194 Matching Annotations
  1. Sep 2019
    1. Note: The peer reviews in Peerage of Science are judged and scored for accuracy and fairness by other reviewers. The Weight -value indicates that, relative to the best review (Weight=1.00)


      Review by Peer 4429 (Weight = 1.00)

      Introduction: The manuscript evaluates the use of genomic prediction in rice to prevent the accumulation of arsenic in rice grains. This is a food safety issue. Genomic prediction could be an appealing strategy for breeding of rice varieties less prone to accumulate arsenic in grains. Genomic prediction could bridge between current strategies based on land management (genetic improvement is cumulative and permanent) and recently proposed genome editing (for which target causal mutations need to be identified first).

      Merits: The study seems original in its proposal of genomic prediction for this particular problem. The authors contextualize in the Introduction the potential interest of genomic prediction against other strategies, including management and genome editing.

      The manuscript is quite broad in scope, as it tackles (1) genetic variation of the traits, (2) genome-wide association study GWAS, and (3) genomic prediction.

      Despite the low number of significant associations in the GWAS, some of the ones that are detected have annotation terms that could make them interesting candidates for further study.

      References are appropriate for the study.

      Critique: Because it covers so much ground, the manuscript is quite long and dense. I think it could be softened a little in some sections. Instead it feels a little bit rushed when it comes to genomic prediction, considering that several prediction methods and strategies are used.

      While genomic prediction is contextualized against other strategies in the Introduction, some of the results are not discussed as compared with other strategies. For example, there could be a greater effort to discuss the results of GWAS in light of the identification of targets required for genome editing (building on L327-336). There should also be a greater effort in discussing the several methods used for genomic prediction and potentially how genetic architecture from GWAS may help explain the differences between methods; for instance, if genomic prediction is concluded to be the best strategy, which method of all tested is recommended?

      I am not totally comfortable with the interpretation that the authors make of the comparison between phenotypic and genomic selection (L346-362). Phenotypic selection is producing 5 to 10% more genetic gain than the genomic (L344-345). This is a large difference that cannot be disregarded. The authors also claim that at equal cost of phenotyping and genotyping, genomic prediction would be preferred. While I agree with the logic that genomic data has the additional benefit that it can be applied to any trait, phenotyping of each of these potentials traits would also be needed with a certain routine to re-train the predictive equation. The authors acknowledge to some extent these points but, because overall phenotypic selection seems to be a better strategy for the specific case of arsenic tolerance and because the suitability of genomic prediction is established as dependent on genotyping costs, the title and conclusions seem a little bit misleading.

      It is clear that the paper was written with the Materials and Methods after the Introduction and it was later moved to the end of the manuscript. As a consequence, abbreviations are not properly defined when first read.

      Discussion: The manuscript offers a broad perspective on a topic of interest, affecting food safety, and proposes a sensible approach to mitigate it. The study is very detailed about the genetic variation of the traits and GWAS results and overall tackles all important points of discussion. However, it is slightly more vague on the genomic prediction section: several methods and strategies are tested but not described in the Methods section with enough detail and not thoroughly discussed. The authors conclude that genomic prediction would be a more suitable strategy to breed for arsenic-tolerant rice compared to other marker-assisted breeding strategies. However, it seems from the results that genomic prediction still underperforms compared to phenotypic selection and this should be put into context too. This manuscript contains some interesting research and it could be suitable for publication, but some revision is recommended as indicated.

      Additional Comments for Authors

      • L38: Be explicit. Mitigation of what?

      • L59: Please define "Aus genetic group".

      • L96: Be explicit. Which three traits?

      • Also L96: The distributions in Fig 1 seem to depart from a normal distribution.

      • Genomic prediction results: There is an n>p problem here, considering that 100 to 300 accessions but ~20,000 markers were used. Bayes A (one of the methods highlighted as most promising) fits all the markers in every iteration; Bayes B and C fit a pre-defined proportion of markers "pi" (could the authors specify to what value that parameter "pi" was set?); etc.

      • Revise English. Several typos and minor grammar errors.


    1. Note: The peer reviews in Peerage of Science are judged and scored for accuracy and fairness by other reviewers. The Weight -value indicates that, relative to the best review (Weight=1.00)


      Review by Peer 1755 (Weight = 1.00)

      Introduction: This paper presents a Bayesian model of mating in a fish, that combines behavioural data on encounters and matings with genetic parentage data. It contrasts this model with classical analyses that use only particular facets of these data.

      Merits: In my opinion, this paper's most important merits are:

      That the model makes conceptual sense, and is presented in a way that is fairly easy to follow.

      That the authors share the model code and data. This will make the model a lot more useful for other researchers.

      That the paper is well written.

      Critique: Despite this, I think there are things that could be clarified or improved:

      1. There seems to be a considerable skew in the reproduction data. This is expected, but this comes with a risk violating the assumptions of common statistical models. Does the models used adequately capture this? In particular, the correlation coefficients (Figure 1) must be largely driven by single influential data points.

      2. Given the above skew and structure of the data and that the model results extrapolates quite a bit from what was observed, it would be nice to see more through checks and discussion about the validitiy of the model. How well the model can reproduce features of the data? The posterior predictions in Figure 4 seem to indicate that the model fits data rather poorly? But I may be mistaken, and the manuscript does not interpret these results much.

      3. I got the JAGS model to run with only minor editing (that is, moving the data generating code to its own file). However, I can't, using the data in the script, recover the scatterplots and Pearson correlations displayed in Figure 1. I assume my analysis (see attached Sweave pdf output) is wrong somehow, suggesting a need for better documentation so that readers such as myself can understand the data. It may help to clarify what variables are what, which samples have been omitted (from what analyses and for what reasons), and store the data in tabular format in addition to the JAGS input format. It would also be a nice addition to have the code used for running the model and summarising the results -- it would save a user quite a bit of effort without much work on behalf of the authors.

      4. The sample sizes for data on releasing of gametes are particularly small. One wonders how much information they contribute? Similarly, both observations (line 248) and modelling (line 305-307) suggest that many encounters were not observed. How does this affect conclusions? This ability to deal with incomplete data is highlighted as a feature of the model. Is there arguments or data that show that it is successful?

      5. In the Introdution and Abstract, one of the motivations for this approach is to capture effects of interactions of the phenotypes within a pair. But then, "Unfortunately our dataset is too small to properly infer the effect of interaction" (line 428-429). First, previous the focus on this unused feature of the model seems misplaced. Second, it is not clear when a dataset is too small and how you know that (presumably by trying a model not shown?).

      6. I think this paper would benefit from more illustration. Figures 1 and 3 are hard to read with small differently shaped symbols, line patterns, and overplotting. I would suggesting making separate plots for males and females to alleviate some of the clutter. Figure 1 b is particularly unreadable. The plots of posteriors are fine, and probably should be in the paper, but I think they should be supplemented with some descriptive graphics that give a feel for the structure of the data and the behaviour of the fish. I would even love to see some visuals of fish mating, maybe stills from the video recordings (or even a supplementary video). Of course, this may be limited by space requirements of the target journal, or nor to the author's taste. But I think you underestimate how cool some of these things are, especially if you aim for a wide audience not well versed in fish mating research.

      Discussion: This is likely beyond the scope of this paper, but I feel that a lot of the questions about the model -- does it work on small datasets; does it successfully account for unobserved encounters; how does its parameters relate to the "classical" measures of sexual selection -- could better be answered with simulated than with real data. I sympathise the use of real data: a good biological example is a lot more convincing to biologists than simulations. However, I feel that there are often too many uncertainties in comparing methods on real data. Results of different methods differ, like the "classical" and the new analyses in this study. But which are right?

      Additional Comments for Authors

      1. The paper would benefit from a two sentence explanation of opportunity for selection, what it measures, and the distinction between opportunity for selection and opportunity for sexual selection.

      2. L8-10: The opening of the abstract sets up the paper to be rather technical, jumping directly into marginal sums of matrices. I think you may want to rethink that approach if the goal is too reach, as the author message said, "a wide audience of ecologists and evolutionary biologists".

      3. For the same reason, I'd advice against the introduction of a 3-dimensional array on line 34. Even if that is mathematically correct, it is immediately going to be summed to the a parental table. Therefore, the 3-dimensional structure doesn't really contribute much, except act as an obstacle to mathematically less savvy readers.

      4. L48-49: "strong link" could be made more precise.

      5. Line 123-124: "The experimental setup is the one used in the "constant environment" treatment in Gauthey et al. (2016)." What is the relationship between this work and Guthey et al 2016? Can this be made clearer?

      6. Lines 226: "po" is not defined in this section. I think the manuscript would benefit from being checked an extra time for mathematical symbols, when they are defined, how they are referred to, and if they can be spelled out in text to help the reader.

      7. Line 270: "Model output" is not a very informative subtitle. I'd suggest dividing the Results into one subsection on the data set, one on the "classical" analyses of sexual selection, and one on the model.

      8. Some of the chocies about model structure (specifically, use of informative priors) is discussed in comments in the model code, but not in the Methods. They should be in the Methods too.


      Review by Peer 1765 (Weight = 0.88)

      Introduction: This paper aims to solve a long-standing issue in sexual selection studies in natural populations: that genetic and behavioural data tell us different things about separate stages of sexuals selection and, therefore, often focus on different processes in sexual selection. While behavioural data tend to focus on mate sampling and mate choice, genetic data provide evidence on the resulting mating/reproductive success. This paper makes an important step in trying to combine both types of data in order to analyse the complete process of sexual selection. Such a tool could substantially advance the field of sexual selection in natural populations. I was very enthousiastic about this approach, until I arrived at Figure 4, which shows that the predictions from model the authors suggest does not correlate at all with the observed data from their case study, suggesting the model is possibly very well thought through, but does not represent the data well. Without empirical evidence, I do not see any reason to put the results of the model above those of the classical methods.

      Merits: The paper describes the model used in a way that is mostly very clearly understandable for non-modelers, which is important for the general use of the proposed method. Moreover they include a case-study which very nicely links the theory to experimental data.

      Critique: The suggested model provides different results from more classical methods of analysing the data. The authors then go on to defend the model as a better way to analyse the data, because they find different results. However, they do not provide evidence that the results from the model fit the data better than the results from the classical analyses. In fact, Figure 4 shows that the model is actually rather bad in predicting observed encounter rates, gamete releases and offspring numbers, because there seems to be no correlation whatsoever between observed and predicted data. For example, many females that did sire large numbers offspring were not predicted to have any offspring according to the model (Fig. 4c). This is not discussed in the paper. I do commend the authors for testing their model on a case study, and combine a theorethical appraoch with an experimental one, but the difference between predicted and observed data should be discussed. The authors could compare the model predictions to the predictions from the classical analyses and see which analyses fit best with the observed data.

      Terminology: Encounter rate is a term that is generally reserved for random events depending on population density and sex ratio. However, the way it is used in the case study (which is certainly the most practical for field observations) includes a certain effect of attraction. In most species, males and females do not generally end up close to a spawning ground/ nest without being attracted by some aspect of the individual or this particular nest. The authors are likely aware of this, because they test for an effect of female size on encounter-rate. The fact that they do not find such an effect does not exclude that their may have been attraction to other characteristics of the female or the nest-site. Therefore, I would suggest to use another word for encounter (for example inspection or visit) to avoid confusion between an event where individuals have likely already been attracted to each other (as used in the case study) and a random "encounter". The latter is, however, impossible to quantify in the field, because it is generally impossible to spot whether two individuals have noticed each other and I see no reason to include it in the model.

      Discussion: The paper addresses a very important issue in the study of sexual selection: how to combine behavioural and genetic data to study the strength of sexual selection. As the authors rightly argue, both types of data omit important processes in sexual selection and very few studies manage to get both types of data for all (or even most) mating events. The model they suggest would make use of incomplete behavioural and genetic data to explain the underlying processess. Such a model could provide an important tool for sexual selection studies. However, the case study the authors provide suggests that the model is not very good at predicting real case scenarios. Therefore, the autors should investigate how the model could be changed to reflect their experimental data. Doing so would provide an important paper that would be very valuable to the field.


      Review by Peer 1758 (Weight = 0.85)

      Introduction: This manuscript offers a statistical alternative to classical sexual selection gradient analysis by using Bayesian inference that allows accounting for male and female effects simultaneously. Furthermore, the authors highlight that mating success is generally underestimated because it is based on the genetic assignment of offspring. The authors use their own data on the mating behaviour and reproductive output of brown trout to compare the results from classical selection analysis with their Bayesian model and find differences between the two.

      Merits: This manuscript is relevant because it highlights limitations of classical sexual selection gradient analysis, and offers a statistical alternative to empiricist with suitable data. I have the following suggestions, which I hope will be useful in revising the authors' original contribution. Also, I welcome that the authors made their research transparent by adding their data and code. However, I want to make clear that I could not review their code because of incompatibilities with JAGS and my software. ​

      Critique: The authors statistical alternative is motivated by two shortcomings to (a) account for the interdependence of females and males in sexually reproducing species and (b) getting a grip on the copulatory behaviour instead of inferring it from offspring data. Whilst I agree that (b) is pressing, (a) depends on the mating systems, e.g. in strictly monogamous species, male and female identity overlap and fitting both would not be informative or appropriate for the analysis of sexually selected individual phenotypic traits. Hence, the applicability of the authors' model would profit from information on its suitability for different mating systems, i.e. expand on "a variety of biological systems", l24, in the discussion. Also, the authors approach also relies on empirical data. In other words, the best model does not change that if mating success lacks behavioural observations, and it usually does, we can only make incomplete inferences. In my view, the main contribution of this manuscript is thus to serve as an important reminder of the complexities at play and the importance of comprehensive data collection, rather than a new tool for measuring sexual selection. Also, the pitfalls and shortcomings, (e.g. bias in stochasticity, what is the null model, operational sex ratio) when measuring sexual selection have been comprehensively illustrated here (Klug, Heuschele, Jennions, & Kokko, 2010) and here (Jennions, Kokko, & Klug, 2012). So, I recommend a more inclusive portrait of the matter and attuning with published jargon (e.g. Table 1 in (Klug, Heuschele, Jennions, & Kokko, 2010).

      • I advocate that the full results of the linear regression analyses as well as the alternative JAGS model are presented in table format in the main text. Results in the supporting information get missed easily, and plots cannot substitute full estimates.

      • The authors could expand more on discussing their most interesting finding, which is the discrepancy between their results using classical regression analyses and Bayesian analysis.

      Discussion: This manuscript is motivated by two shortcomings of the classical sexual selection gradient analysis. I agree with the relevance of one of them (i.e. measuring mating success) and yet argue that the relevance of accounting for the additive effects of the sexes for reproductive success is highly dependent on the species mating system, which the authors should address. I also think that the authors should make clearer that their analysis still depends on empiricists collecting data on mating success. I welcome the authors approach to use their own data to compare whether body size of male and female brown trout might be sexually selected. If the authors revise the current version, their manuscript will serve as an important reminder of what to look out for when analysing potentially sexually selected traits.

      References Jennions, M. D., Kokko, H., & Klug, H. (2012). The opportunity to be misled in studies of sexual selection. Journal of Evolutionary Biology. http://doi.org/10.1111/j.1420-9101.2011.02451.x

      Klug, H., Heuschele, J., Jennions, M. D., & Kokko, H. (2010). The mismeasurement of sexual selection. Journal of Evolutionary Biology. http://doi.org/10.1111/j.1420-9101.2009.01921.x

      Schlicht, E., & Kempenaers, B. (2013). Effects of social and extra-pair mating on sexual selection in blue tits (Cyanistes caeruleus). Evolution, 67(5), 1420-1434. http://doi.org/10.1111/evo.12073

      Additional Comments for Authors l14: be clearer on "costly" or delete because costs were not measured

      l27: add or consider selection gradient, see Table 1 in Klug et al 2010

      l44: ambiguous "to do so". Which of the indices exactly?

      l52 infertile not unfertile

      l53 reference "cost of reproduction"

      l64 reference costs

      l65 back up the claim of "are essential to understand..."

      l68 better name the "fourth definition"

      l88-89 reference

      l93 define "a pair", e.g. socially monogamous? This could be an opportunity to introduce the mating system you want to target

      l109-111 reference?

      l113-115 reference?

      l116 in brown trout? Please add citation

      l120 "a" semi-natural...

      l120-123 split into two sentences to improve readability, e.g. This period represents the trout...

      l124: chemically communicated?

      l129: highly female biased, which might be biological meaningful or a catching bias, please explain. Plus this skew in adult sex ratio will affect the variance in mating success, i.e. "chance variation in mating success is higher when there are fewer potential mates per individual of the focal sex" (Jennions et al 2012), this affects both your statistical approaches but it nowhere mentioned

      l132 how did you sex? Molecularly?

      l145: one or multiple observers? also "taken" not "took"

      l148 any proof? repeatability tests? references for the claim?

      l149 say how you dealt with the 30% for analyses

      l150 rephrase "the zone", e.g. female nesting/egg release site, etc.

      l156 consider "spawning" or gamete release instead of copulating

      l159 "degree day" reads misplaced, only use estimate of time after spawning

      l172 its

      l186 consider making clearer that zero's were included

      l247 depending on where you want to submit avoid fish jargon: "redd"

      l249 give output of all linear regression analyses in table

      l271 I suggest moving these to the main text

      l278 why not report Credible Intervals instead of SDs? Also, SDs show high uncertainty in estimates, which should be addressed in the discussion

      l333-4 reference

      l336 rephrase "to account for..."

      l335 give time unit, e.g. over the course of the experiment

      l336 Comment: I disagree because sexual selection is commonly referred to as the opportunity for evolutionary change, which is the variance in relative fitness and should consider all reproductively mature adults, hence should be measured among individuals that do and do not interact/mate. Especially the latter is usually omitted, but ignoring unmated individuals in a population will automatically inflate the variance of the successful subset (see also (Schlicht & Kempenaers, 2013)).

      l418-19 rephrase, unclear

      Plots: General comment: It might be the pdfs but the quality of plots is low and generally offsetting the raw data a bit, e.g. jittering would help viewing individual data points


      Review by Peer 1761 (Weight = 0.67)

      Introduction: The authors point out how the study of mating systems only using behavioural observations or genetic data usually fails to explain accurately the breeding processes and reproductive outcomes, as well as their relationship with sexual selection features.

      They propose a model that combines both behavioural and genetic data, and a phenotypic trait linked to sexual selection, using brown trout as model species.

      Their model includes several breeding variables behavioural and genetic, and it very adaptable as is able to incorporate other environmental or biological variables if needed.

      They show how genetic and behavioural results analyzed separately may differ. Also, how the results from their model and the classic regression analyses to analyse this data also differ, and so, they aim to explain why.

      Merits: The model they have built seems flexible enough to be adapted to multiple taxa and systems.

      Critique: There is no reference at all about ethics permissions to perform the described experiment. I am quite shocked about this since high numbers of individuals from a wild population were killed.

      There is no mention on the conservation status of the species, the permits obtained to carry out the capture and experiment, the effect of the capture system on the ecosystem, or the explanation/justification for the use of lethal methods.

      For example, I find electrofishing highly non-targeted and I wonder how was its impact on other non-target fish (and non-fish) species. I believe that assembling a team of fishermen to get the same number of adult specimens would be easy enough to arrange.

      My point is not whether the methods were ethically acceptable or not (that is for the journals' ethics committees to decide) but to, at least, justify and explain their use.

      Model testing: I understand that in ecology studies usually researchers don't get all behavioural or all genetic data, and that is what the models try to compensate for. However, when testing models in a biological system the ideal situation is to work in a system where almost all information can be collected (ussualy under lab conditions), build a model with all that information, and then subsample the data (as to simulate a real ecological study) to test the model performance.

      In this study, however, the initial sampling for the data is quite small, specially for behavioural observations (30min/day). Then, the results from the model are quite different from the results obtained from more classic approaches. The authors offer some hypotheses to explain these differences, but they can't be really tested to see whether the authors' model results are better in explaining the system or not.

      All that said, I have to admit that I lack the mathematical background to fully understand and evaluate the model design and performance, and a more qualified researcher should do that.

      Discussion: Although the experimental approach to test the validity of the model predictions could have been better, their attempt to combine behavioural and genetic data in mating system studies and relate it to sexual selection is an important step forward in the behavioural field.

      Hopefully, more efforts like this will be made to reconcile both aspects of the study of mating systems that rapidly changed from behavioural observations only to genetic analyses only.


      Review by Peer 1773 (Weight = 0.51)

      Introduction: In accordance with traditional approach to estimate the effect of sexual selection on phenotypic trait the number of mates should be regressed on a target phenotypic trait in a separate model for each sex. Such analysis ignores common investment of the sexes into mating success. The authors propose a new approach, which allow combining behavioral and genetic data, thereby enabling to gather information through the successive processes of encounter, gamete release and offspring production.

      Merits: The new approach accounted for the three-dimensional structure of the data: males, females and mating occasions. This allowed a qualified definition of mating success and disentangling the joint effects of male and female phenotypes on the different components of reproductive success. Three important features that lack in the traditional approach characterize the authors' model:

      1) conditioning of each process (encounter, gamete release and offspring production) on the preceding one,

      2) simultaneous estimation of the effect of male and female phenotype,

      3) random individual effects.

      ​The authors tested their model on a brown trout and obtained quite different results for the two approaches.

      ​The model can be used for a variety of biological systems where behavioral and genetic data are available.

      Critique: The model should be tested on a larger sample.

      The title of the manuscript is not very successful.

      ​There is a couple of misprints: p. 7 l. 139 and p. 8 l. 159.

      Discussion: This is very important when new algorythms allow to obtain more information from the same set of data. Hopefully, it would be of great importance if the model can be developed to account for real behavior traits in species presenting complex courtship behavior like Drosophila for instance.

    1. [Note: this preprint has been peer reviewed by eLife. The decision letter after peer review, based on three reviews, follows. The decision was sent on 21 May 2019.]

      Summary

      Masachis, Darfeuille et al. analyse a type I toxin - antitoxin (TA) module of the major human gastric pathogen Helicobacter pylori (Hp). Expression of toxins encoded by Type I modules is controlled by small, labile, cis-encoded antisense RNAs and often also by complicated mRNA metabolism that envolves conserved mRNA folding pathways and/or mRNA processing. Using a combination of elegant and robust in vitro and in vivo methods, the authors first show that that the aapA3/IsoA3 TA system of Hp is regulated in a way very similar to that of the homologous aapA1/IsoA1 system from the same organism (Figs 1 and 2). This initial part of the manuscript sets the stage for the next step, where the authors employ a powerful genetic screen combined with deep sequencing to identify single nucleotide changes that abolish production of the AapA3 toxin (Fig. 3). This principle, which was invented by the authors, is technically robust, intellectually attractive and very powerful, and may yield novel insights that at present cannot be reached by other approaches. In particular, the authors discover that single point mutations outside the toxin gene reading frame suppress toxin gene translation. Focusing on the translation initiation region, they discover two mRNA hairpin structures that, when stabilized by single base changes, reduce translation by preventing ribosome binding (Figs 4-6). They propose that these structures are metastable and form during transcription to keep the toxin translation-rate low, as explained in the model figure (Fig. 7).

      Essential Revisions

      All of the reviewers thought the quality of the experimental work in the manuscript is outstanding and the conclusions are justified. However, all thought it would be nice to have additional evidence of the proposed metastable structures in the nascent toxin mRNA. While the reviewers understood this might be technically difficult, they agreed that it is worth a try and had the following suggestions.

      1) Phylogeny (i.e. nucleotide co-variation in sequence alignments) was previously used to deduce the existence of stem-loop structures not only in ribosomal RNAs but also in mRNAs (e.g., hok mRNAs). Did the Authors consider using this approach to support the existence of the proposed metastable structures in the nascent toxin transcript? This possibility depends on the actual homologous sequences available and is not possible in all cases. If phylogeny indeed supports the existence of the metastable structures, the Authors could look for coupled nucleotide covariations that would support a conserved mRNA folding pathway (that is, one mRNA sequence elements pairs with two or more other elements during the fife-time of the mRNA) . The Authors state in the Discussion that "these local hairpins were previously predicted to form during the co-transcriptional folding pathway of several AapA mRNAs (Arnion et al., 2017)." However, they authors did not explain how these hairpins were predicted. It is worth explaining this central point.

      2) Although transient structures are by definition hard to detect, the authors could try in vivo structure probing (DMS) of truncated mRNAs 1-64 and 1-90 to demonstrate the existence of the first and the second metastable structures, respectively.

      3) It is preferable to carry out 2D structure predictions on the naturally occurring transcript, not a sub-sequence. 2D structure prediction generated by algorithms such as RNAfold (or Mfold) that are guided by delta-G stability optimisation are sensitive to the sequence context, so the correct sequence needs to be used to be able to draw conclusions. Additionally, the findings presented in Figure 3D could be analyzed a bit further to produce significant, independent evidence for some structure features. Specifically,

      Figure 2 caption:

      • lines 184 - 186: "2D structure predictions were generated with the RNAfold Web Server (Gruber, Lorenz, Bernhart, Neuböck, & Hofacker, 2008) and VARNA (Darty, Denise, & Ponty, 2009) was used to draw the diagrams."
      • Please state clearly whether any of the results of the experimental 2D structure probing were used as input to RNAfold (i.e. as additional constraints to the prediction algorithm).

      Figure 3D:

      • Please add coloring to the peaks depending on which codon position they overlap (1, 2 or 3) and carefully discuss the corresponding results, also in the context of the 2D structure elements.
      • Given that you have a decent number of pair-mutations, analyze them to see whether any correspond to RNA structure base-pairs (and whether any of the pair mutations rescue the base-pair and thus affect the system differently). This would serve as additional, independent evidence of 2D structure probing and predictions.
    1. [Note: this preprint has been peer reviewed by eLife. The decision letter after peer review, based on three reviews, follows. The decision was sent on 17 June 2019.]

      Summary

      Natural Killer (NK) and the ILC1 subset of innate lymphoid cells share related functions in host defense but have been argued to arise from distinct pathways. Park et al present new evidence challenging this concept. They show that murine Toxoplasma gondii infection promotes the differentiation of NK cells into an ILC1-like cell population which is stable and long-lasting, even after the infection has been cleared. These T. gondii induced cells, unlike Eomes+CD49a- NK cells, are Eomes-CD49a+T-bet+ and therefore resemble ILC1 cells. The authors additionally show that their differentiation involves Eomes down regulation and is STAT-4 dependent, However, in common with NK cells and distinct from ILC1 the T. gondii induced "ILC-like" population circulates to blood and lungs. Finally, the authors employ single cell RNAseq to examine the heterogeneity of the major T. gondii induced innate lymphocyte populations and their NK vs ILC relatedness as assessed by gene expression. Together, their observations establish a previously unappreciated developmental link between NK and ILC1cells in the context of infection.

      The 3 reviewers and editor agree that this is an important contribution that sheds new light on the developmental relationship of NK and ILC1 cells, a scientific issue that has received considerable attention in the innate immunity field. Although extensive, most of the criticisms raised can be addressed by revisions to the manuscript. One additional experiment is requested to provide a missing control.

      Essential Revisions

      All reviewers had a major concern about how this new population of T. gondii induced innate cells should be referred to in the manuscript. Based on the single cell RNAseq data, these cells (cluster 10) are still closer to NK cells than to ILC1s (Figure 5f and Suppl Fig 4e) despite their loss in Eomes expression and acquisition of CD49a expression. Thus, one could easily think of them as "Eomes negative NK" or "ex-NK" cells rather than ILC1s, and to simply refer to them as Eomes-CD49a+ ILC1 cells may be misleading . For this reason, the authors should modify the title of the paper and change their designation throughout the manuscript. We suggest "ILC1-like" as a good descriptor. In addition, although it is clear that the "Eomes negative NK" cells that are generated during T. gondii infection are transcriptionally and epigenetically distinct from the NK cells in the steady state and NK cells after infection (Figure 7 and suppl Figure 6), these "Eomes negative NK" cells referred to as "T. gondii-induced ILC1s" were not directly compared with classical ILC1s. Based on the single cell RNAseq data, these cells may not express many of the ILC1-related signature genes. Therefore, again, the authors need to be cautious in referring to them as ILC1 cells.

      A second concern was that the NK 1.1 depletion shown in Supplemental figure 1 was performed with a PBS rather than isotope matched immunoglobulin control which is considered unacceptable. The authors should repeat at least once with proper control Ig to make sure this is not issue. It is not necessary to repeat entire survival curve just experiments shown in A and B and initial survival to make sure there is no death in controls vs. antibody treated.

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      Reply to the reviewers

      Referee #1

      In this study the authors identify RASSF1A, the Hippo kinase regulator, as a regulator of actin monomer levels in the nuclear compartment via interacting with exportin 6, the specific actin export factor, as well as with the Ran GTPase. This leads to changes in actin-dependent gene regulation and may have functional effects on cell adhesion, all supposedly mediated by subsequent changes in the activity of MRTF-A and SRF. Finally, the authors try to correlate their findings with clinical data of invasive carcinoma. Overall, the findings are interesting since they identify a novel player in the nuclear actin-MRTF module, however, several further controls are needed.

      We would like to thank the reviewer for recognising the novelty of our work. Below there is a detailed description of all the experiments and changes performed to answer their concerns.

      1. Fig.2C the quantification of effective-knockdowns should be included; RASSF1A decrease resulted from MST2 needs to be confirmed via Western blot.

      We now include these data on Figs EV1A and EV2C. The lack of RASSF1A immunofluorescence is due to redistribution away from the NE (Fig 2C), as the total and nuclear protein levels of RASSF1A do not change in MST2-depleted cells (EV2C and EV2D).

      1. It is claimed that SARAH domain is responsible for the interaction, therefore, in Fig. 3B it is necessary to rule out the involvement of RA domain by introducing a 288-340 mutation.

      We agree with the reviewer that the truncated RASSF1A expressing only the SARAH domain is missing, however the SARAH domain alone is not stable and expression was ineffective (as previously found). In light of this we have reworded the text to fit the data by describing the observation at the SARAH domain being ‘required’ for the interaction rather than responsible.

      1. Fig. 3C as the co-immunoprecipitation assay showed, Ran recruitment to the RASSF1A/XPO6/RanGTP complex is totally abolished. Could this be seen in staining as well? The same concern also exists in the Fig. 3D, disturbed formation of the complex after MST2 depletion. Additionally, since MST2 is not involved in the RASSF1A/XPO6/RanGTP complex, how come it affects the complex formation? What is the mechanism?

      This is an important aspect of the manuscript that we did not originally focus on and also a concern of Rev 2 (point 2) and Rev 3 (point 1), however we now provide further experiments to elucidate a potential mechanism where we expand on XPO6 IP +/- RASSF1A and RASSF1A IP +/- MST2 (new Fig 3C,E). We provide additional XPO6 IP (+/- RASSF1A and +/- MST2) together with MST2 IP (+/- RASSF1A and +/- XPO6) to delineate hierarchy of associations and put the complexes in context of the NE association. These additional data indicate that XPO6 and RAN interact independently of MST2, with limited involvement of RASSF1A (or at a reduced level). However, the dependence of XPO6/RAN stability on RASSF1A appears to be restricted to MST2 being present, which we interpret to be due to NE recruitment. We also further support RASSF1A involvement by employing a recombinant RAN binding assay where XPO6 association is reduced in the absence of RASSF1A (new EV3B). We have modified the text to explain this mechanism as below;

      ….We further investigated the role of RASSF1A on the association of RAN with XPO6. Most strikingly, RASSF1A appeared to be required to support the XPO6/RAN complex, as siRNA-mediated knockdown of RASSF1A decreased association between XPO6 and RAN (Fig 3C). Expression of RASSF1A in MDA-MB-231 cells significantly enhances the association of XPO6 with RAN (EV3A). We validated this requirement for RASSF1A with a GST pull-down assay using recombinant GST-RAN and lysates from siCTRL or siRASSF1A-transfected HeLa cells (EV3B). Notably, XPO6 co-immunoprecipitation (IP) indicated that the XPO6/RAN complex with RASSF1A also includes MST2, suggesting potential recruitment to the NE via the RASSF1A-MST2 interaction (Fig 3C). Depletion of MST2 expression using siRNA did not affect XPO6/RAN as dramatically as siRASSF1A, but did reduce XPO6/RASSF1A, which we believe implies that RASSF1A may be required for stabilising XPO6/RAN at the NE, i.e. in an MST2 dependent manner, but the nucleoplasmic XPO6/RAN pool may be less dependent on RASSF1A (Fig 3C). This is supported by the fact that the RASSF1A interaction with XPO6/RAN is also dependent on MST2, and therefore NE localisation (Fig 3D). To verify this mechanism, we explored MST2 associated proteins by IP and found that XPO6/RAN interaction with MST2 was RASSF1A dependent whereas the RASSF1A/RAN interaction with MST2 did not require XPO6 (Fig 3E), confirming our hypothesis that XPO6/RAN complex is stabilised by MST2/RASSF1A interaction.

      Taken together, our results show interaction of XPO6 with RAN can occur independently of RASSF1A, but a pool of XPO6/RAN is stabilised by RASSF1A in a MST2 dependent manner at the NE.

      We have also looked at whether this model could be supported by IF (Fig for reviewers 1, below). Suppression of RASSF1A expression does appear to reduce the nuclear staining of RAN, and as total levels of RAN are unaffected (Fig 3C,E), this implies redistribution to the cytoplasm. As staining of XPO6 is unaffected this supports the biochemical data that the XPO6/RAN complex is reduced. Moreover, it also suggests that RASSF1A might be important to maintain RAN.GTP levels, and RAN.GDP is cytoplasmic, and this may impact on the complex formation. As this requires much further thorough investigation we feel it is too preliminary to include in this story, but have included the following statement in the discussion.

      .. the reduced involvement of RASSF1A in the XPO6/RAN complex in the absence of MST2 suggests that RAN/XPO6 exists independently of RASSF1A in the nucleoplasm. This means that XPO6/RAN complexes may be contextually distinct from RASSF1A/RAN/XPO6 and could involve differences in substrate loading, RAN GDP/GTP loading or post translational modifications of RAN (Guttler and Gorlich, 2011 EMBOJ, Dallol et al, 200, de Boor et al. 2015 PNAS, Bompard et al 2010 jcb).

      Figure for Reviewers 1 <not available on hypothes.is>

      1. Fig.4 is not entirely convincing. All conclusions on nuclear actin levels are based on biochemical fractionations, which can be often problematic. Besides, effects of siRASSF1A need to be rescued by siRNA resistant wt versus SARAH domain deletion derivatives! This is important and necessary. The biochemical analysis of cleat actin levels needs to be complemented by nuclear actin visualizations either with endogenous actin or at least using GFP-actin.

      We originally performed fractionations as the visualization of endogenous nuclear actin is particularly challenging and usage of phalloidin could stabilise actin filaments (Coluccio and Tilney, 1984; Visegrády et al. 2004). It has been shown also that phalloidin might not bind to all the actin structures present in the nucleus as it requires at least seven actin subunits for binding to F-actin, neglecting labelling of short F-actin polymers (Kristó et al., 2016). Moreover, overexpression of epitope-tagged actin can be problematic, as even a subtle change in the amount of actin can interfere with the physiological actin dynamics, and could trigger actin polymerization by itself (Mounier et al., 1997; Ballestrem et al., 1998). However, we did try to visualise nuclear actin filaments (Phalloidin) and actin monomers (DNase I) and although we did not observe any change of the levels of filamentous actin in the nucleus, we now show increased monomeric actin in RASSF1A-depleted cells. These data are now shown in Fig 4C and EV4F.

      It is indeed necessary to validate our results with rescue experiments. Therefore as suggested, we add a new set of experiments in Fig EV4A-C where the effects of RASSF1A silencing on nuclear actin and profilin levels were rescued by co-transfection of siRASSF1A with either SARAH-containing RASSF1A derivatives (but not by SARAH-domain truncated) or plasmids encoding for XPO6. Increase of nuclear actin and profilin in RASSF1A silenced cells was also rescued with a siRNA resistant RASSF1A expression plasmid.

      1. Could the effect of RASSF1A depletion on nuclear actin levels be rescued by overexpression of XPO6? This would more directly confirm XPO6 is downstream of RASSF1A. In fact, rescue and reconstitution studies would be highly desirable.

      This is a very interesting point and we thank the reviewer for this suggestion. We now include the results in Fig. EV4B

      1. How does RASSF1A affect MRTF-A? The authors should study MRTF-A (also known as MAL, or MKL1!) actin interactions directly in the presence or absence of RASSF1A.

      We found that increased nuclear G-actin resulted from RASSF1A silencing leads to increased actin-MRTF-A interactions. We include these data in Fig. EV5C.

      1. What happens to nuclear F-actin in RASSF1A silenced cells? Did the author make efforts to visualize endogenous nuclear F-actin? This would be interesting and provide more and better mechanistic insight, since it has been shown in several studies that nuclear actin assembly regulates MRTF-A or MKL1 or MAL activity. It is also well established by now that nuclear actin is dynamically polymerized by various cellular cues and inputs. Hence, does an increase in nuclear actin levels lead to actin polymerization or changes of nuclear F-actin in this compartment?

      This is very interesting point and related to point 4. Probing endogenous F-actin by using fluorescently labelled phalloidin showed no difference of nuclear actin filaments between control RNA-treated cells and cells silenced for RASSF1A, as shown in Fig EV4F. Interestingly, visualisation of G-actin using fluorescently labelled DNase I revealed increase nuclear G-actin in RASSF1A silenced cells (Fig 4C). This is in agreement with our data showing cytoplasmic MRTF-A (Fig 5C) as increased nuclear G-actin promotes the nuclear export of MRTF-A (Vartiainen et al. 2007).

      Referee #2

      The manuscript by Chatzifrangkeskou et al. describes a novel role for RASSF1A tumor suppressor gene in regulating nuclear export of actin, and thus also MRTF-A-SRF mediated transcription. RASSF1A is a member of a protein family acting upstream of the Hippo-pathway, binding directly to the MST1 and 2 kinases of the Hippo pathway, and its inactivation is implicated in the development of various cancers.

      In the present manuscript, the authors broaden the functional aspects of RASSF1A by linking it to regulation of nuclear actin levels. Actin has been shown to shuttle in and out of the nucleus with the aid of transport factor Importin-9 and Exportin-6, but further regulators are poorly characterized. The authors first show that a pool of RASSF1 can be found on the nuclear envelope, and that this localization is dependent on MST2. Based on the previous data on the interaction between RASSF1 and the Ran-GTPase, which is the major driver of energy dependent nuclear transport, the authors then identify an interaction between RASSF1 and Exportin-6, and surprisingly find that RASSF1 is required for the interaction between Exportin-6 and Ran. In cells, depletion of RASSF1 leads to increased nuclear accumulation of actin and profilin, as well as to decreased expression of specific genes previously linked to nuclear actin, cell adhesion defects and to decreased nuclear localization of the transcription coactivator MRTF-A and consequently decreased SRF activity. Finally, the expression of SRF and RASSF1A are correlated in various cancer cells.

      The outset for the manuscript is very interesting, and the idea that the nuclear actin pool, and consequently gene expression, would be regulated by a tumour suppressor is exciting. However, the mechanism by which RASSF1A operates here remains somewhat unclear, and further experiments as well as quantifications would be needed to support the key hypothesis.

      Major concern

      1. First, how is the NE localization of RASSF1 related to whole business? How would the NE localized RASSF1A contribute to the formation of the Exportin-6-Ran-actin export complex, especially since MST2 does not seem to be in the complex? MST2 seems to be required for RASSF1A localization to the NE, but can it be excluded that it also regulates the nuclear localization of RASSF1A? In these experiments, the subcellular localization of RASSF1A should be analyzed quantitatively from a large number of cells (or by fractionation) to draw any general conclusions. Analyzing actin distribution in MST2 depleted cells (in case it does not affect nuclear localization of RASSF1A per se) would tell, if the NE localization of RASSF1A is important for regulating nuclear actin.

      We thank the reviewer for this suggestion. The nuclear localization of RASSF1A is not affected by the depletion of MST2 as evaluated by both immunofluorescent staining and fractionation (Fig EV2D, EV4D). However, the MST2-dependent RASSF1A NE localisation is important for the regulation of nuclear actin levels as shown by the altered nuclear actin levels in MST2-depleted cells (Fig EV4D).

      1. Second, I am very surprised by the huge effect that RASSF1 depletion has on Exportin-6-Ran interactions (figure 3C), especially since it seems that the depletion of RASSF1 is not very efficient. Moreover, Exportin-6 has been shown to interact directly, like most other nuclear transport factors, with Ran (shown for example in Stuven et al. 2003). Why would the interaction in cells then require an additional factor? The IPs in figures 3C and D should be carefully quantified from several experiments to draw firm conclusions on these experiments. Related to this point, did the authors check the subcellular distribution of Exportin-6 in RASSF1A depleted cells?

      This is essentially the same issue raise by Rev1 (point 3) and Rev 3 (point 1), and an important aspect of the manuscript that we did not originally focus on, however we now provide further experiments to elucidate a potential mechanism where we expand on XPO6 IP +/- RASSF1A and RASSF1A IP +/- MST2 (new Fig 3C,E). We provide additional XPO6 IP (+/- RASSF1A and +/- MST2) together with MST2 IP (+/- RASSF1A and +/- XPO6) to delineate hierarchy of associations and put the complexes in context of the NE association. These additional data indicate that XPO6 and RAN interact independently of MST2, with limited involvement of RASSF1A (or at a reduced level). However, the dependence of XPO6/RAN stability on RASSF1A appears to be restricted to MST2 being present, which we interpret to be due to NE recruitment. We also further support RASSF1A involvement by employing a recombinant RAN binding assay where XPO6 association is reduced in the absence of RASSF1A (new EV3B). We have modified the text to explain this mechanism as below;

      ….We further investigated the role of RASSF1A on the association of RAN with XPO6. Most strikingly, RASSF1A appeared to be required to support the XPO6/RAN complex, as siRNA-mediated knockdown of RASSF1A decreased association between XPO6 and RAN (__Fig 3C). Expression of RASSF1A in MDA-MB-231 cells significantly enhances the association of XPO6 with RAN (EV3A). We validated this requirement for RASSF1A with a GST pull-down assay using recombinant GST-RAN and lysates from siCTRL or siRASSF1A-transfected HeLa cells (EV3B). Notably, XPO6 co-immunoprecipitation (IP) indicated that the XPO6/RAN complex with RASSF1A also includes MST2, suggesting potential recruitment to the NE via the RASSF1A-MST2 interaction (Fig 3C). Depletion of MST2 expression using siRNA did not affect XPO6/RAN as dramatically as siRASSF1A, but did reduce XPO6/RASSF1A, which we believe implies that RASSF1A may be required for stabilising XPO6/RAN at the NE, i.e. in an MST2 dependent manner, but the nucleoplasmic XPO6/RAN pool may be less dependent on RASSF1A (Fig 3C). This is supported by the fact that the RASSF1A interaction with XPO6/RAN is also dependent on MST2, and therefore NE localisation (Fig 3D). To verify this mechanism, we explored MST2 associated proteins by IP and found that XPO6/RAN interaction with MST2 was RASSF1A dependent whereas the RASSF1A/RAN interaction with MST2 did not require XPO6 (Fig 3E), confirming our hypothesis that XPO6/RAN complex is stabilised by MST2/RASSF1A interaction.

      Taken together, our results show interaction of XPO6 with RAN can occur independently of RASSF1A, but a pool of XPO6/RAN is stabilised by RASSF1A in a MST2 dependent manner at the NE.

      As suggested, we have also looked at XPO6 and RAN distribution (Fig for reviewers 1, above). Suppression of RASSF1A expression does appear to reduce the nuclear staining of RAN, and as total levels of RAN are unaffected (Fig 3C,E), this implies redistribution to the cytoplasm. As staining of XPO6 is unaffected this supports the biochemical data that the XPO6/RAN complex is reduced. Moreover, it also suggests that RASSF1A might be important to maintain RAN.GTP levels, and RAN.GDP is cytoplasmic, and this may impact on the complex formation. As this requires much further thorough investigation we feel it is too preliminary to include in this story, but have included the following statement in the discussion.

      .. the reduced involvement of RASSF1A in the XPO6/RAN complex in the absence of MST2 suggests that RAN/XPO6 exists independently of RASSF1A in the nucleoplasm. This means that XPO6/RAN complexes may be contextually distinct from RASSF1A/RAN/XPO6 and could involve differences in substrate loading, RAN GDP/GTP loading or post translational modifications of RAN (Guttler and Gorlich, 2011 EMBOJ, Dallol et al, 200, de Boor et al. 2015 PNAS, Bompard et al 2010 jcb).

      1. Third, the results in figures 4C and 4D on MDA-MB-231 cells are very clear, and the data seems to imply that due to the lack of RASSF1A, these cells have relatively high levels of nuclear actin. However, the Treisman-lab has shown that in these cells, MRTF-A is actually nuclear (Medjkane et al. 2009, NCB), which is exactly the opposite that you would expect, and not in agreement with the subsequent results in figure 5. What is the explanation for this?

      Indeed, the report from Medjkane et al. showed that MDA-MB-231 cells express high levels of RhoA-GTP and therefore MRTF-A is predominantly nuclear. However, RhoA promotes the polymerization of G to F-actin in the cytoplasm as well as in the nucleus. We speculate that the high nuclear actin levels in MDA-MB-231 exist in filamentous state due to the active RhoA signalling. Thus, depletion of G-actin impairs the MRTF-A nuclear export and promotes its nuclear import (Vartiainen et al. 2007; Pawlowski et al. 2010). To address this, we did inhibit Rho/ROCK signalling using Y27632, and as can be seen in figure for reviewers 2, although nuclear actin in MDA-MB-231 is high and MRTF-A nuclear inhibition of ROCK (which should reduce filamentous F-actin) increases G-actin and is concomitant with MTRF-A export.

      Figure for Reviewers 2: Confocal images of G-actin (DNase I) and MRTF-A in control and ROCK inhibitor Y27632-treated-MDA-MB-231 cells. <not available on hypothes.is>

      1. Fourth, it is surprising how well the Importin-9 silencing can "rescue" the effects of RASSF1A silencing on gene expression, adhesion and SRF activation in figure 5. However, key controls are missing. The authors should first of all convincingly demonstrate that Importin-9 is appropriately silenced, since the blot in S3A (of nuclear fractions only) is not very clear. They should then demonstrate that importin-9 silencing can actually "rescue" the nuclear actin levels back to normal with fractionation.

      As suggested we now validated the silencing of IPO9 by both qPCR and immunoblotting (EV5A-B).

      In figure 1D, the PLA experiment does add too much information, and if kept in the manuscript, should be quantified.

      We agree with the reviewer and we now exclude these data from the manuscript.

      Figure 1E would have benefitted from a positive control for the digitonin treatment (e.g. some outer nuclear membrane protein) to prove that plasma membrane is permeabilized, since the RASSF1A staining in the cytoplasm does not look very convincing.

      We now add the Fig EV1F, in which we used α-Tubulin as a control of plasma membrane permeabilisation.

      Minor points

      In quantification of figure 4C, it is not clear what the data is relative to.

      At several places, the authors talk about "expression", when they should be talking about localization. In figure 1A, the white dashed line is in the wrong place.

      The materials and methods contains stuff that is not in the manuscript, e.g. on fluorouridine.

      On page the sentence "Lamin A/C and B1 both contribute to NE integrity, with Lamin B constituting more stable filaments and Lamin A/C more responsible for stable rigidity." is wrong and does not contain references.<br> On page 7, depletion of IPO9 inhibits nuclear import of actin, NOT promotes export.<br> On page 7, last sentence on first paragraph does not reflect the results, since not all genes were increased.<br> In discussion, the first reference is not optimal, since for example the nuclear import pathway for actin was not discovered, when that paper was published.

      We have corrected the typos and inconsistencies.

      Referee #3

      In this manuscript, the authors demonstrated that RASSF1A (Ras association domain family 1 isoform A), a tumour suppressor, functions as a novel regulator of actin nucleocytoplasmic trafficking to regulate nuclear actin levels. They found that RASSF1A localizes to nuclear envelope, and supports the binding between exportin-6 (XPO6) and RAN GTPase to modulate the nuclear actin export. Furthermore, they showed that RASSF1A is involved in the regulation of MRTF-A, a coactivator of the SRF transcription factor. This is an interesting paper containing potentially important findings and general significance. However, the current manuscript does not provide the mechanistic insight into how RASSF1A participates in nucleocytoplasmic transport process, especially, the formation of XPO6/RAN complex.

      Specific comments

      1. It has been already demonstrated that XPO6 directly binds to RAN (Q69L), using recombinant proteins (Stuven et al, 2003). So, how does RASSF1A affect the formation of XPO6/RAN complex? Since this is one of the most striking findings in this study, the authors need to clarify the role of RASSF1A.

      This was similar to the comment by Rev1 (point 3) and Rev2 (point 2) and was important to clarify further as an aspect of the manuscript that we did not originally focus on, however we now provide further experiments to elucidate a potential mechanism where we expand on XPO6 IP +/- RASSF1A and RASSF1A IP +/- MST2 (new Fig 3C,E). We provide additional XPO6 IP (+/- RASSF1A and +/- MST2) together with MST2 IP (+/- RASSF1A and +/- XPO6) to delineate hierarchy of associations and put the complexes in context of the NE association. These additional data indicate that XPO6 and RAN interact independently of MST2, with limited involvement of RASSF1A (or at a reduced level). However, the dependence of XPO6/RAN stability on RASSF1A appears to be restricted to MST2 being present, which we interpret to be due to NE recruitment. We also further support RASSF1A involvement by employing a recombinant RAN binding assay where XPO6 association is reduced in the absence of RASSF1A (new EV3B). We have modified the text to explain this mechanism as below;

      ….We further investigated the role of RASSF1A on the association of RAN with XPO6. Most strikingly, RASSF1A appeared to be required to support the XPO6/RAN complex, as siRNA-mediated knockdown of RASSF1A decreased association between XPO6 and RAN (__Fig 3C). Expression of RASSF1A in MDA-MB-231 cells significantly enhances the association of XPO6 with RAN (EV3A). We validated this requirement for RASSF1A with a GST pull-down assay using recombinant GST-RAN and lysates from siCTRL or siRASSF1A-transfected HeLa cells (EV3B). Notably, XPO6 co-immunoprecipitation (IP) indicated that the XPO6/RAN complex with RASSF1A also includes MST2, suggesting potential recruitment to the NE via the RASSF1A-MST2 interaction (Fig 3C). Depletion of MST2 expression using siRNA did not affect XPO6/RAN as dramatically as siRASSF1A, but did reduce XPO6/RASSF1A, which we believe implies that RASSF1A may be required for stabilising XPO6/RAN at the NE, i.e. in an MST2 dependent manner, but the nucleoplasmic XPO6/RAN pool may be less dependent on RASSF1A (Fig 3C). This is supported by the fact that the RASSF1A interaction with XPO6/RAN is also dependent on MST2, and therefore NE localisation (Fig 3D). To verify this mechanism, we explored MST2 associated proteins by IP and found that XPO6/RAN interaction with MST2 was RASSF1A dependent whereas the RASSF1A/RAN interaction with MST2 did not require XPO6 (Fig 3E), confirming our hypothesis that XPO6/RAN complex is stabilised by MST2/RASSF1A interaction.

      Taken together, our results show interaction of XPO6 with RAN can occur independently of RASSF1A, but a pool of XPO6/RAN is stabilised by RASSF1A in a MST2 dependent manner at the NE.

      As suggested, we have also looked at XPO6 and RAN distribution (Fig for reviewers 1, above). Suppression of RASSF1A expression does appear to reduce the nuclear staining of RAN, and as total levels of RAN are unaffected (Fig 3C,E), this implies redistribution to the cytoplasm. As staining of XPO6 is unaffected this supports the biochemical data that the XPO6/RAN complex is reduced. Moreover, it also suggests that RASSF1A might be important to maintain RAN.GTP levels, and RAN.GDP is cytoplasmic, and this may impact on the complex formation. As this requires much further thorough investigation we feel it is too preliminary to include in this story, but have included the following statement in the discussion.

      .. the reduced involvement of RASSF1A in the XPO6/RAN complex in the absence of MST2 suggests that RAN/XPO6 exists independently of RASSF1A in the nucleoplasm. This means that XPO6/RAN complexes may be contextually distinct from RASSF1A/RAN/XPO6 and could involve differences in substrate loading, RAN GDP/GTP loading or post translational modifications of RAN (Guttler and Gorlich, 2011 EMBOJ, Dallol et al, 200, de Boor et al. 2015 PNAS, Bompard et al 2010 jcb).

      The authors could perform a binding assay using recombinant proteins to examine how the presence of RASSF1A affects the binding between XPO6 and RAN. In addition, the authors should examine the binding between XPO6 and RAN in MDA-MB-213 cells by co-immunoprecipitation (as in Figure 3C). It may also be possible that the knockdown of RASSF1A causes the subcellular translocation of XPO6 or RAN.

      We thank reviewer for this suggestion and we include this data on Fig EV3B where we performed GST-RAN pull down assay using lysates from siCTRL and siRASSF1A-treated cells. We also showed that the binding of XPO6 to RAN is significantly enhanced upon expression of RASSF1A in MDA-MB-231 cells as shown in Fig EV3A. The knockdown of RASSF1A does not alter the subcellular localisation of XPO6 and RAN as showed on page 1 (Rev1, point 3).

      1. Figure 3C: The band intensity of XPO6 in IP sample seems too weak. Also, in Figure 3D, the band intensity of RASSF1A is weak as well. Therefore, it is not convincing if these antibodies could precipitate their antigens.

      Western blots have been replaced with new IPs from new experiments to clarify.

      1. Figure 4A: The effect of siRASSF1A on actin/profilin nuclear export appears to be relatively modest, considering that XPO6-RAN interaction is almost completely disrupted by the same treatment (Figure 3C). This could be due to the higher concentration of actin/profilin in cytoplasm, as the authors stated. However, to clarify this, authors should examine the effect of XPO6 knockdown on the actin/profilin nuclear export.

      Apologises if we misunderstand but we interpret this critique to be related to the extend to which nuclear actin and profilin levels are mainlined upon siRASSF1A. We do feel this are significant and are quantified in associated bars graphs to reflect this. In figure for reviewers 3, we provide additional data on nuclear/cytoplasmic levels of actin and profilin in the absence of XPO6 to demonstrate that the effect of siRASSF1A is similar to that achieved by siXPO6 alone, but as this is not novel we are not including this in the manuscript. We hope this addresses the concerns.

      Figure for Reviewers 3. <not available on hypothes.is>

      1. Page 7: "increased levels of MYL9, ITGB1, PAK1, and OCT4 mRNA" should be "increased levels of MYL9, ITGB1, and PAK1 mRNA"

      This is now corrected.

    3. THIS IS A TEST

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      Referee #1

      In this study the authors identify RASSF1A, the Hippo kinase regulator, as a regulator of actin monomer levels in the nuclear compartment via interacting with exportin 6, the specific actin export factor, as well as with the Ran GTPase. This leads to changes in actin-dependent gene regulation and may have functional effects on cell adhesion, all supposedly mediated by subsequent changes in the activity of MRTF-A and SRF. Finally, the authors try to correlate their findings with clinical data of invasive carcinoma. Overall, the findings are interesting since they identify a novel player in the nuclear actin-MRTF module, however, several further controls are needed.

      Points of critique

      1. Fig.2C the quantification of effective-knockdowns should be included; RASSF1A decrease resulted from MST2 needs to be confirmed via Western blot.
      2. It is claimed that SARAH domain is responsible for the interaction, therefore, in Fig. 3B it is necessary to rule out the involvement of RA domain by introducing a 288-340 mutation.
      3. Fig. 3C as the co-immunoprecipitation assay showed, Ran recruitment to the RASSF1A/XPO6/RanGTP complex is totally abolished. Could this be seen in staining as well? The same concern also exists in the Fig. 3D, disturbed formation of the complex after MST2 depletion. Additionally, since MST2 is not involved in the RASSF1A/XPO6/RanGTP complex, how come it affects the complex formation? What is the mechanism?
      4. Fig.4 is not entirely convincing. All conclusions on nuclear actin levels are based on biochemical fractionations, which can be often problematic. Besides, effects of siRASSF1A need to be rescued by siRNA resistant wt versus SARAH domain deletion derivatives! This is important and necessary. The biochemical analysis of cleat actin levels needs to be complemented by nuclear actin visualizations either with endogenous actin or at least using GFP-actin.
      5. Could the effect of RASSF1A depletion on nuclear actin levels be rescued by overexpression of XPO6? This would more directly confirm XPO6 is downstream of RASSF1A. In fact, rescue and reconstitution studies would be highly desirable.
      6. How does RASSF1A affect MRTF-A? The authors should study MRTF-A (also known as MAL, or MKL1!) actin interactions directly in the presence or absence of RASSF1A.
      7. What happens to nuclear F-actin in RASSF1A silenced cells? Did the author make efforts to visualize endogenous nuclear F-actin? This would be interesting and provide more and better mechanistic insight, since it has been shown in several studies that nuclear actin assembly regulates MRTF-A or MKL1 or MAL activity. It is also well established by now that nuclear actin is dynamically polymerized by various cellular cues and inputs. Hence, does an increase in nuclear actin levels lead to actin polymerization or changes of nuclear F-actin in this compartment?
    4. THIS IS A TEST

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      Referee #2:

      The manuscript by Chatzifrangkeskou et al. describes a novel role for RASSF1A tumor suppressor gene in regulating nuclear export of actin, and thus also MRTF-A-SRF mediated transcription. RASSF1A is a member of a protein family acting upstream of the Hippo-pathway, binding directly to the MST1 and 2 kinases of the Hippo pathway, and its inactivation is implicated in the development of various cancers.

      In the present manuscript, the authors broaden the functional aspects of RASSF1A by linking it to regulation of nuclear actin levels. Actin has been shown to shuttle in and out of the nucleus with the aid of transport factor Importin-9 and Exportin-6, but further regulators are poorly characterized. The authors first show that a pool of RASSF1 can be found on the nuclear envelope, and that this localization is dependent on MST2. Based on the previous data on the interaction between RASSF1 and the Ran-GTPase, which is the major driver of energy dependent nuclear transport, the authors then identify an interaction between RASSF1 and Exportin-6, and surprisingly find that RASSF1 is required for the interaction between Exportin-6 and Ran. In cells, depletion of RASSF1 leads to increased nuclear accumulation of actin and profilin, as well as to decreased expression of specific genes previously linked to nuclear actin, cell adhesion defects and to decreased nuclear localization of the transcription coactivator MRTF-A and consequently decreased SRF activity. Finally, the expression of SRF and RASSF1A are correlated in various cancer cells.

      The outset for the manuscript is very interesting, and the idea that the nuclear actin pool, and consequently gene expression, would be regulated by a tumour suppressor is exciting. However, the mechanism by which RASSF1A operates here remains somewhat unclear, and further experiments as well as quantifications would be needed to support the key hypothesis.

      Major concern

      From the data, it is clear that RASSF1A interacts with Exportin-6 and that its depletion leads to increased levels of actin in the nucleus. However, I do not completely understand the mechanism that the authors are proposing.

      First, how is the NE localization of RASSF1 related to whole business? How would the NE localized RASSF1A contribute to the formation of the Exportin-6-Ran-actin export complex, especially since MST2 does not seem to be in the complex? MST2 seems to be required for RASSF1A localization to the NE, but can it be excluded that it also regulates the nuclear localization of RASSF1A? In these experiments, the subcellular localization of RASSF1A should be analyzed quantitatively from a large number of cells (or by fractionation) to draw any general conclusions. Analyzing actin distribution in MST2 depleted cells (in case it does not affect nuclear localization of RASSF1A per se) would tell, if the NE localization of RASSF1A is important for regulating nuclear actin.

      Second, I am very surprised by the huge effect that RASSF1 depletion has on Exportin-6-Ran interactions (figure 3C), especially since it seems that the depletion of RASSF1 is not very efficient. Moreover, Exportin-6 has been shown to interact directly, like most other nuclear transport factors, with Ran (shown for example in Stuven et al. 2003). Why would the interaction in cells then require an additional factor? The IPs in figures 3C and D should be carefully quantified from several experiments to draw firm conclusions on these experiments. Related to this point, did the authors check the subcellular distribution of Exportin-6 in RASSF1A depleted cells?

      Third, the results in figures 4C and 4D on MDA-MB-231 cells are very clear, and the data seems to imply that due to the lack of RASSF1A, these cells have relatively high levels of nuclear actin. However, the Treisman-lab has shown that in these cells, MRTF-A is actually nuclear (Medjkane et al. 2009, NCB), which is exactly the opposite that you would expect, and not in agreement with the subsequent results in figure 5. What is the explanation for this?

      Fourth, it is surprising how well the Importin-9 silencing can "rescue" the effects of RASSF1A silencing on gene expression, adhesion and SRF activation in figure 5. However, key controls are missing. The authors should first of all convincingly demonstrate that Importin-9 is appropriately silenced, since the blot in S3A (of nuclear fractions only) is not very clear. They should then demonstrate that importin-9 silencing can actually "rescue" the nuclear actin levels back to normal with fractionation.

      In figure 1D, the PLA experiment does add too much information, and if kept in the manuscript, should be quantified. Figure 1E would have benefitted from a positive control for the digitonin treatment (e.g. some outer nuclear membrane protein) to prove that plasma membrane is permeabilized, since the RASSF1A staining in the cytoplasm does not look very convincing.

      Minor points

      In quantification of figure 4C, it is not clear what the data is relative to.

      At several places, the authors talk about "expression", when they should be talking about localization.

      In figure 1A, the white dashed line is in the wrong place.

      The materials and methods contains stuff that is not in the manuscript, e.g. on fluorouridine.

      On page the sentence "Lamin A/C and B1 both contribute to NE integrity, with Lamin B constituting more stable filaments and Lamin A/C more responsible for stable rigidity." is wrong and does not contain references.

      On page 7, depletion of IPO9 inhibits nuclear import of actin, NOT promotes export.

      On page 7, last sentence on first paragraph does not reflect the results, since not all genes were increased.

      In discussion, the first reference is not optimal, since for example the nuclear import pathway for actin was not discovered, when that paper was published.

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      Referee #3:

      In this manuscript, the authors demonstrated that RASSF1A (Ras association domain family 1 isoform A), a tumour suppressor, functions as a novel regulator of actin nucleocytoplasmic trafficking to regulate nuclear actin levels. They found that RASSF1A localizes to nuclear envelope, and supports the binding between exportin-6 (XPO6) and RAN GTPase to modulate the nuclear actin export. Furthermore, they showed that RASSF1A is involved in the regulation of MRTF-A, a coactivator of the SRF transcription factor. This is an interesting paper containing potentially important findings and general significance. However, the current manuscript does not provide the mechanistic insight into how RASSF1A participates in nucleocytoplasmic transport process, especially, the formation of XPO6/RAN complex.

      Specific comments:

      1. It has been already demonstrated that XPO6 directly binds to RAN (Q69L), using recombinant proteins (Stuven et al, 2003). So, how does RASSF1A affect the formation of XPO6/RAN complex? Since this is one of the most striking findings in this study, the authors need to clarify the role of RASSF1A. The authors could perform a binding assay using recombinant proteins to examine how the presence of RASSF1A affects the binding between XPO6 and RAN. In addition, the authors should examine the binding between XPO6 and RAN in MDA-MB-213 cells by co-immunoprecipitation (as in Figure 3C). It may also be possible that the knockdown of RASSF1A causes the subcellular translocation of XPO6 or RAN.

      2. Figure 3C: The band intensity of XPO6 in IP sample seems too weak. Also, in Figure 3D, the band intensity of RASSF1A is weak as well. Therefore, it is not convincing if these antibodies could precipitate their antigens.

      3. Figure 4A: The effect of siRASSF1A on actin/profilin nuclear export appears to be relatively modest, considering that XPO6-RAN interaction is almost completely disrupted by the same treatment (Figure 3C). This could be due to the higher concentration of actin/profilin in cytoplasm, as the authors stated. However, to clarify this, authors should examine the effect of XPO6 knockdown on the actin/profilin nuclear export.

      4. Page 7: "increased levels of MYL9, ITGB1, PAK1, and OCT4 mRNA" should be "increased levels of MYL9, ITGB1, and PAK1 mRNA"

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      Reply to the Reviewers

      I thank the Referees for their constructive and insightful comments, for their promptness, and for their recognition of the significance and interesting nature of our study. The manuscript (MS) was revised by adding substantial new data from experiments we performed in response to the Referees’ comments, culminating in 15 new figure panels. The text was rewritten where necessary, including the Discussion, either in response to the Referees’ comments or in view of the new data. The text was revised also to mention the recent article of Fury et al., which reported four new hydrocephalus-linked genes (Neuron vol. 99, pp. 1–13, July 2018). The new text was underlined to distinguish it from preexisting text.

      Referee 1

      1. The authors should provide more information when the hydrocephalus is first detectable and repeat the tracer experiments at these early time points. A major problem with this study is that only mice with very pronounced hydrocephalus were analyzed. The authors report that mice did not live longer than 3 weeks and they analyzed 18 to 21-days old mice. In this stage the intracranial is obviously excessively high. One cannot rule out that the subsequent damage on brain tissue (actually indicated by decreased metabolic activity in Fig. 1) and potentially also blood-brain-barrier and blood-CSF allow penetration of contrast agent and proteins into CSF irrespective of the primary cause. Therefore, the authors should provide more information when the hydrocephalus is first detectable and repeat the tracer experiments at these early time points. Can the authors measure the rate of CSF production in these mice? The same problem with EM data in Figure 7. This is really intriguing and supports the authors' hypothesis. However, such permeability changes need to be demonstrated at much earlier time points.

      Responses

      A. The typical domed appearance of a hydrocephalus-harboring skull is apparent as early as P4, as shown in a new side-by-side comparison of pups at that age (Fig. 1A).

      B. Though this is not stated in the MS, MR imaging of 3-week old pups is technically challenging. Since I prepared these pups for imaging together with my technician, I am intimately familiar with the experiment. It not only requires inserting a needle into the tail vein of a 3-week old pup (injecting the tail vein even of adult mice is considered a difficult task that requires training; see Groman and Reinhardt, J. Am. Assoc. Lab. Anim. Sci., vol. 43: pp. 35–38, 2004), but also keeping a catheter in place while the mouse is inserted into the bore of the MR machine, and throughout the imaging session that lasted more than 30 min, including the injection of the contrast medium which was done while the mouse was still in the machine. Furthermore, 3-week old hydrocephalus-harboring pups are about 35% smaller than their normal littermates (by weight, see Fig. 1B) to begin with. Repeating this feat on a 2-week old Mpdz KO pup, for example, which weighs approximately 3.5 g, is practically impossible because the thinnest commercially-available syringe needle (gauge 34) is too thick to fit into its tail vein, and because its tail is too small for immobilizing a catheter.

      C. To the best of my knowledge, the rate of CSF production in the mouse was reported for the first time only in June of this year (Steffensen et al., Nature Comm., vol. 9: pp 1-13, 2018). That study measured the flow rate of a fluorescent probe administered directly into the lateral ventricles as an indicator of CSF production. The study established that the Nkcc1 transporter located on the ventricle-facing surface of CP epithelial cells (CPECs) contributes significantly to CSF production. Therefore, we used its abundance as an indicator of CSF rate of production. Quantification of the new images we present in Fig. 10D shows that Nkcc1 is approximately 75 percent more abundant in the CP of KO mice.

      D. We analyzed by TEM the epithelial cell junctions in the CP of P14 pups, provided the images as expanded view data (Fig EV1), and discussed the subtler differences observed at that age between the junctions of WT and KO mice.

      1. Given the complexity in the in vivo setting the authors should try to demonstrate that deletion of Mpdz increases permeability of choroid plexus epithelial cells in vitro.

      Response: We provide now (Fig. 7E) impedance measurements of human papilloma CPECs (hpCPECs; the same cells used by Feldner et al., who referred to them as HIBCPP) in which Mpdz was depleted by transduction with shRNA. The results show that after reaching plateau, the impedance of the control group remained approximately 42 percent higher than that of the cells transduced by Mpdz-targeting shRNA.

      (Comment on the use of hpCPECs: though we ran experiments on the abundances of LDLR and of cell junction proteins on primary hCPECs, we switched to hpCPECs to reduce the cost of the functional experiment. Primary hCPECs and their specialty media cost approximately $1000 per vial and can be passaged only up to 5 doublings; hpCPECs can be passaged more than 30 times. I believe that Feldner et al. used these cells for the same reason.)

      1. The H&E staining suggests an open aqueduct of Sylvius. However, more functional analysis of CSF flux through the ventricular system would be needed to exclude stenosis.

      Response: We present images (Fig. 5C) of Evans blue-injected WT and KO mice (the same technique used by Feldner et al.). They agree with the finding of Feldner et al. in regard to the presence of stenosis in the aqueduct. We revised the text accordingly. While, we don’t rule out the possible contribution of aqueduct stenosis to the generation of hydrocephalus, this finding is not in conflict with the pathophysiological mechanism we propose.

      1. Figure 6: Why has only ZO-1 been analyzed? Mpdz binds to several TJ and AJ proteins and the literature suggests that loss of Mpdz does not lead to disassembly of junctions but rather to weakening. A detailed expression analysis of such proteins is needed otherwise such strong statements cannot be made.

      Response: We expanded the comparison of the abundance of CPEC junction proteins to a total of three (ZO1, JAMC, and E-CADHERIN). While we provide quantitative analysis of new confocal immunofluorescence (IF) images of these proteins in the CP (Fig. 6A-C), we opted also to use immunoblotting (IB) of MPDZ-depleted hCPECs for the same purpose, because is it more amenable to quantification (Fig. 6D), and because the amount of tissue in the CP of a 3-week old mouse is too small for IB. The IF and IB-based quantifications were in agreement with each other.

      1. Figure 8: Data on the LDLR are preliminary. A functional assay should be performed to show that loss of MPDZ affects LDLR-mediated endocytosis.

      Response: We compared LDLR endocytosis in MPDZ-depleted and in control hCPECs. Quantitative comparison of IF images (Fig. 9D) showed that LDLR was overabundant both on the surface and postendocytosis in MPDZ-deficient cells.

      Minor comments:

      Figure 3/4/5: Please, state the age of the animals and number of animals analyzed. Figure 6/7: Number of biological replicates should be added.

      Response: We added this information as suggested.

      Referee 2

      1. Evidence to support altered transcytosis is not sufficient. EM images (TEM = transmission EM, not transmitted EM), may suffer from fixation problems, which commonly include formation of vacuoles. Quantification, sample numbers, ventricle location, and statistics are needed to make statements about junction length, for example. However as is, with the current approaches used and representative images shown, it is not possible to conclude that transcytosis is altered in this tissue. Classic approaches to examine transcytosis have not been used (e.g. Evans blue, HRP injections). Chow & Gu (Neuron 2017) provides one example on how some of these studies could be performed.

      Response: I thank the reviewer for suggesting the protocol of Chow & Gu. We followed it and probed the CP of WT and KO mice by TEM. The new images (Fig. 8) show that the number of endocytose DAB particles was approximately 6-fold higher in the CPECs of Mpdz KO mice.

      1. Extensive evidence in the field demonstrates that the CSF is not a serum filtrate, and this is clear from any number of fine, contemporary reviews on the topic. In addition, given the novelty of proteomic CSF analysis in hydrocephalus, we have no reference point of comparison to understand the described characterizations and make a clear interpretation. How unique is the altered proteome to this model of hydrocephalus? Would hydrocephalus by any other mechanism also lead indirectly to heightened CSF ApoE and other protein expression (via elevated intracranial pressure or ventriculomegaly/distension, etc)? It seems the CSF is sampled after puncturing the lateral ventricle. This injury alone may induce changes in the CSF. Why not use a more conventional approach vetted by many groups for obtaining pure samples of CSF (e.g. DeMattos et al., J Neurochem 2002)?

      Response:

      A. The Referee’s point is well-taken. We removed the misleading first sentence of this section. Indeed, we attribute the overabundance of proteins in the CSF of the KO mice to increased transcytosis, not to an increase in paracellular permeability.

      B. I thank the Referee for recognizing the novelty of our CSF proteomic analysis. Isn’t absence of reference an inescapable consequence of novelty? However, we noted that out of the 313 proteins we identified, 295 had been detected in 3 previous studies on the CSF composition in the mouse. We interpreted the results by grouping functionally the 23 overabundant proteins in the CSF of KO mice. We discussed the significance of each group and suggested that “their overabundance is part of a multifaceted physiological response to the stress imposed on the brain by the expanding hydrocephalus”. We hope that our data will serve as reference for future studies. I should point out, however, that at least one study (Finehout et al., Electrophoresis 2004, 25, 2564–2575) compared CSF of hydrocephalic patients and healthy subjects. However, Finehut et al. resolved the CSF by 2D gel chromatography and analyzed by mass-spectroscopy material extracted from gel spots, possibly reducing the detection sensitivity. Consequently, they detected only 82 proteins. We cite this reference in the revised MS.

      C. I thank the Referee for supplying the above references. We extracted CSF through the cisterna magna of WT and KO mice and analyzed their proteomes. The differences between the CSF of WT and KO mice were of the same nature as between the previous CSF samples, i.e., overabundance of proteins in the CSF of KO mice, frequently of the same proteins as in the previous samples. We attribute the similarity of the compositions of the CSF samples extracted by the two methods to the careful technique we had used in the first round of experiments, and the minimal damage it incurred.

      1. Which choroid plexus is used in analyses? The lateral ventricles are the most severely affected, but most images shown seem to represent morphology of the 3rd ventricle choroid plexus. The age of sample collections may also influence interpretation of results. It appears that samples are typically collected and analyzed around P18, but by this age, the hydrocephalus is extensive and the authors state that the mice are not viable past ~P21 (3 weeks). It seems that hydrocephalus that is this extensive and induces severe injury in the brain and its vasculature, would alter the interstitial fluid and CSF. Hence, it is unclear is the effects described in the present study are primary, secondary, tertiary....including earlier pre-symptomatic or early hydrocephalic samples to the study would be informative.

      Response: Aside from the section shown in Fig. 6A, all the CP samples of KO mice were from the lateral ventricles. As seen in Fig. 5A and 5B, the 3rd ventricle CP is small and easy to miss. While we interpret the composition of overabundant proteins in the CSF of the KO mouse as a stress response, we did not detect lesions, necrotic tissue, or bleeding in the brain parenchyma of KO mice at any age. We believe, therefore, that it is unlikely that brain injury contributed to the differences we identified in the CSF compositions of WT and KO mice. This argument was added to the Results section on CSF analysis.

      1. What is the anatomical source of the contrast enhancement in Figure 4? The data suggests the choroid plexus might be a source, but the data presented shows a somewhat asymmetric contrast enhancement pattern (bottom of Figure 4B) and in other cases appears either highly focal and also in the aqueduct (top of Figure 4B). Given the presumed broad expression pattern of Mpdz, it is possible that alternative sources would include ependyma, circumventricular organs, or other potential areas of blood-brain barrier breakdown and vascular defects. Contrast enhancement might also suggest hemorrhage, which is not supported by the proteomic studies, but it would be worthwhile noting by presenting additional data regarding comparisons in content of basic serum proteins or albumin or by showing evidence for preserved vascularity of the choroid plexus. Lastly, what happens to contrast enhancement after 10min- does it dissipate in the CSF or persist in particular regions?

      Response:

      A. The anatomical source of the contrast medium had been highlighted in Fig. 4A and magnified in the insets in Fig. 4B. The clear fit between the locations of the CP in the T2-weighted images and the contract medium brighter regions in the T1-weighted images leaves little doubt that the origin of the contrast medium is the CP. We revised the text of the legend to clarify this observation.

      B. I thank the reviewer for suggesting a comparison of the serum albumin abundances in WT and KO CSF as a measure of BBB breakdown in the CP of the latter. There was no statistically significant difference between the WT and KO abundances of serum albumin as well as of three other serum proteins, ruling out breach of the BBB. This point was added to the text. We had presented TEM images of WT and KO CP capillaries to show they are morphologically similar. To strengthen this statement, we added magnified fields of the intercellular junctions and the fenestrae that are typical to these vessels. (Fig. EV2).

      C. I am unable to respond to this question because we ended the MR imaging 10 min after the injection of contrast medium. The hydrocephalus-harboring pups were smaller by a 1/3 than their normal littermates. The T1-wighted contrast medium imaging followed 20 min of T2-weighted imaging of brain morphology. We were concerned that these pups will not survive a lengthy anesthesia and the other stresses involved in this experiment. Death of a mouse even at the very end of the 10 min T1-wighted contrast medium imaging would nullify the whole experiment and impede our overall progress because of the scarcity of KO mice.

      1. Regarding the paracellular permeability mechanism and the presence of 23 new proteins in the CSF, what are the protein size and electrostatic charge comparisons? Do these proteins appear selected based on any criteria that could be more easily explained by ventricular permeability alone? What does the silver stain look like, and what is the typical CSF protein concentration in these samples?

      Response:

      A. We added the isoelectric points of all the proteins that were overabundant in the CSF of Mpdz KO mice to Table 1.

      B. The possible connection between the condition of hydrocephalus and the identity of the overabundant CSF proteins had been discussed at length in the first version of the MS and in the current version. The sizes of these proteins range from 5 kDa (thymosin b-10) up to 509 kDa (apolipoprotein B-100) (Appendix Table A1).

      C. We did not test the barrier function of the ependyma, but it is very unlikely to account for the protein overabundance in the CSF of Mpdz-/- mice because Feldner et al., who used a very similar mouse model, reported that the ependymal tight junctions were morphologically normal. Though the pore size of tight junctions is not uniform, normally even the smallest CSF proteins are too large to pass through them (Shen et al., Annu. Rev. Physiol. 2011. 73:283–309). The most likely route of the CSF proteins is transcytosis, as discussed in the revised Results section.

      D. The CSF was not resolved by SDS-PAGE. It underwent liquid chromatography followed directly by mass-spectroscopy, as described in the Methods section.

      E. The mean protein concentrations in the CSF of WT and KO mice were 4.4 and 11.1 μg/mL, respectively, as shown in Fig. 10A of the revised MS.

      1. It is unclear why the authors think the Feldner 2017 Mpdz knockout mouse has aqueductal stenosis, in contrast to the Milner 2015 mouse model? The discrepancy suggests that some of the data may be unique to the Milner knockout model?

      Response: Feldner et al. 2017 stated several times that the aqueduct of Mpdz KO mice was stenotic after P3. Their conclusion is based on tracking the flow of Evans blue dye injected into the right lateral ventricle, as shown in their Fig. 4A. Our new images of brains of WT and KO mice that underwent the same procedure agree with their findings (Fig. 5C). We revised the text accordingly. While, we don’t rule out the possible contribution of aqueduct stenosis to the generation of hydrocephalus, this finding is not in conflict with the pathophysiological mechanism we propose.

      Minor concerns

      1. Why was PET imaging of the mice performed? There is no experimental justification for it as a starting experiment, and it does not offer any additional data that was not presented in the MRI data. This should be clarified, or the data moved to supplemental information.

      Response: While PET does not achieve the sharp delineation between solid tissue and CSF that MRI provides, it distinguishes between glucose-consuming live tissue and non-cellular material. The observed match between the PET signal and the MR-resolved brain morphology shows that the MR-detected solid brain material was live brain parenchyma rather than necrotic tissue. We added text to this effect in order to explain the rationale of PET imaging. We believe that this information is significant because it rules out wide-spread tissue breakdown as an explanation of the large difference between the CSF compositions in WT and KO mice.

      1. Figure 3- what was the n number of mice?

      Response: Each row of one T2 and two T1-weighted MR images corresponds to one mouse. The same applies to Fig. 4. We clarified this in the legends of Figs. 3 and 4.

      1. Figure 8 legend does not mention LDL-R

      Response: We corrected this mistake.

      1. Fig 3C mislabeled T2 and T1 in the legend. Fig4C legend also mislabeled T2 (should write T1)

      Response: We corrected these mistakes.

      1. "weighted" is misspelled on page 7 and in the legend of Fig 4

      Response: We corrected these mistakes.

      I thank the Referee for bringing to our attention these minor yet disconcerting mistakes.

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      Referee #2

      The authors dissect the pathogenic mechanics of the MPDZ knockout mouse model of congenital human hydrocephalus. They neatly demonstrated the aberrant contrast enhancement in this model, suggesting a change in permeability of a structure in the ventricular system. Arguing for both an increase in the structure/permeability and an increase in secretory function of the choroid plexus, they then suggest ultrastructural changes in the choroid plexus and describe the proteomic differences in the CSF composition of this hydrocephalus model. Overall, this would provide an important contribution to understanding the pathogenesis of hydrocephalus, but the mechanism is likely not as "straightforward" as described in the abstract. The choroid plexus may be involved in addition to other structures. The current interpretation of the results requires further experiments to support the conclusion. Major points to address include:

      Major concerns:

      1. Evidence to support altered transcytosis is not sufficient. EM images (TEM = transmission EM, not transmitted EM), may suffer from fixation problems, which commonly include formation of vacuoles. Quantification, sample numbers, ventricle location, and statistics are needed to make statements about junction length, for example. However as is, with the current approaches used and representative images shown, it is not possible to conclude that transcytosis is altered in this tissue. Classic approaches to examine transcytosis have not been used (e.g. Evans blue, HRP injections). Chow & Gu (Neuron 2017) provides one example on how some of these studies could be performed.
      2. Extensive evidence in the field demonstrates that the CSF is not a serum filtrate, and this is clear from any number of fine, contemporary reviews on the topic. In addition, given the novelty of proteomic CSF analysis in hydrocephalus, we have no reference point of comparison to understand the described characterizations and make a clear interpretation. How unique is the altered proteome to this model of hydrocephalus? Would hydrocephalus by any other mechanism also lead indirectly to heightened CSF ApoE and other protein expression (via elevated intracranial pressure or ventriculomegaly/distension, etc)? It seems the CSF is sampled after puncturing the lateral ventricle. This injury alone may induce changes in the CSF. Why not use a more conventional approach vetted by many groups for obtaining pure samples of CSF (e.g. DeMattos et al., J Neurochem 2002)?
      3. Which choroid plexus is used in analyses? The lateral ventricles are the most severely affected, but most images shown seem to represent morphology of the 3rd ventricle choroid plexus. The age of sample collections may also influence interpretation of results. It appears that samples are typically collected and analyzed around P18, but by this age, the hydrocephalus is extensive and the authors state that the mice are not viable past ~P21 (3 weeks). It seems that hydrocephalus that is this extensive and induces severe injury in the brain and its vasculature, would alter the interstitial fluid and CSF. Hence, it is unclear is the effects described in the present study are primary, secondary, tertiary....including earlier pre-symptomatic or early hydrocephalic samples to the study would be informative.
      4. What is the anatomical source of the contrast enhancement in Figure 4? The data suggests the choroid plexus might be a source, but the data presented shows a somewhat asymmetric contrast enhancement pattern (bottom of Figure 4B) and in other cases appears either highly focal and also in the aqueduct (top of Figure 4B). Given the presumed broad expression pattern of Mpdz, it is possible that alternative sources would include ependyma, circumventricular organs, or other potential areas of blood-brain barrier breakdown and vascular defects. Contrast enhancement might also suggest hemorrhage, which is not supported by the proteomic studies, but it would be worthwhile noting by presenting additional data regarding comparisons in content of basic serum proteins or albumin or by showing evidence for preserved vascularity of the choroid plexus. Lastly, what happens to contrast enhancement after 10min- does it dissipate in the CSF or persist in particular regions?
      5. Regarding the paracellular permeability mechanism and the presence of 23 new proteins in the CSF, what are the protein size and electrostatic charge comparisons? Do these proteins appear selected based on any criteria that could be more easily explained by ventricular permeability alone? What does the silver stain look like, and what is the typical CSF protein concentration in these samples?
      6. It is unclear why the authors think the Feldner 2017 Mpdz knockout mouse has aqueductal stenosis, in contrast to the Milner 2015 mouse model? The discrepancy suggests that some of the data may be unique to the Milner knockout model?

      Minor concerns

      1. Why was PET imaging of the mice performed? There is no experimental justification for it as a starting experiment, and it does not offer any additional data that was not presented in the MRI data. This should be clarified or the data moved to supplemental information.
      2. Figure 3- what was the n number of mice?
      3. Figure 8 legend does not mention LDL-R
      4. Fig 3C mislabeled T2 and T1 in the legend. Fig4C legend also mislabeled T2 (should write T1)
      5. "weighted" is misspelled on page 7 and in the legend of Fig 4

      In its current form, I regret that I cannot support publication of this study as a short report in EMBO Molecular Medicine.

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      Referee #1

      The analyses need to be performed at much earlier time points before overt damage through the intracerebral pressure occurs.

      This manuscript addresses the pathogenesis of congenital hydrocephalus in Mpdz-/- mice. The authors nicely demonstrate that MRI contrast agents diffuse into cerebrospinal fluid (CSF) in -/- mice but not in +/+ controls. Also, the authors detect a higher protein content in CSF. Based on this they argue that hydrocephalus occurs by increased paracellular permeability at the choroid plexus. In contrast to a previous report in this journal they did not detect stenosis of the aqueduct. This is a highly interesting study. Mpdz has originally be described to be strongly expressed in epithelial cells of the choroid plexus. These cells form a tight barrier between blood plasma and CSF. Given the literature reports that Mpdz stabilizes cell-cell junctions, it is intriguing to conclude that hydrocephalus might be caused by increased flux of proteins and water across the blood-CSF barrier. As such, the pathogenesis would be through over-production of CSF. Little is known about this, but choroid plexus tumors can indeed cause hydrocephalus.

      The manuscript need very substantial revision to demonstrate that overproduction of CSF is the primary cause.

      1. A major problem with this study is that only mice with very pronounced hydrocephalus were analyzed. The authors report that mice did not live longer than 3 weeks and they analyzed 18 to 21-days old mice. In this stage the intracranial is obviously excessively high. One cannot rule out that the subsequent damage on brain tissue (actually indicated by decreased metabolic activity in Fig. 1) and potentially also blood-brain-barrier and blood-CSF allow penetration of contrast agent and proteins into CSF irrespective of the primary cause. Therefore, the authors should provide more information when the hydrocephalus is first detectable and repeat the tracer experiments at these early time points.<br> Can the authors measure the rate of CSF production in these mice?<br> The same problem with EM data in Figure 7. This is really intriguing and supports the authors' hypothesis. However, such permeability changes need to be demonstrated at much earlier time points.
      2. Given the complexity in the in vivo setting the authors should try to demonstrate that deletion of Mpdz increases permeability of choroid plexus epithelial cells in vitro.
      3. The H&E staining suggests an open aqueduct of Sylvius. However, more functional analysis of CSF flux through the ventricular system would be needed to exclude stenosis.
      4. Figure 6: Why has only ZO-1 been analyzed? Mpdz binds to several TJ and AJ proteins and the literature suggests that loss of Mpdz does not lead to disassembly of junctions but rather to weakening. A detailed expression analysis of such proteins is needed otherwise such strong statements cannot be made.
      5. Figure 8: Data on the LDLR are preliminary. A functional assay should be performed to show that loss of MPDZ affects LDLR-mediated endocytosis.

      Minor comments:

      • Figure 3/4/5: Please, state the age of the animals and number of animals analyzed.
      • Figure 6/7: Number of biological replicates should be added.