, but based on Fig 1, it seems that there are ASD individuals that fall on both sides of this distribution. So if there are effect sizes that can be gleaned, this would be in spite of the variability. Second, it would be paramount to determine how many people are outliers-by-region. This, in and of itself, would be useful information. If a significant proportion of individuals can be identified as outliers, this suggests that variability is the norm rather than an exception. I'm skeptical as to whether you get interesting information from removing these individuals from analyses.

6) Result, page 9: "While the normative modelling approach can be sensitive to different pathology." I don't think you're capturing anything interesting about pathology with this method, especially as it pertains to CT values.

7) Result, page 9-10: I'm still confused by this notion of atypicality. Presumably this suggests that 5-10% of all ASDs are more than 2SDs from a normative distribution. But is this at both tails of the distribution? There are significant interpretational issues with this. thus, it is imperative on the authors to do a better job of describing these distributions.

8) Part of the rationale of this paper is that using the w-score is far more robust than using simple CT values. I'm sure that residualized CT values could have been used for any of these analyses. If that were to be done how would this change the results?

Minor comments and suggestions on presentation:

1) While this paper has some merits, I found it hard to read. There is not a clear delineation between the methods and the results, and some methodological considerations are written into the results section and vice-versa.

2) In the introduction, the authors use the word "deviance" to describe what appears more to me like age-related variation and heterogeneity in ASD. Deviance may be too strong a term and easily mis-interpretable. I would suggest replacing it with something a bit more like variation. Also, the work at the institution of the main author (for example by Baron-Cohen and authors) really champions the use of terms like "neurotypical" rather normally developing. I think, in general, the authors may want to take their cues from this type of language.

3) This passage in the Introduction need of references. The work by Hong (in Boris Bernhardt's group), Bedford (in Mallar Chakravarty's group), Schuetze (in Signe Bray's group), and Meng-Chuan Lai all come to mind.

"Even within mesoscopic levels of analysis such as examining brain endophenotypes, heterogeneity is the rule rather than the exception (Ecker, 2017). At the level of structural brain variation, neuroimaging studies have identified various neuroanatomical features that might help identify individuals with autism or reveal elements of a common underlying biology (Ecker, 2017). However, the vast neuroimaging literature is also considerably inconsistent, with reports of hypo- or hyper-connectivity, cortical thinning versus increased grey or white matter, brain overgrowth, arrested growth, etc., leaving stunted progress towards understanding mechanisms driving cortical pathophysiology in ASD."

4) I found the Discussion missed the mark. It was mostly written as a rehash of the results, with no real biological interpretation. There is not a sufficient examination of the relationship of these findings to other important papers (Kundrakpham, Bedford, Hong, Ecker, Hyde, Lange, etc...).

5) Figure 3 - The colour bars should be labelled.

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 4 of the preprint: https://www.biorxiv.org/content/10.1101/252593v4

Summary:

This paper uses data from the Autism Brain Imaging Data Exchange (ABIDE) to model the relationship between cortical thickness in different brain regions and patients with autism spectrum disorders (ASD) compared to neurotypical controls. The reviewers appreciated the goals and approach of this paper, but, as described below, had questions about the suitability of the data for this analysis, the ways in which the data were processed, the way in which the results were interpreted, and the significance of these findings for understanding autism spectrum disorders.

Reviewer #3:

The methods used by the authors seem like potentially really useful tools for research on neural activity related to sequences of stimuli. We were excited to see that a new toolbox might be available for these sorts of problems, which are widespread. The authors touch on a number of interesting scenarios and raise relevant issues related to cross-validation and inference of statistical significance. However, given (1) the paucity of code that they've posted, and its specificity to specific exact data and (2) the large literature on latent variable models combined with surrogate data for significance testing, I would hesitate to call TDLM a "framework". Moreover, in trying to present it in this generic way, the authors have made it more difficult to understand exactly what they are doing.

Overall: This paper presents a novel approach for detecting sequential patterns in neural data however it needs more context. What's the contribution overall? How and why is this analysis technique better than say Bayesian template matching? Why is it so difficult to understand the details of the method?

Major Concerns:

The first and most important problem with this paper is that it is intended (it appears) to be a more detailed and enhanced retelling of the author's 2019 Cell paper. If this is the case, then it's important that it also be clearer and easier to read and understand than that one was. The authors should follow the normal tradition in computational papers:

Present a clear and thorough explanation of one use of the method (i.e., MEG observations with discrete stimuli), then present the next approach (i.e., sequences?) with all the details necessary to understand it.

The authors should start each section with a mathematical explanation of the X's - the equation(s) that describes how they are derived from specific data. Much of the discussion of cross validation actually refers to this mapping.

Equation 5 also needs a clearer explanation - it would be better to write it as a sum of matrices (because that is clearer) than with the strange "vec" notation. And TAUTO, TF and TR should be described properly - TAUTO is "the identity matrix", TF and TR are "shift matrices, with ones on the first upper and lower off diagonals".

The cross validation schemes need a clear description. Preferably using something like a LaTeX "algorithm" box so that they are precisely explained.

Recognizing the need to balance readability for a general reader and interest, perhaps the details could be given for the first few problems, and then for subsequent results, the detail could go into a Methods section. Alternatively, the methods section could be done away with (though some things, such as the MEG data acquisition methods are reasonably in the methods).

Usually, we think about latent variable model problems from a generative perspective. The approach taken in this paper seems to be similar to a Kalman filter with a multinomial observation (which would be equivalent to the logistic regression?), but it's unclear. Making the connection to the extensive literature on dynamical latent variable models would be helpful.

Minor concerns:

1) Many of the figures, and some of the text are from the 2019 Cell paper. The methods text is copied verbatim without citation.

2) The TLDM model is presented without context or comparison to other computational approaches employed to identify sequences. Is it also used in the 2016 Kurth-Nelson paper? How does it compare, e.g., to Bayesian template matching (in the case of hippocampal data)?

3) Cite literature from recent systems neuroscience using hidden Markov models and related discrete state space approaches on neural activity.

4) How does this method deal with a long sequence for which the intra-sequences have variance in their delta t's? Or data where the observations have some temporal lag relative to each other?

5) In the "sequences of sequences" section, the authors talk about combining states into meta states. But then the example they give, it appears they just use their vanilla approach. This whole section belongs in a different place than a "supplemental note". The data need proper attribution, an IACUC/ethics statement, etc.

6) While code can be useful, it is not archival in the same way equations are. Supplementary Note 1 should be in the Methods, and needs to be rewritten in such a way that it explains the steps (i.e., in an algorithm box) rather than just using code. Moreover, when the data generated via this code is used in the text, this section in the methods can be mentioned/linked.

Reviewer #2:

This paper addresses the important overall issue of how to detect and quantify sequential structure in neural activity. Such sequences have been studied in the rodent hippocampus for decades, but it has recently become possible to detect them in human MEG (and perhaps even fMRI) data, generating much current excitement and promise in bringing together these fields.

In this paper, the authors examine and develop in more detail the method previously published in their groundbreaking MEG paper (Liu et al. 2019). The authors demonstrate that by aiming their method at the level of decoded neural data (rather than the sensor-level data) it can be applied to a wide range of data types and settings, such as rodent ephys data, stimulating cross-fertilization. This generality is a strength and distinguishes this work from the typically ad hoc (study-specific) methods that are the norm; this paper could be a first step towards a more domain-general sequence detection method. A further strength is that the general linear modeling framework lends itself well to regressing out potential confounds such as autocorrelations, as the authors show.

However, our enthusiasm for the paper is limited by several overall issues:

1) It seems a major claim is that the current method is somehow superior to other methods (e.g. from the abstract: "designed to take care of confounds" implying that other methods do not do this, and "maximize sequence detection ability" implying that other methods are less effective at detection). But there is very little actual comparison with other methods made to substantiate this claim, particularly for sequences of more than two states which have been extensively used in the rodent replay literature (see Tingley and Peyrache, Proc Royal Soc B 2020 for a recent review of the rodent methods; different shuffling procedures are applied to identify sequenceness, see e.g. Farooq et al. Neuron 2019 and Foster, Ann Rev Neurosci 2017). The authors should compare their method to some others in order to support these claims, or at a minimum discuss how their method relates to/improves upon the state of the art.

2) The scope or generality of the proposed method should be made more explicit in a number of ways. First, it seems the major example is from MEG data with a small number of discrete states; how does the method handle continuous variables and larger state spaces? (The rodent ephys example could potentially address this but not enough detail was provided to understand what was done; see specific comments below.) Second, it appears this method describes sequenceness for a large chunk of data, but cannot tell whether an individual event (such as a hippocampal sharp wave-ripple and associated spiking) forms a sequence not. Third, there is some inconsistency in the terminology regarding scope: are the authors aiming to detect any kind of temporal structure in neural activity (first sentence of "Overview of TDLM" section) which would include oscillations, or only sequences? These are not fatal issues but should be clearly delineated.

3) The inference part of the work is potentially very valuable because this is an area that has been well studied in GLM/multiple regression type problems. However, the authors limit themselves to asking "first-order" sequence questions (i.e. whether observed sequenceness is different from random) when key questions -- including whether or not there is evidence of replay -- are actually "second-order" questions because they require a comparison of sequenceness across two conditions (e.g. pre-task and post-task; I'm borrowing this terminology from van der Meer et al. Proc Royal Soc B 2020). The authors should address how to make this kind of comparison using their method.

Minor Comments:

1) Some discussion of grounding the question of what is considered a sequence should be included. What may look like a confound to a modeler may or may not be impacting downstream readout neurons; without access to a neural readout it is not a priori clear what our statistical methods "should" be detecting.

2) The abstract emphasizes hippocampal replay, but no actual analysis of this is done. I don't think performing such analysis is necessary (although it would be a good way to compare this method to others) but the two should be more aligned.

3) In the "Statistical Inference" section, the authors stated "Permuting time destroys the temporal smoothness of neural data, creating an artificially narrow null distribution...". Did the authors try shift shuffles, which shifts the time dimension of each row rather than randomly permuting it, hence breaking the relationship between variables but keeping their autocorrelation?

4) In the "Regularization" section, it is hard to tell how L1 outperforms L2 in terms of detecting sequenceness without benchmarking them with ground truth. Are the authors doing this by quantifying decoding performance on withheld task data? Van der Meer et al. Hippocampus 2017 examine this issue for hippocampal place cell data.

5) As a rodent ephys person I was excited about the application to hippocampal place cell data, but I couldn't understand Figure 5d and the associated supplementary description. In order for me to evaluate this component of the ms, substantially more explanation is needed on how the data is preprocessed and arranged, and what the analysis pipeline looks like. For instance, Is the left plot in Fig. 5d an average of all pairwise sequences (each decoded location with its neighbors)? And the right plot is the timescale at which this sequence repeats? If so, the repeat frequency should be at rat theta frequency or a little faster (because of phase precession) so I would expect 9 or 10 Hz max -- surprised to see what looks like 12 Hz? In the Supplementary note, I found the discussion about running direction distracting, wouldn't it be simpler and easier to understand to analyze only one direction to start? Also, please clarify if the sequence algorithm was run on the raw decoded probabilities, or on the maximum a posteriori (MAP) locations. What happens if there are no spikes in a given time bin (likely to happen with a small 10 ms window) and were putative interneurons excluded (they should be)? Finally, the authors should note that theta sequences can arise from independent spiking of phase precessing neurons (Chadwick et al. eLife 2015) which seems exactly the kind of issue that the multiple regression framework of TDLM should be able to elucidate; what covariates could be added into the model to test Chadwick et al's claim?

Reviewer #1:

This paper describes temporal delayed linear modelling (TDLM), a method for detecting sequential replay during awake rest periods in human neuroimaging data. The method involves first training a classifier to decode states from labeled data, then building linear models that quantify the extent to which one state predicts the next expected state at particular lags, and finally assessing reliability by running the analysis with permuted labels.

This method has already been fruitfully used in prior empirical papers by the authors, and this paper serves to present the details of the method and code such that others may make use of it. Based on existing findings, the method seems extremely promising, with potential for widespread interest and adoption in the human neuroimaging community. The paper would benefit, however, from more discussion of the scope of the applicability of the method and its relationship to methods already available in the rodent and (to a lesser extent) human literature.

1) TDLM is presented as a general tool for detecting replay, with special utility for noninvasive human neuroimaging modalities. The method is tested mainly on MEG data, with one additional demonstration in rodent electrophysiology. Should researchers expect to be able to apply the method directly to EEG or fMRI data? If not, what considerations or modifications would be involved?

2) How does the method relate to the state of the art methods for detecting replay in electrophysiology data? What precludes using those methods in MEG data or other noninvasive modalities? And conversely, do the authors believe animal replay researchers would benefit from adopting the proposed method?

3) It would be useful for the authors to comment on the applicability of the method to sleep data, especially as rodent replay decoding methods are routinely used during both awake rest and sleep.

4) How does the method relate to the Wittkuhn & Schuck fMRI replay detection method? What might be the advantages and disadvantages of each?

5) The authors make the point that spatial correlation as well as anti-correlation between state patterns reduces the ability to detect sequences. The x axis for Fig 3c begins at zero, demonstrating that lower positive correlation is better than higher positive correlation. Given the common practice of building one classifier to decode multiple states (as opposed to a separate classifier for each state), it would be very useful to provide a demonstration that the relationship in Fig 3c flips (more correlation is better for sequenceness) when spatial correlations are in the negative range.

6) In the Results, the authors specify using a single time point for spatial patterns, which would seem to be a potentially very noisy estimate. In the Methods, they explain that the data were downsampled from 600 to 100 Hz to improve SNR. It seems likely that downsampling or some other method of increasing SNR will be important for the use of single time point estimates. It would be useful for the authors to comment on this and provide recommendations in the Results section.

7) While the demonstration that the method works for detecting theta sequences in navigating rodents is very useful, the paper is missing the more basic demonstration that it works for simple replay during awake rest in rodents. This would be important to include to the extent that the authors believe the method will be of use in comparing replay between species.

8) The authors explain that they "had one condition where we measured resting activity before the subjects saw any stimuli. Therefore, by definition these stimuli could not replay, but we can use the classifiers from these stimuli (measured later) to test the false positive performance of statistical tests on replay." My understanding of the rodent preplay literature is that you might indeed expect meaningful "replay" prior to stimulus exposure, as existing sequential dynamics may be co-opted to represent subsequent stimulus sequences. It may therefore be tricky to assume no sequenceness prior to stimulus exposure.

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:

The reviewers all felt that the work is extremely valuable: a domain-general replay detection method would be of wide interest and utility. However, as it stands, the paper is lacking context and comparisons to existing methods. Most importantly, the paper would have a larger impact if comparisons with standard replay methods were included. The paper would also benefit from additional detail in the description of the methods and data.

Reviewer #3:

This study by Kiss and colleagues reports the findings of proximity biotinylation experiments for the discovery of novel RAB18 effectors. The authors perform careful proteomic analysis that appears well-controlled and successful in recapitulating known interactions. That small GTPase interactions can be identified with this approach has been previously demonstrated, though the application of this approach to RAB18 is novel and of interest to the field. A number of intriguing findings with potentially important implications are reported. However, this manuscript has several weaknesses.

Major concerns and questions:

1) As the authors report, proximity biotinylation may not reflect direct protein-protein interactions but simply colocalization of bait and prey proteins. A true protein-protein interaction ideally would be further supported by ancillary experiments such as in vitro binding or co-immunoprecipitation, including an assessment of whether the interaction is affected by the GTP- or GDP-bound state. While co-IP in WT and GEF-deficient cells was performed for 1 candidate interactor (TMC04, Figure 6C), protein-protein interactions were not tested for the other 2, with the latter relying on either repeat BioID (SPG20, Figure 3A) or reciprocal BioID (SEC22A, Figure 5B).

2) Putative RAB18 interactions may be affected by the BioID fusion itself or by heterologous expression. While it is reassuring that known interactors were detected with this approach, the conclusions would be better supported by testing the localization of the fusion protein in comparison to endogenous RAB18, and/or by rescue of a phenotype associated with RAB18-deficiency.

3) Conclusions about the dependence of RAB18 interactions on its GTP or GDP-bound state rely on differences observed in cells with deficiency of RAB18 GEFs. It is certainly possible however that RAB3GAP may serve as a GEF for other GTPases, or have other functions, that cause the observed differences in labeling. The conclusions would be strengthened by additional experiments showing a direct effect - e.g. reproducing the disrupted labeling of candidate effectors with a GDP-locked RAB18 point mutant, or showing that RAB3GAP deficiency reduces binding of a candidate effector to RAB18.

4) The putative role of SEC22A in regulating lipid droplet morphology relies on siRNA perturbations that are prone to off-target effects. This is especially concerning given the high degree of sequence similarity between SEC22A and SEC22B, the latter of which has a known role in regulating LD morphology. Rescue of this phenotype with a siRNA-resistant SEC22A cDNA would rule out this possibility.

5) The finding of SPG20 protein abundance being affected by RAB18-deficiency relies on immunofluorescence with an antibody exhibiting cross-reactivity. While the authors do attempt to adjust for this non-specific background fluorescence, this conclusion would be strengthened by immunoblotting for a change in abundance of the specific band corresponding to SPG20. If confirmed, measurement of SPG20 transcripts levels would also help clarify the level of regulation for the altered protein abundance.

6) The influence of stable expression of a RAB18 GTP-locked point mutant on cholesterol metabolism is intriguing but the experimentation appears perfunctory. For 14C-CE cellular levels in 14C-oleate-loaded cells (Figure 7A), the most striking difference is the greatly enhanced synthesis level of CE at t=0. Is the subsequent drop due to an effect of RAB18 on efflux, or simply a consequence of the higher starting level at t=0? For efflux assays on 3H-cholesterol-loaded cells (Figure 7B), the data is only presented as a ratio of 3H activity in media relative to lysates after a 5 hr incubation with HDL. Interpretation of these results would be aided by a more detailed analysis. How does 3H-cholesterol uptake compare after 24 hr incubation but prior to addition of HDL (t=0)? After the 5 hr HDL chase, are the differences in the ratio driven by an increase in extracellular activity, a decrease in intracellular activity, or both? Ultimately these conclusions would be better supported by a more detailed analysis. Does disruption of the candidate effectors phenocopy the effect of RAB18 disruption? Are any known mediators of cholesterol efflux affected by RAB18 disruption? While a comprehensive mechanism may be reasonably considered beyond the scope of this paper, some additional descriptive analysis would be useful in interpreting these findings.

Reviewer #2:

This study used WT and mutant RAB18 to look for interacting proteins in normal and GEF-deficient cells. A catalog of interactions that are regulated by nucleotide binding and/or GEF activity were uncovered. Among identified proteins, there are known/established ones and there are some new ones. Initial validation was carried out for some newly identified effectors such as TMCO4 and Sec22A.

Major concerns and questions:

1) While the addition of new RAB18 effectors is useful to researchers who are interested in RAB18, the overall conclusion that RAB18 may regulate membrane contacts and lipid metabolism is not new.

2) Figure 7: the effect of RAB18 on cholesterol esterification and efflux may arise from multiple causes. This set of experiments do not provide any real insights into RAB18's role in cholesterol metabolism.

3) Given RAB18's interaction with ORP2, TMEM24 and OCRL, perhaps the authors may examine plasma membrane PIP2. The results would be more specific and novel.

Reviewer #1:

This manuscript used proximity biotinylation to discriminate functional RAB18 interactions. The authors provide some evidence for several of the interactors and some functional data supporting a role for RAB18 in modulating cholesterol mobilization.

Major concerns and questions:

1) Based on the spectral counts, the author calculated a mutant:WT ratios as a readout to identify nucleotide-binding-dependent effectors. But it is important to show that WT protein and mutant protein have similar expression level to begin with. And the intracellular localization of the mutation and WT should also be determined. Do they show the similar intracellular localization?

2) The ratio of mutation:WT is useful to remove some background. But this may omit some very highly interacting proteins just because their fold change is low. The converse is true for rare proteins. It would be better to have a list of candidate effectors based on the absolute counts.

3) Sec22A knockdown will change the morphology of lipid droplets. A knockdown efficiency test and some representative fluorescence images here would make this data more compelling.

4) Same comment for the cholesterol mobilization experiment. Expression level of the protein is needed. Figure 7A is rather confusing, as the Gln67Leu mutation already has higher CE before loading HDL. Why is this this? Better uptake or reduced efflux? What is the de novo cholesterol synthesis activity in this cell line?

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 preprint: https://www.biorxiv.org/content/10.1101/871517v1

Summary:

As a possible path to better understand and develop treatments for Warburg Micro Syndrome (WMS), the authors have investigated the networks of protein-protein interactions involving genes mutated in this rare genetic disease. The goals of the work are to identify new proteins involved in the pathophysiology of the disease and to better understand the molecular and cellular effects of disease-causing mutations. The data will likely be of interest to researchers studying WMS and RAB18, the protein focused on here, but reviewers expressed some concerns about the validation and interpretation of the presented protein interaction data.

Reviewer #3:

This manuscript describes measurements of neuronal activity in mice performing a discrimination task, and a new model that links these data to psychophysical performance. The key element of the new model is that sensory neurons are subject to gain modulations that evolve during each trial. They show that the model can produce pure sensory integration, Weber-Fechner performance, or intermediate states that nicely replicate the behavioral observations. This is an interesting and valuable contribution.

My only significant comment relates to the discussion, which should do more to make sure the reader understands how very different the sensory representation is in this study compared with the great majority of earlier related work in the primate:

First, choice related signals are not systematically related to stimulus preferences (no Choice Probability). This is mentioned, but only very briefly.

Second, there appears to be no relationship between stimulus preference (visual field in this case) and noise correlation. Unfortunately, this emerges from the model fits, not an analysis of data. But is an important difference with profound implications for how the coding of information is organized. It really needs a discussion. It should also be supported by an analysis of correlations in the data. I know some people argue that 2 photon measures make this difficult, but if that's true then surely they can’t be used to support a model in which correlations are a key component.

Reviewer #2:

In this manuscript, the authors present an in-depth analysis of the properties of sensory responses in several visual areas during performance of an evidence-accumulation task for head-fixed running mice (developed and studied by the authors previously), and of how these properties can illuminate aspects of the performance of mice and rats during pulsatile evidence accumulation, with a focus on the effect of "overall stimulus strength" on discriminability (Weber-Fechner scaling).

The manuscript is very dense and presents many findings, but the most salient ones are a description of how the variability in the large Ca++ transients evoked by the behaviourally-relevant visual stimuli (towers) are related to several low-level behavioural variables (speed, view) and also variables relevant for the task (future choice, running count of accumulated evidence), and a framework based on multiplicative-top down feedback that seeks to explain some aspects of this variability and ultimately the psychophysical performance in the accumulating-towers task. The first topic is framed in the context of the literature on choice-probability, and the second in the context of "Weber-Fechner" scaling, which in the current task would imply constant performance for given ratios of Left/Right counts as their total number is varied.

Overall, the demonstration of how trial to trial variability is informative about various relevant variables is important and convincing, and the model with multiplicative feedback is elegant, novel, naturally motivated by the neural data, and an interesting addition to a topic with a long-history.

Main Comments

1) Non-integrable variability. In addition to 'sensory noise' (independent variability in the magnitude of each pulse), it is critical in the model to include a source of variability whose impact does not decay through temporal averaging (to recover Weber-Fechner asymptotically for large N). This is achieved in the model by positing trial-to-trial variability (but not within-trial) in the dot product of the feedforward (w) and feedback (u) directions. But the way this is done seems to me problematic:

The authors model variability in wu as LogNormal (pp42 middle). First, the justification for this choice is incorrect as far as I can tell. The authors write: "We model m_R with a lognormal distribution, which is the limiting case of a product of many positive random variables". But neither is the dot product of w and u a product (it's a sum of many products), nor are the elements of this sum positive variables (the vector u has near zero mean and both positive and negative elements allowing different neurons to have opposite preferences on choice - see e.g., fifth line from the end in pp15 where it is stated that u_i<0 for some cells), nor would it have a LogNormal distribution even if the elements of the sum were indeed positive. Without further assumptions, the dot product wu will have a normal distribution with mean and variance dependent on the (chosen) statistics of u and w.

Two conditions seem to be necessary for uw: it should have a mean positive but close to zero (if it's too large a(t) will explode), and it should have enough variability to make non-integrable noise have an impact in practice. For a normal distribution, this would imply that for approximately half of the trials, wu would need to be negative, meaning a decaying accumulator and effectively no feedback. This does not seem like a sensible strategy that the brain would use.

The authors should clarify how this LogNormality is justified and whether it is a critical modelling choice (as an aside, although LogNormality in u*w allows non-negativity, low mean and large variability, the fact that it has very long tails sometimes leads to instability in the values of a(t)).

2) Related to this point, it would be helpful to have more clarity on exactly what is being assumed about the feedback vector u. The neural data suggests u has close to zero mean (across neurons). At the same time, it is posited that u varies across trials (3rd paragraph in pp18: "accumulator feedback is noisy") and that this variability is significant and important (previous comment). However, it would seem like neurons keep their choice preference across trials, meaning the trial to trial variability in each element of u has to be smaller than the mean. The authors only describe variability in uw (LogNormal), but, in addition to the issues just mentioned about this choice, what implications does this have for the variability in u? The logic of the approach would greatly increase if the authors made assumptions about the statistics of u consistent with the neural data, and then derived the statistics of uw.

3) Overall, it seems like there is an intrinsically hard problem to be solved here, which is not acknowledged: how to obtain large variability in the effective gain of a feedback loop while at the same time keeping the gain "sufficiently restricted", i.e., neither too large and positive (runaway excitation) nor negative (counts are forgotten). While the authors avoid worrying about model parameters by fitting their values from data (with the caveats discussed above), their case would become much stronger if they studied the phenomenology of the model itself, exposing clearly the computational challenges faced and whether robust solutions to these problems exist.

Reviewer #1:

This study investigates the responses of neurons in the parietal cortex of mice (recorded via two-photon Ca imaging) performing a virtual navigation task, and then relates their activity to the animal's psychophysical performance. It is essentially two studies rolled into one. The analysis of neurophysiological activity in the first part shows that visually driven responses in the recorded "cue cells" are strongly modulated by the eventual choice and/or by the integrated quantity that defines that choice (the difference in left vs right stimulus counts), as well as by other task variables, such as running speed. The model comparison study of the second part shows that, in the context of a sensory-motor circuit for performing the task, this type of feedback may account for subtle but robust psychophysical effects observed in the mice from this study and in rats from previous studies from the lab. Notably, the feedback explains intriguing deviations in choice accuracy from the Weber-Fechner law.

Both parts are interesting and carefully executed, although both are pretty dense; there are a ton of important technical details at each step. I wonder if this isn't too much for a single study. Had I not been reading it as a reviewer, I probably would have stopped after Fig. 4 or just skimmed the rest. After that, the motivation, methods, and analyses shift markedly. I'm not pushing hard on this issue, but I think the authors should ponder it.

Other comments:

1) It wasn't clear to me how the time of a particular cue onset was defined. In a real environment the cues would appear small (from afar) and get progressively bigger as the animal advances (at least if they are 3D objects, as depicted in Fig 1). What would be the cue onset in that case, and does the virtual environment work in the same way? This is probably not a serious issue, but it comes across as a bit at odds with the supposed "pulsatile" nature of the sensory stream, and would seem somewhat different from the auditory case with clicks.

A related question concerns multiple references to cue timing made in the Intro, as if such timing were very precise. This seems strange given that all time points depend on the running speed of the mice, which is probably variable. So, how exactly is cue position converted to cue time, and why is there an assumption of very low variability? Some of this detail may be in previous reports, but it would be important to make at least a brief, explicit clarification early on.

2) "positively and negatively choice-modulated cells exhibited gradually increasing effect sizes vs. place/time in the trial (Fig. 4e)" I found Fig. 4e confusing. Some curves are monotonic and some are not, and I'm not sure what is the point of showing the shades (which cover everything). If the key point is to contrast SSA and feedback models/effects, then it would be better to plot their corresponding effects directly, on the same graph, or to show predictions versus actual data in each case, in two graphs.

3) Fig 6 and the accompanying section of the manuscript investigate a variety of models with different architectures (feedback vs purely feedforward) and noise sources. Here, if I understood correctly, the actual cue-driven responses are substituted with variables that are affected by different types of noise. It is this part that I found a bit disconnected from the rest, and somewhat confusing.

Here, there's a jump from the actual cells to model responses. I think this needs an earlier and more explicit introduction. It is clear what the objective of the modeling effort is; what's unclear are the elements that initially go into it. This is partly because the section jumps off with a discussion about accumulator noise, but the modeling involves many more assumptions (i.e., simplifications about the inputs to the accumulators).

What I wondered here was, what happened to all the variance that was carefully peeled away from the cue driven responses in the earlier part of the manuscript? Were the dependencies on running speed, viewing angle, contra versus ipsi sensitivity, etc still in play, or were the modeled cue-driven responses considering just the sensory noise from the impulse responses? I apologize if I missed this. I guess the broader question is how exactly the noise sources in the model relate to all the dependencies of the cue cells exposed in the earlier analyses.

Overall, my general impression is that this section requires more unpacking (perhaps it should become an independent report?).

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 carefully studies the properties of sensory responses in several visual areas during performance of a task in which head-fixed mice run along a virtual corridor and must turn toward the side that has more visual cues (small towers) along the wall. The results provide insight into the mechanisms whereby sensory evidence is accumulated and weighted to generate a choice, and into the sources of variability that limit the observed behavioral performance. All reviewers thought the work was generally interesting, carefully done, and novel.

However, the reviewers' impression was that the manuscript as it stands is very dense. In fact, it is largely two studies with different methods and approaches rolled into one. The first one (physiology) is still dense but less speculative and with interesting, solid results, and the revisions suggested by the reviewers should be relatively straightforward to address. In contrast, the modeling effort is no doubt connected to the physiology, but it really addresses a separate issue. The general feeling was that this material is probably better suited for a separate, subsequent article, for two reasons. First, because it will require substantial further work (see details below), and second, because it adds a fairly complex chapter to an already intricate analysis of the neurophysiological data.

We suggest that the authors revise the neurophys analyses along the lines suggested below (largely addressing clarity and completeness), leaving out the modeling study for a later report.

Reviewer #2:

Arg5, 6, a polyprotein is cleaved to produce two proteins Arg5 and Arg6. The authors report that production of these two proteins is mediated by a mitochondrial protease that is known for its function in N-terminal cleavage.

The in vitro analysis is interesting, but the possibility of a contaminating activity cannot be ruled out. This needs to be tested by additional experiments, preferably by more data in intact cells.

Reviewer #1:

This study investigates the biogenesis of Arg5,6 in the yeast S. cerevisiae. Arg5,6 is a polyprotein that was previously established to be proteolytically processed into two proteins (Arg5 and Arg6) that are part of a complex with Arg2. The primary advance reported in the current study is to assign this processing to MPP, a mitochondrial protease known primarily for removing the N-terminal signal peptides from mitochondrial precursors. Additional work showed that the cleavage occurs at an internal sequence that resembles a mitochondrial targeting sequence (MTS), which presumably explains why it is recognised by MPP. This MTS-like internal processing signal is ineffective for directing translocation on its own. Some species contain this polyprotein organisation of Arg5,6, whereas other species encode the two proteins as separate open reading frames. S. cerevisiae Arg5,6 can be replaced effectively by two separately encoded products.

Specific points:

1) The authors use purified MPP to show that in vitro synthesized Arg5,6 precursor can be processed to the correct sized products. At that point, the authors "conclude that Arg5,6 is imported into the mitochondrial matrix and processed twice by MPP". This is plausible, but is premature based on the data, which show that MPP is able to process Arg5,6. However, the conclusion that MPP actually does process Arg5,6 in vivo is not documented, and the alternative that something else does this job is not formally excluded. This caveat should be acknowledged unless the authors are able to show necessity of MPP, not just sufficiency.

2) The experiment showing cleavage with purified MPP (Fig. 1E and S1A) would be strengthened with control experiments using a catalytically inactive mutant of MPP, and a Arg5,6 substrate with a mutated site for cleavage. The first control would rigorously exclude any contaminants, and the second would help verify the site of cleavage.

3) The conclusion that MPP processes Arg5,6 at the correct site in their in vitro experiments is based on size by SDS-PAGE. The resolution is not sufficient to draw this conclusion, which should be adjusted to say that processing occurs at approximately the correct site (unless the authors perform additional analysis to document the precise cleavage site). Mutagenesis of the putative site (point 2 above) would also be helpful in establishing the site more precisely.

4) The smaller products seen in Fig. 1E would seem to suggest that MPP exhibits a degree of promiscuity in vitro that is not seen in vivo. This should be noted in the text.

5) The authors observe that Arg6(1-343) cannot replace Arg6(1-502). They conclude that residues 344-502 are needed for enzyme activity, but this could be for many reasons. For example, Arg6(1-343) might not associate with Arg5. It is premature to imply that catalytic activity is impaired without making such measurements. The conclusion should be adjusted.

6) It is worth testing whether Arg5(344-862) produced by in vitro translation can be processed by purified MPP. This would help distinguish between some intrinsic problem with access versus a more nuanced issue relating to how import is mediated by the iMTS-L versus a bona fide MTS (e.g., with only the latter recruiting MPP as speculated by the authors).

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:

There were some technical concerns regarding the confidence with which the authors draw conclusions about whether the MPP is indeed the responsible protease. It is likely that the authors will be able to address these concerns with relatively straightforward additional experiments.

We feel that the notion of a polyprotein being processed into multiple functional products by cellular proteases is very well established. Providing an additional example relevant for some species, but not others, is a modest advance in our opinion, as emerged during discussion among the referees and editors. This problem is further compounded by a very similar concept for another mitochondrial protein reported by a subset of these authors recently.

Reviewer #3:

This is an interesting paper that looks for neural markers of "team flow" experiences compared to individual flow or social interaction using EEG measured during a musical social app game. The approach and analyses are sophisticated, with the main findings being that in a combined beta-low gamma frequency range there was higher power in regions of left temporal cortex for team flow than the other conditions; that other brain regions responded to individual flow or social interaction; that directed analyses found greater information from these other brain regions to the left temporal cortex; and that the left temporal cortices of players engaged in team flow synchronized.

However, these findings are difficult to interpret as they depend on the behavioural manipulation of the experiment that is purported to separate team flow, individual flow and social interaction, and I don't think these are clearly separated behaviourally. There were 3 conditions. In SyncA, players each tapped on a screen to control one stream of the music. In ScrA the music was scrambled and in Occl the game was as in SyncA, but the players were separated by a barrier. SyncA is supposed to measure team flow, ScrA individual flow but not team flow, and Occl is supposed to reduce social interaction. However, when one examines the ratings that players gave for team flow, individual flow and social interaction, they do not line up exactly with this theoretical manipulation. Specifically (Fig 1), individual flow ratings are higher in SyncA and Occl than ScrA, so SyncA and Occl don't differ in individual flow. Social interaction ratings are higher in SyncA than ScrA, and SrcA is higher than Occl, so Occl disrupts social interaction, but so does ScrA. And Team flow is disrupted by both ScrA and Occl. In other words, there is no clean mapping of the 3 experimental manipulations to the three ratings scales. Also very problematic is that for the rating questions, the three scales of individual flow, team flow and social interaction were not independent (Figure S2). Individual flow was taken as the average of questions 1-6, the social interaction as questions 7-9 and the team flow as questions 1-9! This makes it hard to interpret the findings because team flow is conceptually taken here as the combination of individual flow and social interaction, making the arguments appear circular.

The "depth of flow state" is a potentially interesting measure, consisting of the mean auditory evoked response (although I note that it is not clear how it was calculated: if it is the average of P1, N1, P2 and N2 or the power in theta) to unexpected task irrelevant beeps. Essentially it measures how distractible the person is from the task. So theoretically, it is not clear exactly how this relates to the complex concept of team flow. People were found to be most distractible for ScrA, not surprisingly, as the scrambled game is probably less fun and engaging, but across subjects, only SyncA was correlated with the individual flow index. Why? I also assume there was no correlation with team flow. Why not? So this is an interesting measure, but conceptually I'm not sure what it tells us about team flow.

For the analysis of beta-gamma, power at the electrode level at left temporal regions was higher for SyncA - but it was also higher for ScrA than for Occl (Fig 3), so what does that mean? From Fig 1e, team flow ratings were actually lower for ScrA than Occl (although maybe not significantly, but this is in the opposite direction). Also, this difference became exaggerated with high gamma, so why was this not analyzed? And how is this interpreted within the team flow concept?

For the cluster analysis, some clusters were found with higher beta-gamma power for SyncA, other clusters for ScrA and yet other clusters where power was lower for Occl. However, given as I describe above, that it is not clear exactly how these conditions relate to the concepts of individual flow, team flow and social interaction, I don't think the authors can say as they do that clusters where power is highest for SyncA represent team flow. Clusters where power is lowest for Occl were said to represent social interaction, but this cannot be said because Occl also had high ratings for individual flow (Fig 1) so could be either or both high individual flow and/or low social interaction. Clusters where power is highest for ScrA are interpreted as "flow suppression", but not clear why and whether this refers to individual flow or team flow as both are suppressed behaviourally (Fig 1)?

The directed connectivity analyses are interesting, but again difficult to interpret in terms of the individual flow, group flow, social interaction model. The regions need to be named more descriptively than GP1, etc. At the very least a table in the main text saying what these regions are would be helpful.

For the analyses of inter-brain effects, why did they authors go to a new measure, information, rather than using a directed measure as in the previous analysis?

I am also concerned about the very large number of statistical tests done here - probably experiment-wise error rate control is necessary. The more significant tests will survive this in any case.

I am also questioning the very detailed brain regions used in the source analysis. It would be difficult I think for EEG to be able to independently separate signals coming from nearby regions so precisely.

It also seems problematic that many participants were eliminated because they did not prefer to play the game in an interpersonal way over a solo or occlusion setup. Thus it seems that a very selected type of participant was used and I'm not sure if this can generalize. Also, some of the participants were friends, and this may have also influenced how they responded. At least some discussion of these issues is necessary.

Reviewer #2:

In the present manuscript, the authors introduce a novel task to measure 'team flow'. They test if alignment of brain activity is indicative of a shared experience, similar to mutual understanding (see e.g. work by Stolk et al. TiCS). They utilize a hyperscanning procedure where EEG recordings were obtained for two participants, while they were engaged in a task that requires cooperation.

While the approach is interesting and the topic timely; all the results rest on a methodological assumption, which has not been accounted for.

Both participants are presented with the same visual and auditory stimuli, which, when presented simultaneously, elicit the very same evoked response. When applying spectral analysis techniques to these simultaneously evoked responses, one can easily observe 'synchronization', which however, is completely driven by the simultaneous presentation of the external stimuli. This problem is aggravated when rhythmic visual stimuli are presented.

In addition, several statistical comparisons do not explicitly test the interactions, which are implied by the authors (this problem has been discussed in detail here: https://www.nature.com/articles/nn.2886)

In addition, several queries apply:

1) The Flow index needs to be defined earlier in the manuscript (at least prior to Figure 1)

2) a. Per Fig. 2c: The authors state 'As expected, the mean AEP response was significantly higher in the Inter-ScrA condition more than the other two conditions.' - Why was this expected? This statement is not trivial, why should the violation introduce a stronger response?

b. Furthermore, it is difficult to reconcile it with the next statement 'Thus, this weaker AEP for the task-irrelevant stimulus in the Inter-SyncA and Occl-SyncA conditions provides neural evidence that the brain has reached a distinct selective-attentional state marking the flow experience.'

• This is a far stretch from the ERP data

3) Fig. 2d - The authors need to test for differences in interactions and they cannot claim differences when one test is significant and the other is not. See e.g. https://garstats.wordpress.com/2017/03/01/comp2dcorr/

This again pertains to Figure 4c

4) Testing different frequency bands independently is again not valid, since, power values across bands are strongly correlated, see e.g. see work by Donoghue and Voytek (2020) biorxiv or Haller et al. (2018) biorxiv. Fig 3c makes this even more likely that some of the effects are broadband and not band-limited 'oscillations'.

5) All the differences localize to auditory areas, which makes one very suspicious that we are looking at evoked and therefore synchronized activity, and not alignment of endogenous oscillations, see e.g. a recent commentary: https://doi.org/10.1080/23273798.2020.1758335 The current paradigm basically would show synchrony (mistaken as team flow), when simultaneous spurious 'entrainment' (simultaneous evoked activity) is present in both participants; this confound needs to be accounted for since it confounds subsequent metrics of phase synchrony

6) Statistics in Fig. 4b, these tests and ROIs are not independent, a data-driven cluster approach could be utilized instead (see Maris and Oostenveld 2007).

7) Bar plots are deprecated, see Weissgerber et al PLOS Biol 2015.

8) Analysis for Figure 5a needs a depiction on what is actually analyzed. The hierarchical clustering approach is introduced with clear rationale and explanation.

Overall, this is an interesting approach. It is a methodological challenge to record EEG data from two interacting participants, but given that this is a relatively young field, some methodological prerequisites need to be established first. Critically, the authors need to present convincing evidence that we are not just facing the results of simultaneously evoked auditory and visual evoked responses.

Reviewer #1:

In this EEG study, the authors aimed to identify neural correlates of the subjective feeling of "team flow", i.e., a particular feeling of ease, task-related attention and control while doing a task together with someone else. This is a clearly interesting question and with a recent surge of hyperscanning research a timely study. The authors seem to have carefully selected pairs of participants who have similarly good performance in the game and similar music taste to be able to induce feelings of flow in their participants. Unfortunately, there seem to be quite serious problems in their statistical analyses which should be corrected first before the work can be assessed.

1) Participants:

a. The methods state that there are 15 participants, of which five were paired twice (p.13). In the Statistical analysis section, the authors state that "the unit of analysis" was participation, i.e., n = 20 (p. 17). This means apparently that five participants took part twice but were considered as independent measures in the statistical analyses. However, these are obviously dependent measures (or, repeated measures). The authors should include 20 (independent) participants in their analyses or need to take into account that five of the recorded 20 participants are identical.

b. The supplementary material explains in detail the selection of participants. Based on the selection criteria, 38 participants were identified (suppl mat p. 3), but it is not explained what happened to the 23 participants which are not part of the current manuscript. (Also, only the supplementary materials state that preferably friends were selected as pairs and that only those were selected (and called "prosocial") who considered doing the task together more pleasurable than doing the task alone. This should be mentioned in the main text and it seems to bias the subjective evaluation of the conditions presented in Fig 1?)

2) Statistical analyses:

Several of the analyses compare the neural data in the three different conditions with one-way ANOVAs. As these are dependent measures from the same participants, this should be analyzed with repeated measures ANOVA. Also, I didn't quite understand the statistics presented on p.8 (on information flow, with two-way ANOVAs with the impressive df of 26 and 494) and on p.9 (F(26,10133) = ... ?), but again the different measures within one subject seem to be considered as independent measures?

3) At several points of the analyses, it seemed like the analyses were biased. For instance, for the AEP analyses (which I generally considered a nice way to establish an "objective" measure of flow) only those channels were considered which in each resting trial robustly showed an AEP (p.14/15). Does that mean that different channels were considered for each trial and condition? I would suggest selecting the same set of central electrodes and then take these for all AEP analyses. Another case is the clustering analyses in which the number of cluster was selected such that condition differences were significant. Maybe I misunderstood this point but I guess the clustering should be done first and in the second (and independent) step, the condition differences can be assessed.

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 reports on a sophisticated experimental study in human participants. The study looks for neural markers of "team flow" experiences compared to individual flow or social interaction using EEG measured during a musical social app game. While the approach and analyses are sophisticated, all reviewers individually raised a series of substantial concerns with respect to EEG and statistical analysis. The editors and reviewers hence are unable to share the conclusions the authors would like to draw.

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

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Reply to the reviewers

We thank the Reviewers for the positive assessment of our work and their insightful remarks. Please find below a point-by-point response to each comment.

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

Scheckel et al. report a large dataset on cell type-specific translational profiling of PrD-associated molecular alterations in the a mouse model thorough RiboTRAP and ribosome profiling approaches. They report a more severe alteration in the translatome specifically in astrocyte and microglia as compared to neuronal populations. This highlights that changes in these two cell classes might have a predominant role in the pathology of PrD.

Data and the methods are presented such that they can be reproduced. The data analysis section of the manuscript could be further elaborated. In particular, it could be clarified which / how comparisons with existing dataset have been performed. Statistical analysis description is sometimes missing (e.g. fig 6e, not clear what the stars on top of the bars stands for, which test was performed and the significance). Moreover, the section of the methods regarding the western blots presented in figure 6 appear to be missing.

Fig 6e shows the output (log2 fold change) of DESeq2. Genes with a Benjamini-Hochberg adjusted p value \*Major concern:**

The most important improvement the authors should consider for their paper is to more specifically attempt to isolate specific effects on translational efficiency of mRNAs. As it stands, the authors largely use RiboTrap data as a reference to compare their footprinting data - but arguably, this misses mRNAs that are present in the transcriptome and not efficiently recruited onto ribosomes. It appears to be somewhat a lost opportunity to not attempt to test in the dataset (possibly by comparison to RNA-Seq from FACS isolated cells as a reference) whether there is a systematic change in translational efficiency (possibly in mRNAs with specific features?). In the current form, the RiboTrap and footprinting approaches largely serve to isolate mRNAs from cre-defined cell types but given the lack of a "total transcriptome" reference from the respective cells, it can not be easily interpreted whether certain transcripts are heavily regulated at the level of translation. Thus, despite using much more advanced methodologies than the Sorce study, the fundamental conclusions emerging from this work are rather similar to this previously published piece of work.

Translational changes can be assessed in a cell-type specific manner without artefacts related to dissociation/isolation procedures and are arguably more relevant than transcriptional changes (Haimon et al., Nat. Immunol. 2018). Both, the assessment of translation as well as the investigation of specific cell types differentiates this study from transcriptional profiling studies including Sorce et al. Accordingly, our approach identified > 1000 cell-type specific translational changes that were missed in the Sorce study (Fig. 5a-d).

We agree however with the reviewer that a comparison of our data with RiboTrap data does not take non-transcribed RNAs into account. We have refrained from such a comparison for several reasons:

We agree with the reviewer that a systematic comparison of transcriptomes and translatomes in the assessed cell types at every time point would have allowed us to identify genes regulated on a post-transcriptional level. The goal of this study was however to identify biologically relevant prion-induced molecular changes in a cell-type specific manner rather than identify post-transcriptional regulation. To assess the validity of our approach we chose closely related datasets (RiboTrap datasets) to compare our data to. The inclusion of RNAseq datasets from FACS-isolated cells would require an additional 2 years of work since all samples and datasets would need to be newly generated (breeding mice, inoculating mice with prions and waiting for up to 8 months for mice to reach the terminal time point, establishing procedures, generating and analyzing datasets) RNA-Seq from FACS isolated neurons is problematic due to neuronal processes often being lost during the dissociation/isolation procedures. Additionally, dissociation/isolation procedures typically introduce stress-related artefacts. These procedure-induced changes complicate comparisons with techniques that have been optimized to avoid such artefacts (including the method applied in this manuscript). Differences between transcriptional and translational datasets could thus be either due to post-transcriptional regulation or due to artefact differences and are likely difficult to interpret.

**Additional suggestions:**

1) In Figure 1d the authors point out occasional neuronal cells exhibiting Rpl10a-GFP expression with arrows. It appears that these arrows may have moved during figure preparation - please check/fix if necessary.

Thank you for pointing this out. We have fixed the arrows.

2) In Supplementary Figure 1b and c it appears that the PV labeling is missing in the panel for Rpl10a:GFP controls. If this is intentional please indicate this in the figure legend.

A co-localization of GFP-positive cells and PV was assessed only in Cre-positive (GFP expressing) mice but not in Cre-negative mice that don’t express GFP. We have clarified this point in the corresponding figure legend.

3) It appears that the authors sequenced a significant number of libraries generated for multiple time points post-inoculation. From the figures and legends it was not entirely clear to me, how many replicates were analyzed given that in some analyses samples from different time points were combined in a single plot.

All analyzed samples are listed in Supplementary File 1. We have emphasized this pointed in the results section.

4) It was unclear to me how long after inoculation the group of "terminally ill" mice were sacrificed. Somewhere in the text it states that there are 2 months between 24 wpi and terminally ill - but it appears that this was not a preset timepoint but varied from animal to animal based on symptoms. Please clarify.

We sacrifice mice at the last humane time point possible at which they show terminal disease symptoms, including piloerection, hind limb clasping, kyphosis and ataxia. Intraperitoneal inoculated mice reach that time point at 31 - 32 weeks post inoculation (+/- few days). Control mice (inoculated with non-infectious brain homogenate) were sacrificed at the same time. We have clarified this point in the methods section.

5) From the Western blot data in Figure 6f the authors conclude that GFAP expression is upregulated in PrD mice whereas astrocyte number is unchanged. Given that the translatome is assessed based on a Rpl10-GFP dependent on recombination mediated by cre driven from GFAP promoter it is possible that the astrocytic alterations in ribosome footprints are in part a secondary consequence of increased Rpl10-GFP recombination/ expression in PrD mice (due to activation of the GFAP promoter). To estimate the impact of such an effect the authors should compare GFP levels in terminally ill control and PrD mice by western blotting.

We agree with the reviewer that this information would be important to add. We have therefore assessed GFP levels in Rpl10a:GFP mice bred with GFAPCre and Cx3cr1CreER mice. The corresponding western blots are included in Supplementary Figure 11. GFP levels remained constant in terminally ill GFAPCre mice. This is not surprising since even a low GFAP promoter activity is likely to allow sufficient Cre recombinase expression to remove a STOP cassette allowing GFP expression (controlled by the Rosa26 promoter) in GFAPCre mice. In contrast, we observed an increase in GFP expression in terminally Cx3cr1CreER mice, which is most likely linked to the increase in microglia numbers. As pointed out in the manuscript, the translational changes we identified cannot reflect differences in cell numbers due to the nature of our assay. This suggests that a difference in GFP expression does not impact our analyses.

We have added this data to the manuscript.

6) The western blot analysis of fig 6f-g has been performed using a normalization over calnexin, yet no calnexin signals shown to support this statement.

We have included blots of the normalization control calnexin as Supplementary Figure 11a.

7) Clarify the percentage of non-parenchimal machrophages that are accounting for the Cx3cr1-creER mouse line since the authors consider this only to be a minor contamination.

The labeling of non-parenchymal macrophages using Cx3cr1CreER mice has previously been estimated to be ~1% (Haimon et al., Nat. Immunol. 2018). We have added this information to the manuscript.

8) Regarding the presentation of the data, Fig 5a would be clearer if in the y axes, for each cell type the order of PrD and Ctrl samples was maintained.

Fig 5a displays hierarchical clustering based on Euclidian distances. As samples are ordered according their distance from each other, we cannot change the order as suggested by the reviewer.

Reviewer #1 (Significance (Required)):

Overall, this is an important and interesting study. Besides its insights into the biology, the transcriptomic data will provide a valuable resource for researchers in the field.

Previous studies employed bulk RNAseq or microdissection for mapping transcriptomic changes (Majer et al.2019; Sorce et al. 2020 and others). The Sorce et al study concluded that astrocytic alterations in the transcriptome are more dominant than neuronal gene expression changes. While the conclusion of the present study remains the same, it is the first to use of ribosome profiling to dissect actively translated transcripts over the progression of the pathology in the mouse model. Thus, the data presented here would allow for identifying cell type-specific alterations as well as alterations specifically in mRNA translation which would be missed by bulk RNA-Seq and RNA-Seq on FACS-isolated cells. However, the authors do not fully capitalize on this strength, given that no detailed comparisons are done to a real transcriptome reference are performed (see above).

This work is of broad interest to scientists in neurodegeneration as well as glial biology.

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

Using a series of Cre-driven mouse strains a GFP-tagged version of RPL10a (a ribosomal protein) was targeted to different cell types allowing Dr Scheckel and colleagues to investigate translational changes as prion disease progresses in mice. Their data suggest massive changes in microglia and astrocytes but not neurons. The approach was particularly powerful as ribosome IP has been combined with ribosome profiling. The manuscript is very well written. What might help, however, is to make the figures more accessible (perhaps change some of the labelling?)

I have only minor comments regarding some of the figures:

Fig 1a: This scheme could be improved, adding wpi and better aligning the cell-types in relation to the time when the cell-types were analysed.

We have replaced weeks with wpi and changed the alignment of cell types to clarify that all cell types were analyzed at every time point.

Fig 1b-e: The resolution could be improved to better discern the different cell-types.

We submitted low-quality figures due to an upload limit but will submit final figures of higher quality. Additionally, we have added higher magnification pictures to better discern the different cell types as Supplementary Fig. 1d-e.

Fig 4: Astrocytes are categorised into A1 and A2 and microglia based on DAM and homeostatic signature (How does this relate to the M1 and M2 classification?).

The categorization of microglia into homeostatic and disease-associated (as well as other) microglia has largely replaced the initial categorization into pro-inflammatory M1 and anti-inflammatory M2 microglia (Dubbelaar et al., Front Immunol. 2018), We have therefore opted for the more current categorization. This explanation has also been added to the manuscript.

Reviewer #2 (Significance (Required)):

Highly significant. I have published on de novo protein synthesis in neurodegenerative disease

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

**Summary:**

The authors sampled actively translated proteins by cell type in the brains of RiboTag expressing mice under the control of cell specific cre recombination to determine changes in the translational profiles. They injected prions IP to induce prion disease. Their model shows little to no neuron loss at the terminal stage due to animal welfare regulations, but neuronal loss is a key hallmark of prion disease, along with gliosis. However, since other groups under different animal welfare regulations have shown that prion injection is sufficient to fully model the disease given enough time, there is sufficient evidence that this model captures early disease pathogenesis. The methodology used here has some clear advantages over previous cell-type isolation methods that require more lengthy sorting procedures. However, proteins with a long half-life or tightly regulated levels (such as TDP-43) are likely underrepresented by this method. The method also depends strongly on the specificity of the cre driver used; CamkIIa (excitatory N), parvalbumin (inhibitory N), GFAP (A), Cx3cr1 (microglia). While there is some off-target expression of the GFAP and Cx3cr1, the overall expression profiles generally match cell-specific transcriptomes obtained by other groups using other methods. They find major changes in astrocytes and microglia at terminal stages, after the onset of neurological symptoms, and comparatively fewer in neurons. Oligodendrocytes are not examined. The authors are commended on a thorough and well-designed study, especially in the comparison of multiple neuronal and glial types simultaneously.

**Major comments:**

Key conclusion 1: "Our results suggest that aberrant translation within glia may suffice to cause severe neurological symptoms and may even be the primary driver of prion disease." This conclusion is well-supported, serving as a hypothesis for future work. The data shows that the most abundant PTG changes are indeed in microglia at 24 wpi, before the onset of symptoms. In addition, although some genes are also differentially translated in the neuronal populations, examination of the Supplemental Tables shows that these are mostly highly expressed glial genes and could represent contamination of the sample during gliosis. The authors may wish to discuss this more prominently to avoid confusion. This data indeed suggests that glial changes alone are could be sufficient to produce the neurological symptoms in these mice. However, the authors should include discussion that the two genes changed at 24 weeks in PV neurons (Oprm1, Cyp2s1) do appear to be neuronal and may be relevant to pathogenesis as well. These mRNAs were also decreased in their previous paper conducting bulk sequencing in the hippocampus, according to the authors' online Prion RNAseq Database. Knockout experiments in mouse models have shown that dysregulation of one or a few critical genes in neurons can be sufficient to induce dysfunction and neurological symptoms, and the current evidence does not seem sufficient to rule it out. Fig 3d also suggests that PTGs in PV neurons may be particularly important, even accounting for the additional regions present in the RP analysis.

We agree with the reviewer that few critical neuronal genes might be sufficient to induce neurological dysfunction and symptoms and have added this point to the results and discussion. Additionally, we have highlighted that many neuronal genes are glia-enriched and might reflect glia contamination.

Key Conclusion 2: "Cell-type specific changes become only evident at late PrD stages." This conclusion is well supported. However, as the authors noted, due to legal constraints their model represents early to mid disease onset rather than a true terminal environment matching that of patients. Therefore, it would be advantageous to choose a more appropriate name for the "terminal" group, perhaps based on one of the key humane endpoint criteria that would help readers in the field to place these important results in context of the overall disease process.

We have added additional information to clarify our definition of terminal stage to the methods.

Key Conclusion 3: "This suggests that the prion-induced molecular phenotypes reflect major glia alterations, whereas the neuronal changes responsible for the behavioral phenotypes may be ascribed to biochemically undetectable changes such as altered neuronal connectivity." The authors should modify the second half of this claim. As discussed above, changes to even a few neuronal genes can be sufficient to induce neurodegeneration. The claim that "the neuronal changes responsible for the behavioral phenotypes may be ascribed to biochemically undetectable changes," fails to acknowledge the changes in PV neurons observed in this study, however few they may be. The authors also do not take into account the possible role of transcribed RNAs that are not immediately translated (for example those that accumulate at synapses for fast translation on demand) or the overall proteome, which are not included in their analysis. Though their method cannot detect these components, the authors should examine the implications that such other changes may still be present in the discussion. The authors should also discuss the functions of the few specific PV PTGs and explore their potential relationship with neurodegeneration. This is especially important since the authors acknowledge that a key reason for including PV neurons in the analysis is ample evidence in the literature that they play a role in disease pathogenesis. Finally, the authors note that a top GO term in microglial cells was synaptic transmission. The authors should expand on this finding in the discussion, as the interplay of glia and neurons in the pathogenesis of disease is likely highly relevant.

We have removed the claim that “behavioral phenotypes may be ascribed to biochemically undetectable changes” and added the point that few neuronal changes might be sufficient to induce neuronal dysfunction & symptoms. As stated in the manuscript, we believe that the enrichment of the GO term synaptic transmission in microglia is an artefact. We therefore refrained from further discussing this finding and have highlighted that it is in artefact in the results.

• *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.* - *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.*

As discussed above, the inclusion of RNAseq datasets from FACS isolated cells would require an additional 2 years of work since all samples and datasets would need to be newly generated (breeding mice, inoculating mice with prions and waiting for up to 8 months for mice to reach the terminal time point, establishing procedures, generating and analyzing datasets).

Key Conclusion 1: No additional experiments needed. Key Conclusion 2: No additional experiments needed. Key Conclusion 3: No additional experiments needed for a modified statement.

The data and methods are largely reproducible. Additional information should be provided about the methods for Gene Ontology analysis, how it was controlled, and what was used as a significance measure.

We have added additional information about the GO analysis to the methods section. The complete list of GO terms is now included as Supplementary File 10.

Some groups contain only two animals. At least three should be included per group for a minimally robust analysis.

We have tried to include 3 replicates per group as suggested by the reviewer. In few exceptions, we lost an individual sample and one sample had to be excluded due to low quality. In these instances (GFAP_2wpi Ctrl; CamKIIa_CX_term_Ctrl, CamKIIa_CX_term_PrD, Cx3cr1_term_Ctrl and Cx3cr1_term_PrD) we ensured that both replicates showed a high correlation and could still yield reliable results (see below). Consistently, the DESeq2 algorithm (which can handle also just 2 replicates per group) identified differentially translated genes in the terminal samples.

**Minor comments:**

Fig. 1 c-e all panels should have a scale bar. E, closer insets or larger images are needed to see the colocalization in these very small cells.

We have added scale bars to all panels. A colocalization is indeed not visible in the uploaded low-quality Figures that were submitted due to the size limit. We believe that a colocalization is visible in the high-quality final pictures but are also happy to provide closer insets upon editorial request.

Fig. 5f: To allow interpretation of the Gene Ontology analysis, authors should include the number of genes involved in the pathway and the number of those genes found in their sample input list.

We have added details regarding the GO analysis to the methods section, and are now providing the requested information in Supplementary File 10.

Fig. S6: It is not clear from viewing the figure or the legend what the percentages on the axes refer to.

The principal components 1 and 2 are plotted on the x and y axes, respectively. The % of variance explained by these principal components is indicated. We have added this information to the figure legend.

Fig. S7: the gene numbers are confusing because they do not match the data in Fig. 4a. It would be helpful to use the same LFC cutoff as in Fig. 4a to avoid misunderstandings by the reader, or explain why no cutoff is used and what information the authors wish to convey by presenting the data that way.

*Typically, all significant changes (p adj Fig S9: The legend indicates that genes changed in all 5 datasets are colored in green, however this is not easily visible on the graphs (appears more gray).

Genes changing in all datasets are colored in green in Fig. 5. Genes changing in all datasets are colored in grey in Supplementary Fig. 9. We have adjusted the corresponding legends. The quality of the figures is very low due to the upload limit. The final figures will be of higher quality.

Fig. S10: on page 12 Supplementary Fig. 10c is referenced, but likely refers to 10b. Throughout manuscript: It should be RNase, not RNAse.

Both points have been addressed.

Reviewer #3 (Significance (Required)):

This work provides an important conceptual advance in prion disease research that glia may be primary drivers of disease equal to or surpassing certain neuronal populations. Though the authors have shown previously that glial changes are dominant in bulk sequencing of the hippocampus, cell type-specific analysis adds an important level of detail to convince the field that few transcriptional changes occur in neurons though neurological defects are already present. Historically, neuronal defects have been assumed to occupy the main role, with glia being largely ignored. This echoes recent similar changes in other areas of the neurodegenerative disease field where we are recognizing the important roles of glia in pathogenesis, and how they may be modulated to treat disease.

Their findings in PV neurons also may reflect early key changes in this important neuronal population that contribute to neurological symptom onset. They will allow further study of the genes and pathways involved and may lead to additional effective treatments for disease. Finally, the thorough comparison of multiple neuronal and glial populations will allow future investigation of the interplay of neurons and microglia in pathogenesis and shows the importance of studying them synergistically rather than individually.

*Audience:*

The neurodegenerative disease field in general will be interested in the findings. Immunologists, other neuroscientists, and pharmaceutical and other drug development organizations will also be influenced by the work.

*Own expertise:*

Neurodegenerative disease, transgenic mouse models, neuropathology, translational neuroscience

REFEREE'S CROSS-COMMENTING:

I agree with Reviewer 1 that a comparison of the total transcriptome with ribosomally active transcripts would aid the interpretation of this work. It would also uncover or refute the presence of cell-type differences in translation efficiency that directly impact the authors' major conclusion that glia are more affected than neurons. I support the request of this additional experiment.

As discussed above we have refrained from such a comparison since 1) the scope of this study was to identify biologically relevant prion-induced molecular changes and not study post-transcriptional regulation, 2) the generation of such dataset will take ~ 2 years, and 3) difference between transcriptional and translational changes are likely a combination of post-transcriptional regulation and artefact induced change that are probably difficult to interpret.

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

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Referee #3

Evidence, reproducibility and clarity

Summary:

The authors sampled actively translated proteins by cell type in the brains of RiboTag expressing mice under the control of cell specific cre recombination to determine changes in the translational profiles. They injected prions IP to induce prion disease. Their model shows little to no neuron loss at the terminal stage due to animal welfare regulations, but neuronal loss is a key hallmark of prion disease, along with gliosis. However, since other groups under different animal welfare regulations have shown that prion injection is sufficient to fully model the disease given enough time, there is sufficient evidence that this model captures early disease pathogenesis. The methodology used here has some clear advantages over previous cell-type isolation methods that require more lengthy sorting procedures. However, proteins with a long half-life or tightly regulated levels (such as TDP-43) are likely underrepresented by this method. The method also depends strongly on the specificity of the cre driver used; CamkIIa (excitatory N), parvalbumin (inhibitory N), GFAP (A), Cx3cr1 (microglia). While there is some off-target expression of the GFAP and Cx3cr1, the overall expression profiles generally match cell-specific transcriptomes obtained by other groups using other methods. They find major changes in astrocytes and microglia at terminal stages, after the onset of neurological symptoms, and comparatively fewer in neurons. Oligodendrocytes are not examined. The authors are commended on a thorough and well-designed study, especially in the comparison of multiple neuronal and glial types simultaneously.

Major comments:

Key conclusion 1: "Our results suggest that aberrant translation within glia may suffice to cause severe neurological symptoms and may even be the primary driver of prion disease." This conclusion is well-supported, serving as a hypothesis for future work. The data shows that the most abundant PTG changes are indeed in microglia at 24 wpi, before the onset of symptoms. In addition, although some genes are also differentially translated in the neuronal populations, examination of the Supplemental Tables shows that these are mostly highly expressed glial genes and could represent contamination of the sample during gliosis. The authors may wish to discuss this more prominently to avoid confusion. This data indeed suggests that glial changes alone are could be sufficient to produce the neurological symptoms in these mice. However, the authors should include discussion that the two genes changed at 24 weeks in PV neurons (Oprm1, Cyp2s1) do appear to be neuronal and may be relevant to pathogenesis as well. These mRNAs were also decreased in their previous paper conducting bulk sequencing in the hippocampus, according to the authors' online Prion RNAseq Database. Knockout experiments in mouse models have shown that dysregulation of one or a few critical genes in neurons can be sufficient to induce dysfunction and neurological symptoms, and the current evidence does not seem sufficient to rule it out. Fig 3d also suggests that PTGs in PV neurons may be particularly important, even accounting for the additional regions present in the RP analysis.

Key Conclusion 2: "Cell-type specific changes become only evident at late PrD stages." This conclusion is well supported. However, as the authors noted, due to legal constraints their model represents early to mid disease onset rather than a true terminal environment matching that of patients. Therefore, it would be advantageous to choose a more appropriate name for the "terminal" group, perhaps based on one of the key humane endpoint criteria that would help readers in the field to place these important results in context of the overall disease process.

Key Conclusion 3: "This suggests that the prion-induced molecular phenotypes reflect major glia alterations, whereas the neuronal changes responsible for the behavioral phenotypes may be ascribed to biochemically undetectable changes such as altered neuronal connectivity." The authors should modify the second half of this claim. As discussed above, changes to even a few neuronal genes can be sufficient to induce neurodegeneration. The claim that "the neuronal changes responsible for the behavioral phenotypes may be ascribed to biochemically undetectable changes," fails to acknowledge the changes in PV neurons observed in this study, however few they may be. The authors also do not take into account the possible role of transcribed RNAs that are not immediately translated (for example those that accumulate at synapses for fast translation on demand) or the overall proteome, which are not included in their analysis. Though their method cannot detect these components, the authors should examine the implications that such other changes may still be present in the discussion. The authors should also discuss the functions of the few specific PV PTGs and explore their potential relationship with neurodegeneration. This is especially important since the authors acknowledge that a key reason for including PV neurons in the analysis is ample evidence in the literature that they play a role in disease pathogenesis. Finally, the authors note that a top GO term in microglial cells was synaptic transmission. The authors should expand on this finding in the discussion, as the interplay of glia and neurons in the pathogenesis of disease is likely highly relevant.

• 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. - 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.

Key Conclusion 1: No additional experiments needed. Key Conclusion 2: No additional experiments needed. Key Conclusion 3: No additional experiments needed for a modified statement.

The data and methods are largely reproducible. Additional information should be provided about the methods for Gene Ontology analysis, how it was controlled, and what was used as a significance measure. Some groups contain only two animals. At least three should be included per group for a minimally robust analysis.

Minor comments:

Fig. 1 c-e all panels should have a scale bar. E, closer insets or larger images are needed to see the colocalization in these very small cells. Fig. 5f: To allow interpretation of the Gene Ontology analysis, authors should include the number of genes involved in the pathway and the number of those genes found in their sample input list. Fig. S6: It is not clear from viewing the figure or the legend what the percentages on the axes refer to. Fig. S7: the gene numbers are confusing because they do not match the data in Fig. 4a. It would be helpful to use the same LFC cutoff as in Fig. 4a to avoid misunderstandings by the reader, or explain why no cutoff is used and what information the authors wish to convey by presenting the data that way. Fig S9: The legend indicates that genes changed in all 5 datasets are colored in green, however this is not easily visible on the graphs (appears more gray). Fig. S10: on page 12 Supplementary Fig. 10c is referenced, but likely refers to 10b. Throughout manuscript: It should be RNase, not RNAse.

Significance

This work provides an important conceptual advance in prion disease research that glia may be primary drivers of disease equal to or surpassing certain neuronal populations. Though the authors have shown previously that glial changes are dominant in bulk sequencing of the hippocampus, cell type-specific analysis adds an important level of detail to convince the field that few transcriptional changes occur in neurons though neurological defects are already present. Historically, neuronal defects have been assumed to occupy the main role, with glia being largely ignored. This echoes recent similar changes in other areas of the neurodegenerative disease field where we are recognizing the important roles of glia in pathogenesis, and how they may be modulated to treat disease.

Their findings in PV neurons also may reflect early key changes in this important neuronal population that contribute to neurological symptom onset. They will allow further study of the genes and pathways involved and may lead to additional effective treatments for disease. Finally, the thorough comparison of multiple neuronal and glial populations will allow future investigation of the interplay of neurons and microglia in pathogenesis and shows the importance of studying them synergistically rather than individually.

Audience:

The neurodegenerative disease field in general will be interested in the findings. Immunologists, other neuroscientists, and pharmaceutical and other drug development organizations will also be influenced by the work.

Own expertise:

Neurodegenerative disease, transgenic mouse models, neuropathology, translational neuroscience

REFEREE'S CROSS-COMMENTING:

I agree with Reviewer 1 that a comparison of the total transcriptome with ribosomally active transcripts would aid the interpretation of this work. It would also uncover or refute the presence of cell-type differences in translation efficiency that directly impact the authors' major conclusion that glia are more affected than neurons. I support the request of this additional experiment.

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Referee #2

Evidence, reproducibility and clarity

Using a series of Cre-driven mouse strains a GFP-tagged version of RPL10a (a ribosomal protein) was targeted to different cell types allowing Dr Scheckel and colleagues to investigate translational changes as prion disease progresses in mice. Their data suggest massive changes in microglia and astrocytes but not neurons. The approach was particularly powerful as ribosome IP has been combined with ribosome profiling. The manuscript is very well written. What might help, however, is to make the figures more accessible (perhaps change some of the labelling?)

I have only minor comments regarding some of the figures:

Fig 1a: This scheme could be improved, adding wpi and better aligning the cell-types in relation to the time when the cell-types were analysed. Fig 1b-e: The resolution could be improved to better discern the different cell-types. Fig 4: Astrocytes are categorised into A1 and A2 and microglia based on DAM and homeostatic signature (How does this relate to the M1 and M2 classification?).

Significance

Highly significant. I have published on de novo protein synthesis in neurodegenerative disease

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Referee #1

Evidence, reproducibility and clarity

Scheckel et al. report a large dataset on cell type-specific translational profiling of PrD-associated molecular alterations in the a mouse model thorough RiboTRAP and ribosome profiling approaches. They report a more severe alteration in the translatome specifically in astrocyte and microglia as compared to neuronal populations. This highlights that changes in these two cell classes might have a predominant role in the pathology of PrD.

Data and the methods are presented such that they can be reproduced. The data analysis section of the manuscript could be further elaborated. In particular, it could be clarified which / how comparisons with existing dataset have been performed. Statistical analysis description is sometimes missing (e.g. fig 6e, not clear what the stars on top of the bars stands for, which test was performed and the significance). Moreover, the section of the methods regarding the western blots presented in figure 6 appear to be missing.

Major concern:

The most important improvement the authors should consider for their paper is to more specifically attempt to isolate specific effects on translational efficiency of mRNAs. As it stands, the authors largely use RiboTrap data as a reference to compare their footprinting data - but arguably, this misses mRNAs that are present in the transcriptome and not efficiently recruited onto ribosomes. It appears to be somewhat a lost opportunity to not attempt to test in the dataset (possibly by comparison to RNA-Seq from FACS isolated cells as a reference) whether there is a systematic change in translational efficiency (possibly in mRNAs with specific features?). In the current form, the RiboTrap and footprinting approaches largely serve to isolate mRNAs from cre-defined cell types but given the lack of a "total transcriptome" reference from the respective cells, it can not be easily interpreted whether certain transcripts are heavily regulated at the level of translation. Thus, despite using much more advanced methodologies than the Sorce study, the fundamental conclusions emerging from this work are rather similar to this previously published piece of work.

Additional suggestions:

1) In Figure 1d the authors point out occasional neuronal cells exhibiting Rpl10a-GFP expression with arrows. It appears that these arrows may have moved during figure preparation - please check/fix if necessary.

2) In Supplementary Figure 1b and c it appears that the PV labeling is missing in the panel for Rpl10a:GFP controls. If this is intentional please indicate this in the figure legend.

3) It appears that the authors sequenced a significant number of libraries generated for multiple time points post-inoculation. From the figures and legends it was not entirely clear to me, how many replicates were analyzed given that in some analyses samples from different time points were combined in a single plot.

4) It was unclear to me how long after inoculation the group of "terminally ill" mice were sacrificed. Somewhere in the text it states that there are 2 months between 24 wpi and terminally ill - but it appears that this was not a preset timepoint but varied from animal to animal based on symptoms. Please clarify.

5) From the Western blot data in Figure 6f the authors conclude that GFAP expression is upregulated in PrD mice whereas astrocyte number is unchanged. Given that the translatome is assessed based on a Rpl10-GFP dependent on recombination mediated by cre driven from GFAP promoter it is possible that the astrocytic alterations in ribosome footprints are in part a secondary consequence of increased Rpl10-GFP recombination/ expression in PrD mice (due to activation of the GFAP promoter). To estimate the impact of such an effect the authors should compare GFP levels in terminally ill control and PrD mice by western blotting.

6) The western blot analysis of fig 6f-g has been performed using a normalization over calnexin, yet no calnexin signalis shown to support this statement.

7) Clarify the percentage of non-parenchimal machrophages that are accounting for the Cx3cr1-creER mouse line since the authors consider this only to be a minor contamination.

8) Regarding the presentation of the data, Fig 5a would be clearer if in the y axes, for each cell type the order of PrD and Ctrl samples was maintained.

Significance

Overall, this is an important and interesting study. Besides its insights into the biology, the transcriptomic data will provide a valuable resource for researchers in the field.

Previous studies employed bulk RNAseq or microdissection for mapping transcriptomic changes (Majer et al.2019; Sorce et al. 2020 and others). The Sorce et al study concluded that astrocytic alterations in the transcriptome are more dominant than neuronal gene expression changes. While the conclusion of the present study remains the same, it is the first to use of ribosome profiling to dissect actively translated transcripts over the progression of the pathology in the mouse model. Thus, the data presented here would allow for identifying cell type-specific alterations as well as alterations specifically in mRNA translation which would be missed by bulk RNA-Seq and RNA-Seq on FACS-isolated cells. However, the authors do not fully capitalize on this strength, given that no detailed comparisons are done to a real transcriptome reference are performed (see above).

This work is of broad interest to scientists in neurodegeneration as well as glial biology.

Reviewer #3

Jaron and collaborators provide a large-scale comparative work on the genomic impact of asexuality in animals. By analysing 26 published genomes with a unique bioinformatic pipeline, they conclude that none of the expected features due to the transition to asexuality is replicated across a majority of the species. Their findings call into question the generality of the theoretical expectations, and suggest that the genomic impacts of asexuality may be more complicated than previously thought.

The major strengths of this work is (i) the comparison among various modes and origins of asexuality across 18 independent transitions; and (ii) the development of a bioinformatic pipeline directly based on raw reads, which limits the biases associated with genome assembly. Moreover, I would like to acknowledge the effort made by the authors to provide on public servers detailed methods which allow the analyses to be reproduced. That being said, I also have a series of concerns, listed below:

1) Theoretical expectations.

As far as I understand, the aim of this work is to test whether 4 classical predictions associated with the transition to asexuality and 5 additional features observed in individual asexual lineages hold at a large phylogenetic scale. However, I think that these predictions are poorly presented, and so they may be hardly understood by non-expert readers. Some of them are briefly mentioned in a descriptive way in the Introduction (L56 - 61), and with a little more details in the Boxes 1 and 2. However, the evolutive reasons why one should expect these features to occur (and under which assumptions) is not clearly stated anywhere in the Introduction (but only briefly in the Results & Discussion). I think it is important that the authors provide clear-cut quantitative expectations for each genomic feature analysed and under each asexuality origin and mode (Box 1 and 2). Also highlighting the assumptions behind these expectations will help for a better interpretation of the observed patterns.

2) Mutation accumulation & positive selection.

A subtlety which is not sufficiently emphasized to my mind is that the different modes of asexuality encompass reproduction with or without recombination (Box 2), which can lead to very different genetic outcomes. For example, it has been shown that the Muller's ratchet (the accumulation of deleterious mutations in asexual populations) can be stopped by small amounts of recombination in large-sized populations (Charlesworth et al. 1993; 10.1017/S0016672300031086). Similarly a new recessive beneficial mutation can only segregate at a heterozygous state in a clonal lineage (unless a second mutation hits the same locus); whereas in the presence of recombination, these mutations will rapidly fix in the population by the formation of homozygous mutants (Haldane's Sieve, Haldane 1927; 10.1017/S0305004100015644). Therefore, depending on whether recombination occurs or not during asexual reproduction, the expectations may be quite different; and so they could deviate from the "classical predictions". In this regard, I would like to see the authors adjust their conclusions. Moreover, it is also not very clear whether the species analysed here are 100% asexuals or if they sometimes go through transitory sexual phases, which could reset some of the genomic effects of asexuality.

3) Transposable elements.

I found the predictions regarding the amount of TEs expected under asexuality quite ambiguous. From one side, TEs are expected not to spread because they cannot colonize new genomes (Hickey 1982); but on the other side TEs can be viewed as any deleterious mutation that will accumulate in asexual genome due to the Muller's ratchet. The argument provided by the authors to justify the expectation of low TE load in asexual lineages is that "Only asexual lineages without active TEs, or with efficient TE suppression mechanisms, would be able to persist over evolutionary timescales". But this argument should then equally be applied to any other type of deleterious mutations, and so we won't be able to see Muller's ratchet in the first place. Therefore, not observing the expected pattern for TEs in the genomic data is not so surprising as the expectation itself does not seem to be very robust. I would like the authors to better acknowledge this issue, which actually goes into their general idea that the genomic consequences of asexuality are not so simple.

4) Heterozygosity.

Due to the absence of recombination, asexual populations are expected to maintain a high level of diversity at each single locus (heterozygosity), but a low number of different haplotypes. However, as presented by the authors in the Box 2, there are different modes of parthenogenesis with different outcomes regarding heterozygosity: (1) preservation at all loci; (2) reduction or loss at all loci; (3) reduction depending on the chromosomal position relative to the centromere (distal or proximal). Therefore, the authors could benefit from their genome-based dataset to explore in more detail the distribution of heterozygosity along the chromosomes, and further test whether it fits with the above predictions. If the differing quality of the genome assemblies is an issue, the authors could at least provide the variance of the heterozygosity across the genome. The mode #3 (i.e. central fusions and terminal fusions) would be particularly interesting as one would then be able to compare, within the same genome, regions with large excess vs. deficit of heterozygosity and assess their evolutive impacts.

Moreover, the authors should put more emphasis on the fact that using a single genome per species is a limitation to test the subtle effects of asexuality on heterozygosity (and also on "mutation accumulation & positive selection"). These effects are better detected using population-based methods (i.e. with many individuals, but not necessarily many loci). For example, the FIS value of a given locus is negative when its heterozygosity is higher than expected under random mating, and positive when the reverse is true (Wright 1951; 10.1111/j.1469-1809.1949.tb02451.x).

5) Absence of sexual lineages.

A second limit of this work is the absence of sexual lineages to use as references in order to control for lineage-specific effects. I do not agree with the authors when they say that "the theoretical predictions pertaining to mutation accumulation, positive selection, gene family expansions, and gene loss are always relative to sexual species [...] and cannot be independently quantified in asexuals." I think that this is true for all the genomic features analysed, because the transition to asexuality is going to affect the genome of asexual lineages relative to their sexual ancestors. This is actually acknowledged at the end of the Conclusion by the authors.

To give an example, the authors say that "Species with an intraspecific origin of asexuality show low heterozygosity levels (0.03% - 0.83%), while all of the asexual species with a known hybrid origin display high heterozygosity levels (1.73% - 8.5%)". Interpreting these low vs. high heterozygosity values is difficult without having sexual references, because the level of genetic diversity is also heavily influenced by the long term life history strategies of each species (e.g. Romiguier et al. 2014; 10.1038/nature13685).

I understand that the genome of related sexual species are not available, which precludes direct comparisons with the asexual species. However, I think that the results could be strengthened if the authors provided for each genomic feature that they tested some estimates from related sexual species. Actually, they partially do so along the Result & Discussion section for the palindromes, transposable elements and horizontal gene transfers. I think that these expectations for sexual species (and others) could be added to Table 1 to facilitate the comparisons.

6) Regarding statistics, I acknowledge that the number of species analysed is relatively low (n=26), which may preclude getting any significant results if the effects are weak. However, the authors should then clearly state in the text (and not only in the reporting form) that their analyses are descriptive. Also, their position regarding this issue is not entirely clear as they still performed a statistical test for the effect of asexuality mode / origin on TE load (Figure 2 - supplement 1). Therefore, I would like to see the same statistical test performed on heterozygosity (Figure 2).

7) As you used 31 individuals from 26 asexual species, I was wondering whether you make profit of the multi-sample species. For example, were the kmer-based analyses congruent between individuals of the same species?

Reviewer #2

This paper is interesting because it is studying, through a comparative genomic approach, how asexuality affects genome evolution in animal lineages while focusing on the same features. Such an extensive comparison can, in principle, distinguish the common consequences of asexuality, in contrast to previous studies that focused on few asexual species (or only one). It is interesting that the authors did not find a universal genomic feature of "asexual" species. This is a potentially important contribution to the field of the evolution of reproductive systems.

However, I am concerned about limitations and potential biases in many of the specific genomic features analysed, and resultant difficulties in drawing any general conclusions from these analyses. For example, the heterozygosity analyses need to be more clearly explained and the potential limits of the methods used discussed further. The use of kmer spectra analyses as opposed to genome assemblies is understandable, but these are biases here that were not discussed. I am also concerned about the impact of low read quality and low coverage genomic data, and whether issues with genome assembly affect the conclusions. There are also issues about conclusions related to species of hybrid origin as there are numerous "unknown" cases and cytological data is lacking for many of the studied animal groups (therefore the authors should be cautious on the evidence of reproduction mode).

Ideally, all the genomes of the asexual animal clades studied should have been sequenced and assembled using the same method which would make this comparative study much stronger. We realize this may not yet be practical, but the absence of such data must temper the conclusions. It is nevertheless the first article including and comparing many distinct parthenogenetic animal clades and the main result that no common universal genomic feature of parthenogenesis is, with caveats, interesting.

Major Issues and Questions:

1) The authors choose to refer to asexuality when describing thelytokous parthenogenesis. Asexuality is a very general term that can be confusing: fission, vegetative reproduction could also be considered asexuality. I suggest using parthenogenesis throughout the manuscript for the different animal clades studied here. Moreover, in thelytokous parthenogenesis meiosis can still occur to form the gametes, it is therefore not correct to write that "gamete production via meiosis... no longer take place" (lines 57-58). Fertilization by sperm indeed does not seem to take place (except during hybridogenesis, a special form of parthenogenesis).

2) The cellular mechanisms of asexuality in many asexual lineages are known through only a few, old cytological studies and could be inaccurate or incomplete (for example Triantaphyllou paper of 1981 of Meloidogyne nematodes or Hsu, 1956 for bdelloid rotifers). The authors should therefore mention in the introduction the lack of detailed and accurate cellular and genetic studies to describe the mode of reproduction because it may change the final conclusion.

For example, for bdelloid rotifers the literature is scarce. However the authors refer in Supp Table 1 to two articles that did not contain any cytological data on oogenesis in bdelloid rotifers to indicate that A. vaga and A. ricciae use apomixis as reproductive mode. Welch and Meselson studied the karyotypes of bdelloid rotifers, including A. vaga, and did not conclude anything about absence or presence of chromosome homology and therefore nothing can be said about their reproduction mode. In the article of Welch and Meselson the nuclear DNA content of bdelloid species is measured but without any link with the reproduction mode. The only paper referring to apomixis in bdelloids is from Hsu (1956) but it is old and new cytological data with modern technology should be obtained.

3) In the section on Heterozygosity, the authors compute heterozygosity from kmer spectra analysis from reads to "avoid biases from variable genome assembly qualities" (page 16). But such kmer analysis can be biased by the quality and coverage of sequencing reads. While such analyses are a legitimate tool for heterozygosity measurements, this argument (the bias of genome quality) is not convincing and the authors should describe the potential limits of using kmer spectra analyses.

4) The authors state that heterozygosity levels “should decay over time for most forms of meiotic asexuality". This is incorrect, as this is not expected with "central fusion" or with "central fusion automixis equivalent" where there is no cytokinesis at meiosis I.

5) I do not fully agree with the authors’ statement that: "In spite of the prediction that the cellular mechanism of asexuality should affect heterozygosity, it appears to have no detectable effect on heterozygosity levels once we control for the effect of hybrid origins (Figure 2)." (page 17)

The scaling on Figure 2 is emphasizing high values, while low values are not clearly separated. By zooming in on the smaller heterozygosity % values we may observe a bigger difference between the "asexuality mechanisms". I do not see how asexuality mechanism was controlled for, and if you look closely at intra group heterozygosity, variability is sometimes high.

It is expected that hybrid origin leads to higher heterozygosity levels but saying that asexuality mechanism is not important is surprising: on Figure 2 the orange (central fusion) is always higher than yellow (gamete duplication). Also, the variability found within rotifers could be an argument against a strong importance of asexuality origin on heterozygosity levels: the four bdelloid species likely share the same origin but their allelic heterozygosity levels appears to range from almost 0 to almost 6% (Fig 2 and 3, however the heterozygosity data on Rotaria should be confirmed, see below).

The authors’ main idea (i.e. asexuality origin is key) seems mostly true when using homoeolog heterozygosity and/or composite heterozygosity which is not what most readers will usually think as "heterozygosity". This should be made clear by the authors mostly because this kind of heterozygosity does not necessarily undergo the same mechanism as the one described in Box 2 for allelic heterozygosity. If homoeolog heterozygosity is sometimes not distinguishable from allelic heterozygosity, then it would be nice to have another box showing the mechanisms and evolution pattern for such cases (like a true tetraploid, in which all copies exist).

The heterozygosity between homoeologs is always high in this study while it appears low between alleles, but since the heterozygosity between homeologs can only be measured when there is a hybrid origin, the only heterozygosity that can be compared between ALL the asexual groups is the one between alleles.

Both in the results and the conclusion the authors should not over interpret the results on heterozygosity. The variation in allelic heterozygosity could be small (although not in all asexuals studied) also due to the age of the asexual lineages. This is not mentioned here in the result/discussion section.

6) Regarding the section on Heterozygosity structure in polyploids.

There is inconsistency in many of the numbers. For example, A. vaga heterozygosity is estimated at 1.42% in Figure 1, but then appears to show up around 2% in Figure 2, and then becomes 2.4% on page 20. It is unclear is this is an error or the result of different methods.

It is also unclear how homologs were distinguished from homeologs. How are 21 bp k-mers considered homologous? In the method section. the authors describe extracting unique k-mer pairs differing by one SNP, so does this mean that no more than one SNP was allowed to define heterozygous homologous regions? Does this mean that homologues (and certainly homoeologs) differing by more than 5% would not be retrieved by this method. If so, then It is not surprising that for A. vaga is classified as a diploid.

The result for A. ricciae is surprising and I am still not convinced by the octoploid hypothesis. In Fig S2. there is a first peak at 71x coverage that still could be mostly contaminants. It would be helpful to check the GC distribution of k-mers in the first haploid peak of A. ricciae to check whether there are contaminants. The karyotypes of 12 chromosomes indeed do not fit the octoploid hypothesis. I am also surprised by the 5.5% divergence calculated for A. ricciae, this value should be checked when eliminating potential contaminants (if any). In general, these kind of ambiguities will not be resolved without long-read sequencing technology to improve the genome assemblies of asexual lineages.

7) Regarding the section on palindromes and gene conversion.

The authors screened all the published genomes for palindromes, including small blocks, to provide a more robust unbiased view. However, the result will be unbiased and robust if all the genomes compared were assembled using the same sequencing data (quality, coverage) and assembly program. While palindromes appear not to play a major role in the genome evolution of parthenogenetic animals since only few palindromes were detected among all lineages, mitotic (and meiotic) gene conversion is likely to take place in parthenogens and should indeed be studied among all the clades.

8) Regarding the section on transposable elements.

The authors are aware that the approach used may underestimate the TEs present in low copy numbers, therefore the comparison might underestimate the TE numbers in certain asexual groups.

9) Regarding the section on horizontal gene transfer.

For the HGTc analysis, annotated genes were compared to the UniRef90 database to identify non-metazoan genes and HGT candidates were confirmed if they were on a scaffold containing at least one gene of metazoan origin. While this method is indeed interesting, it is also biased by the annotation quality and the length of the scaffolds which vary strongly between studies.

10) Regarding the use of GenomeScope2.0.

When homologues are very divergent (as observed in bdelloid rotifers) GenomeScope probably considers these distinct haplotypes as errors, making it difficult to model the haploid genome size and giving a high peak of errors in the GenomeScope profile. Moreover, due to the very divergent copies in A. vaga, GenomeScope indeed provides a diploid genome (instead of tetraploid).

For A. vaga, the heterozygosity estimated par GenomeScope2.0. on our new sequencing dataset is 2% (as shown in this paper). This % corresponds to the heterozygosity between k-mers but does not provide any information on the heterogeneity in heterozygosity measurements along the genome. A limitation of GenomeScope2.0. (which the authors should mention here) is that it is assuming that the entire genome is following the same theoretical k-mer distribution.

Reviewer #1

This paper addresses the very interesting topic of genome evolution in asexual animals. While the topic and questions are of interest, and I applaud the general goal of a large-scale comparative approach to the questions, there are limitations in the data analyzed. Most importantly, as the authors raise numerous times in the paper, questions about genome evolution following transitions to asexuality inherently require lineage-specific controls, i.e. paired sexual species to compare with the asexual lineages. Yet such data are currently lacking for most of the taxa examined, leaving a major gap in the ability to draw important conclusions here. I also do not think the main positive results, such as the role of hybridization and ploidy on the retention and amount of heterozygosity, are novel or surprising.

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 preprint: https://www.biorxiv.org/content/10.1101/497495v2

Summary

This paper addresses the question of whether there are distinct genomic features in animals that reproduce asexually. The authors examine a range of features in the genomes of 26 species representing 18 independent evolutionary origins of asexuality. The reviewers were unanimous that this is an interesting question, and find that exploring it in a broad evolutionary context is the right approach. However, they raised questions about biases in specific analyses that complicated their interpretation, and the extent to which the central claims can be supported without comparison to closely related sexual species.

Reviewer #2:

General assessment:

The paper studies how facial expressions of proposers in a repeated ultimatum game affect decisions by responders. The paper makes three main contributions. First, responder's decisions are affected by the facial expressions of proposers. Second, the paper statistically compares the fit of several decision functions (utility functions). In the preferred model, the degree of inequity aversion of the responder depends on the facial expression of the proposer. Third, facial expressions of proposers correlate with pupil dilation of responders. The second contribution is the main contribution of the paper, as the first point has been shown before in many different economic games. I think that the second point - the modeling exercise - is interesting, but should be improved. Moreover, I think the experimental design has some important issues, which seem hard to address without collecting new data.

Substantive concerns:

1) One of the main selling points of the paper is that it studies iterative/repeated games instead of one-shot interactions. The authors seem to ignore (rule out) repeated game strategies however. This is understandable, given that analyzing the repeated game (with signaling) is complex, and beyond the point of the paper. More importantly, the statistical analysis ignores the dynamic nature of the game. From what I understand, in the analysis all data are pooled, both across participants and trials. Given this, I think the authors overinterpret the model, as the interpretation in the text is often dynamic (for example, on page 10, lines 254-255, but also in several other instances), whereas the statistical analysis is not.

2) Given that facial expressions affect decision-making, it is no surprise that including facial expressions in the decision values improves the fit. The most interesting part (to me) of the modeling exercise is to determine how facial expressions are best incorporated in the model. The authors organized a kind of 'horse race' between several models to address this. But why select these models? The choice seems ad-hoc and could be better motivated. For example, the best performing model treats positive and negative deviations from neutral faces in the same way, whereas the emotion recognition task and the pupil dilation analysis suggest that participants treat positive and negative emotions differently. An arguably simpler model would be one where more positive emotions lead to a higher weight on the other's payoffs. In sum, it would be good to better motivate which models are included (or not), and perhaps include several other competing models.

3) Another interesting feature of the modeling exercise is that it can help to quantify the relative importance of facial expressions. The best performing model predicts 86% of the decisions correctly. To judge whether this is a lot or a little, it would be good to report the accuracy of competing models (e.g. self-interest or 'standard' inequity aversion without facial expressions). It would also be helpful to report the log-likelihood and BIC for each model. Reporting all this (for all models) would help to understand the added value of facial expressions.

4) In the experiment, participants are given explicit instructions on how to make decisions (page 23, lines 644-654). I think this is a poor design choice if you study how people make decisions.

5) The sample size is rather small (n=44). Moreover, almost half (21 out of 44) of the participants are told to be playing against a computerized strategy, although the authors note that this did not affect decisions. I do not understand the reasons why it was not possible to match people with a confederate (page 22). Given that the study uses deception, it seems easy enough to always tell people that they are playing with a real person, but perhaps I miss something. Additionally, it is unclear what 'playing against a computerized strategy' means here. Are participants told that their decisions affect someone else's earnings? This seems crucial for social preferences to have a bite.

6) In the experiment, the proposers' expressions and offers are a function of the history of the game (responders do not know this). This makes it hard to identify if responders really respond to the expressions on the pictures, or if they respond to other factors in the history of the game, such as previous earnings or previous offers. For example, Figure 4 shows that responders' decisions are affected by the offer in the preceding trial (n-1). However, as the offer in trial (n) is a function of the offer in trial (n-1), this could simply pick up the effect of the current offer (n).

Reviewer #1:

The authors use an iterative ultimatum game to show that the proposer's facial expression, as well as the offer amount, influence human choice behavior. In particular, it is suggested that a proposer's facial responses to a participant's decisions specifically modulate the negative influence of perceived inequality on decision values. The combination of a game theoretic behavioral choice paradigm with computational cognitive modeling and a physiological arousal measure is appealing. I do, however, have some major concerns with novelty and interpretability, listed below in order of importance.

1) It is not particularly surprising that participants are more willing to accept an advantageous inequality if the proposer signals, with a smile, that it pleases them (or, conversely, less willing to accept if the proposer signals discontent), particularly in light of previous work having already shown that both advantageous and disadvantageous inequalities are more frequently accepted if the proposer is smiling than if the proposer looks angry (e.g., Mussel et al., 2013). The addition of pupillary data could have added a fundamentally different dimension to such findings; however, since pupil size could not be significantly related directly to model-based decision values (please make this null effect more salient to the reader, unless I have misunderstood it), the choice data and physiological measure seem disconnected, which weakens the impact of each.

2) The authors argue that the ecological validity of previous work assessing the influence of facial expressions on UG decisions (e.g., Mussel et al., 2013) was limited by the use of non-contingent affective stimuli in independent, one-shot, games. It could be argued, however, that the response-contingent affective and monetary feedback used in the current study threatens construct validity, by conflating game theoretic strategizing with basic reward learning. This is particularly problematic since the computational models lack a representation of learning, or any incorporation of feedback over trials, in spite of such information being shown to profoundly influence acceptance decisions in model-free analyses. Given the overall emphasis on changes in participants' behavior across trials, it is important to formally characterize those learning curves, using reinforcement learning or some other relevant computational framework.

3) It appears that a parabolic modulation was considered for the inequality term, but not for the self-reward term. Given the dramatic improvement in model-fits across exponential and parabolic modulations of the inequality term, it would be interesting to see the performance of a model that includes parabolic modulation of both self-reward and inequality.

4) Given the apparent difference in affective modulation of advantageous vs. disadvantageous inequality, the exclusive focus on advantageous inequality in the discussion of model-based analyses makes it difficult to map modeling results to potential underlying psychological constructs (also, it is unclear how results from separately modeled advantageous and disadvantageous inequalities were integrated during model selection).

5) Another difficulty with data interpretation is the absence of a comparison across different total amounts (e.g., 200 out of 1000 vs. 200 out of 300). It seems to me that the constant total (of 1000) may have unduly focused participants on the inequality, over self reward.

6) "This indicated that participants' affective biases were more prominent for negative emotions, causing them to under-estimate the severity of negative affective displays". It is unclear from the methods whether asymmetries in the rated valence of facial expressions reflect a bias on the part of participants, or a limit on the confederates' abilities to simulate a range of negative expressions.

7) "After excluding six extreme outliers [...]" Please account for the methods and effects of outlier exclusions.

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:

There was consensus among the reviewers that this paper addresses an interesting and important question of how social, affective and economic variables are formally integrated in strategic decision-making. However, the absence of a model-based account of how repeated game strategies and learning processes were shaped by the transition probabilities was a major concern, as was the lack of coherence between decision-making and pupillary effects.

Reviewer #3:

The manuscript reexamines AMPK-deficiency in the T cell compartment using mixed bone marrow chimeras, to show that T cell cell expansion (and effector functioning) both in vitro and in vivo is compromised by AMPK deficiency, that this is despite any effect of this deficiency on early events during TCR signalling, and that ROS scavenging ameliorates these defects to some extent. While the data are interesting, they remain incremental at this point, since a role for AMPK in the functioning of the T cell lineage has been shown previously (including by the authors), as the authors cite. The potentially novel nuanced observations the authors report in the present manuscript are not accompanied by novel mechanistic insights as yet.

The competitive bone marrow chimeras show the relative reduction of the AMPK-deficient genotype in the effector-memory T cell compartment, as would be predicted by previous literature. The more robust lack of AMPK-deficient T cells in the CXCR3-expressing subset and in gut lymphoid tissues is interesting, but no further mechanistic insights are offered into how AMPK specifically affects commitment to and or/survival in this compartment.

Similarly, the authors show that, interestingly, AMPK-deficient T cells show much poorer homeostatic proliferation, in a number of models of such proliferation. The authors connect this deficit to increased mitochondrial turnover and to the generation of ROS in the absence of AMPK. Once again, these are potentially interesting data. However, the causal connectivity claimed between the mitochondrial phenotype and the homeostatic proliferation defect is not well supported by the data, which consists only of a partial pharmacological rescue by a ROS scavenger in vitro. Further, there are no data indicating any explanation for this apparent distinction between initial cognate activation-induced proliferation and homeostatic proliferation.

Therefore, while this is a sound incremental manuscript of utility to the field, it does not as yet provide sufficient breadth of interest for a cross-disciplinary readership.

Reviewer #2:

The manuscript by Anouk Lepez and colleagues examines the importance of AMPK in long term T cell fitness and proliferation and concludes that although AMPK is dispensable for early TCR signaling and short term proliferation it is required for sustained long-term T cell proliferation and effector/memory T cell survival. The authors demonstrate that AMPK aggravated the severity of graft vs host disease and mechanistically proposed that AMPK enhanced the mitochondrial membrane potential of T cells to limit ROS production and associated toxicity. As the authors acknowledge, previous work on AMPK has shown that its absence does not affect T cell proliferation, however earlier work has also established that absence of AMPK affects GVHD (Beezhold, K et al, Blood (2016) 128 (22): 806) and that AMPK maintains homeostasis through regulation of Mitochondrial ROS (Rabinovitch et al, Cell Rep 2017 Oct 3;21(1):1-9. Current work does not add any additional mechanistic insights to the already known functions of AMPK. Authors, however, have an interesting finding in the reduced population of gut lamina propria and intra-epithelial compartment but did not examine the outcomes of such defects.

Major Concerns:

1) AMPK was previously found to be dispensable for the generation of effector T cells (cited papers 15,16). Please expand on the reasons for differing results of this paper. Similarly, in vivo experiments have found AMPK-/- T cells to be largely immunocompetent (cited paper 17). The authors' focus seems to be on homeostatic expansion but it is not clear what the importance of the requirement of AMPK for homeostatic proliferation is. Additionally, if Lamina Propria and IEL compartments are most affected when AMPK is absent in T cells, what is its outcome on gut immunity? Authors fail to examine this.

2) Much of the data presented in many of the figures is derived data presented as proportions or ratios of AMPK-KO to WT T cells.

3) The GVHD data presented in figure 3 makes the point that absence of AMPK reduces the severity of GVHD. Is this due to defective cytokine production/defective division/defective survival of transferred cells? Moreover these findings were already published in Blood in 2016.

4) The in vitro data do not substantially add to the author's point that homeostatic proliferation is defective in the absence of AMPK.

5) With regards to mitochondrial fitness, this was demonstrated in fibroblasts in the paper published in Cell Reports in 2017. Although it is interesting that AMPK has conserved properties in fibroblasts and T cells, this is not a conceptual leap.

6) The final figure in the paper has major caveats.(Figure 7H,I) Rescue of T cell proliferation in the presence of ROS scavenger. This experiment should be extended to show if the ROS scavenger rescues other defects like priming in the IL7+DC condition, IFNg production, Cxcr3 expression, GVHD pathogenicity.

Reviewer #1:

The study by Lepez et al, investigates the requirement for the metabolic sensor AMPK in the T-cell lineage. The analysis builds on genetic ablation that results in functional deficit of AMPK in the lineage to assess cellular response in homeostatic conditions, in response to antigen and in an in vitro cell culture system. The experiments are well executed and generally carefully controlled. The cell culture system allows the interrogation of mechanistic underpinnings at the cellular level in vitro and can be coupled with the validation of predictions in vivo.

AMPK regulation of cellular ROS homeostasis is one of the main outcomes reported in this work. However, the data supporting the latter are somewhat preliminary. Overall, in my view this work offers some advance on current knowledge but sufficient mechanistic insight is lacking at this juncture.

Concerns:

The experiments connecting AMPK signaling and ROS homeostasis are interesting but the evidence that ROS toxicity is inhibited by AMPK is largely correlative.

Nutrient sensing modalities are undoubtedly affected in AMPK deficient cells and the implications of these for ROS homeostasis are not evident in the analysis or discussion. For instance, AMPK control of redox regulation by the maintenance of cellular NADPH (Chandel's group) has been described and is a potential target that could be assessed in T-cells.

In Figure 7D, the WT cells show 70% mortality and the KO ~90% with differences maintained in the dose response analysis (S11). An important control would be the demonstration that (WT) cells are protected following treatment with an anti-oxidant/ scavenger. Further, does modulation of AMPK in WT cells - activation or inhibition - replicate the results seen with WT and KO cells?

The inclusion of another ROS perturbation such as mitochondria-targeted MitoParaquat will strengthen the assessment of differential susceptibilities in the survival/ ROS toxicity assays.

Given the rich literature on ROS regulation of T-cell function, the identity and characterisation of the ROS component[s] regulated by AMPK is necessary. This is relevant, as not only are there several sources of cellular ROS, their requirements are thought to be distinct in T-cell subsets.

Finally, the data presented do not account for the differential requirement of AMPK in T-cell subsets, which appears to be a major objective of the study. The conclusions of the study would be strengthened with an effort that establishes the identity of the ROS component and its interaction or regulation by AMPK.

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:

The manuscript examines the importance of AMPK in long term T cell fitness and proliferation and concludes that although AMPK is dispensable for early TCR signaling and short term proliferation, it is required for sustained long-term T cell proliferation and effector/memory T cell survival. The authors demonstrate that AMPK aggravates the severity of graft vs host disease and propose that AMPK enhances mitochondrial membrane potential in T cells to limit ROS production and associated toxicity and that ROS scavenging ameliorates these defects to an extent. However, causal connectivity claimed between the mitochondrial phenotype and the homeostatic proliferation defect is not established. The competitive bone marrow chimeras show the relative reduction of the AMPK-deficient genotype in the effector-memory T cell compartment, as predicted by previous literature. The more robust lack of AMPK-deficient T cells in the CXCR3-expressing subset and in gut lymphoid tissues is interesting, but no further mechanistic insights are offered into how AMPK specifically affects commitment to and or/survival in this compartment. Previous work on AMPK has shown that its absence does not affect T cell proliferation and also established that absence of AMPK affects GVHD (Beezhold, K et al, Blood (2016) 128 (22): 806) and that AMPK maintains homeostasis through regulation of Mitochondrial ROS (Rabinovitch et al, Cell Rep 2017 Oct 3;21(1):1-9. AMPK regulation of mitochondrial fitness, is previously demonstrated in fibroblasts (Cell Reports in 2017), and sufficient insight in constraining T-cell function is not provided. While the experiments are well executed and carefully controlled with several potentially interesting new observations, the study does not provide a sufficient advance to current knowledge or offer novel mechanistic insights into AMPK signalling in the mature T-cell compartment.