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    1. Reviewer #3

      Jaron and collaborators provide a large-scale comparative work on the genomic impact of asexuality in animals. By analysing 26 published genomes with a unique bioinformatic pipeline, they conclude that none of the expected features due to the transition to asexuality is replicated across a majority of the species. Their findings call into question the generality of the theoretical expectations, and suggest that the genomic impacts of asexuality may be more complicated than previously thought.

      The major strengths of this work is (i) the comparison among various modes and origins of asexuality across 18 independent transitions; and (ii) the development of a bioinformatic pipeline directly based on raw reads, which limits the biases associated with genome assembly. Moreover, I would like to acknowledge the effort made by the authors to provide on public servers detailed methods which allow the analyses to be reproduced. That being said, I also have a series of concerns, listed below:

      1) Theoretical expectations.

      As far as I understand, the aim of this work is to test whether 4 classical predictions associated with the transition to asexuality and 5 additional features observed in individual asexual lineages hold at a large phylogenetic scale. However, I think that these predictions are poorly presented, and so they may be hardly understood by non-expert readers. Some of them are briefly mentioned in a descriptive way in the Introduction (L56 - 61), and with a little more details in the Boxes 1 and 2. However, the evolutive reasons why one should expect these features to occur (and under which assumptions) is not clearly stated anywhere in the Introduction (but only briefly in the Results & Discussion). I think it is important that the authors provide clear-cut quantitative expectations for each genomic feature analysed and under each asexuality origin and mode (Box 1 and 2). Also highlighting the assumptions behind these expectations will help for a better interpretation of the observed patterns.

      2) Mutation accumulation & positive selection.

      A subtlety which is not sufficiently emphasized to my mind is that the different modes of asexuality encompass reproduction with or without recombination (Box 2), which can lead to very different genetic outcomes. For example, it has been shown that the Muller's ratchet (the accumulation of deleterious mutations in asexual populations) can be stopped by small amounts of recombination in large-sized populations (Charlesworth et al. 1993; 10.1017/S0016672300031086). Similarly a new recessive beneficial mutation can only segregate at a heterozygous state in a clonal lineage (unless a second mutation hits the same locus); whereas in the presence of recombination, these mutations will rapidly fix in the population by the formation of homozygous mutants (Haldane's Sieve, Haldane 1927; 10.1017/S0305004100015644). Therefore, depending on whether recombination occurs or not during asexual reproduction, the expectations may be quite different; and so they could deviate from the "classical predictions". In this regard, I would like to see the authors adjust their conclusions. Moreover, it is also not very clear whether the species analysed here are 100% asexuals or if they sometimes go through transitory sexual phases, which could reset some of the genomic effects of asexuality.

      3) Transposable elements.

      I found the predictions regarding the amount of TEs expected under asexuality quite ambiguous. From one side, TEs are expected not to spread because they cannot colonize new genomes (Hickey 1982); but on the other side TEs can be viewed as any deleterious mutation that will accumulate in asexual genome due to the Muller's ratchet. The argument provided by the authors to justify the expectation of low TE load in asexual lineages is that "Only asexual lineages without active TEs, or with efficient TE suppression mechanisms, would be able to persist over evolutionary timescales". But this argument should then equally be applied to any other type of deleterious mutations, and so we won't be able to see Muller's ratchet in the first place. Therefore, not observing the expected pattern for TEs in the genomic data is not so surprising as the expectation itself does not seem to be very robust. I would like the authors to better acknowledge this issue, which actually goes into their general idea that the genomic consequences of asexuality are not so simple.

      4) Heterozygosity.

      Due to the absence of recombination, asexual populations are expected to maintain a high level of diversity at each single locus (heterozygosity), but a low number of different haplotypes. However, as presented by the authors in the Box 2, there are different modes of parthenogenesis with different outcomes regarding heterozygosity: (1) preservation at all loci; (2) reduction or loss at all loci; (3) reduction depending on the chromosomal position relative to the centromere (distal or proximal). Therefore, the authors could benefit from their genome-based dataset to explore in more detail the distribution of heterozygosity along the chromosomes, and further test whether it fits with the above predictions. If the differing quality of the genome assemblies is an issue, the authors could at least provide the variance of the heterozygosity across the genome. The mode #3 (i.e. central fusions and terminal fusions) would be particularly interesting as one would then be able to compare, within the same genome, regions with large excess vs. deficit of heterozygosity and assess their evolutive impacts.

      Moreover, the authors should put more emphasis on the fact that using a single genome per species is a limitation to test the subtle effects of asexuality on heterozygosity (and also on "mutation accumulation & positive selection"). These effects are better detected using population-based methods (i.e. with many individuals, but not necessarily many loci). For example, the FIS value of a given locus is negative when its heterozygosity is higher than expected under random mating, and positive when the reverse is true (Wright 1951; 10.1111/j.1469-1809.1949.tb02451.x).

      5) Absence of sexual lineages.

      A second limit of this work is the absence of sexual lineages to use as references in order to control for lineage-specific effects. I do not agree with the authors when they say that "the theoretical predictions pertaining to mutation accumulation, positive selection, gene family expansions, and gene loss are always relative to sexual species [...] and cannot be independently quantified in asexuals." I think that this is true for all the genomic features analysed, because the transition to asexuality is going to affect the genome of asexual lineages relative to their sexual ancestors. This is actually acknowledged at the end of the Conclusion by the authors.

      To give an example, the authors say that "Species with an intraspecific origin of asexuality show low heterozygosity levels (0.03% - 0.83%), while all of the asexual species with a known hybrid origin display high heterozygosity levels (1.73% - 8.5%)". Interpreting these low vs. high heterozygosity values is difficult without having sexual references, because the level of genetic diversity is also heavily influenced by the long term life history strategies of each species (e.g. Romiguier et al. 2014; 10.1038/nature13685).

      I understand that the genome of related sexual species are not available, which precludes direct comparisons with the asexual species. However, I think that the results could be strengthened if the authors provided for each genomic feature that they tested some estimates from related sexual species. Actually, they partially do so along the Result & Discussion section for the palindromes, transposable elements and horizontal gene transfers. I think that these expectations for sexual species (and others) could be added to Table 1 to facilitate the comparisons.

      6) Regarding statistics, I acknowledge that the number of species analysed is relatively low (n=26), which may preclude getting any significant results if the effects are weak. However, the authors should then clearly state in the text (and not only in the reporting form) that their analyses are descriptive. Also, their position regarding this issue is not entirely clear as they still performed a statistical test for the effect of asexuality mode / origin on TE load (Figure 2 - supplement 1). Therefore, I would like to see the same statistical test performed on heterozygosity (Figure 2).

      7) As you used 31 individuals from 26 asexual species, I was wondering whether you make profit of the multi-sample species. For example, were the kmer-based analyses congruent between individuals of the same species?

    2. Reviewer #2

      This paper is interesting because it is studying, through a comparative genomic approach, how asexuality affects genome evolution in animal lineages while focusing on the same features. Such an extensive comparison can, in principle, distinguish the common consequences of asexuality, in contrast to previous studies that focused on few asexual species (or only one). It is interesting that the authors did not find a universal genomic feature of "asexual" species. This is a potentially important contribution to the field of the evolution of reproductive systems.

      However, I am concerned about limitations and potential biases in many of the specific genomic features analysed, and resultant difficulties in drawing any general conclusions from these analyses. For example, the heterozygosity analyses need to be more clearly explained and the potential limits of the methods used discussed further. The use of kmer spectra analyses as opposed to genome assemblies is understandable, but these are biases here that were not discussed. I am also concerned about the impact of low read quality and low coverage genomic data, and whether issues with genome assembly affect the conclusions. There are also issues about conclusions related to species of hybrid origin as there are numerous "unknown" cases and cytological data is lacking for many of the studied animal groups (therefore the authors should be cautious on the evidence of reproduction mode).

      Ideally, all the genomes of the asexual animal clades studied should have been sequenced and assembled using the same method which would make this comparative study much stronger. We realize this may not yet be practical, but the absence of such data must temper the conclusions. It is nevertheless the first article including and comparing many distinct parthenogenetic animal clades and the main result that no common universal genomic feature of parthenogenesis is, with caveats, interesting.

      Major Issues and Questions:

      1) The authors choose to refer to asexuality when describing thelytokous parthenogenesis. Asexuality is a very general term that can be confusing: fission, vegetative reproduction could also be considered asexuality. I suggest using parthenogenesis throughout the manuscript for the different animal clades studied here. Moreover, in thelytokous parthenogenesis meiosis can still occur to form the gametes, it is therefore not correct to write that "gamete production via meiosis... no longer take place" (lines 57-58). Fertilization by sperm indeed does not seem to take place (except during hybridogenesis, a special form of parthenogenesis).

      2) The cellular mechanisms of asexuality in many asexual lineages are known through only a few, old cytological studies and could be inaccurate or incomplete (for example Triantaphyllou paper of 1981 of Meloidogyne nematodes or Hsu, 1956 for bdelloid rotifers). The authors should therefore mention in the introduction the lack of detailed and accurate cellular and genetic studies to describe the mode of reproduction because it may change the final conclusion.

      For example, for bdelloid rotifers the literature is scarce. However the authors refer in Supp Table 1 to two articles that did not contain any cytological data on oogenesis in bdelloid rotifers to indicate that A. vaga and A. ricciae use apomixis as reproductive mode. Welch and Meselson studied the karyotypes of bdelloid rotifers, including A. vaga, and did not conclude anything about absence or presence of chromosome homology and therefore nothing can be said about their reproduction mode. In the article of Welch and Meselson the nuclear DNA content of bdelloid species is measured but without any link with the reproduction mode. The only paper referring to apomixis in bdelloids is from Hsu (1956) but it is old and new cytological data with modern technology should be obtained.

      3) In the section on Heterozygosity, the authors compute heterozygosity from kmer spectra analysis from reads to "avoid biases from variable genome assembly qualities" (page 16). But such kmer analysis can be biased by the quality and coverage of sequencing reads. While such analyses are a legitimate tool for heterozygosity measurements, this argument (the bias of genome quality) is not convincing and the authors should describe the potential limits of using kmer spectra analyses.

      4) The authors state that heterozygosity levels “should decay over time for most forms of meiotic asexuality". This is incorrect, as this is not expected with "central fusion" or with "central fusion automixis equivalent" where there is no cytokinesis at meiosis I.

      5) I do not fully agree with the authors’ statement that: "In spite of the prediction that the cellular mechanism of asexuality should affect heterozygosity, it appears to have no detectable effect on heterozygosity levels once we control for the effect of hybrid origins (Figure 2)." (page 17)

      The scaling on Figure 2 is emphasizing high values, while low values are not clearly separated. By zooming in on the smaller heterozygosity % values we may observe a bigger difference between the "asexuality mechanisms". I do not see how asexuality mechanism was controlled for, and if you look closely at intra group heterozygosity, variability is sometimes high.

      It is expected that hybrid origin leads to higher heterozygosity levels but saying that asexuality mechanism is not important is surprising: on Figure 2 the orange (central fusion) is always higher than yellow (gamete duplication). Also, the variability found within rotifers could be an argument against a strong importance of asexuality origin on heterozygosity levels: the four bdelloid species likely share the same origin but their allelic heterozygosity levels appears to range from almost 0 to almost 6% (Fig 2 and 3, however the heterozygosity data on Rotaria should be confirmed, see below).

      The authors’ main idea (i.e. asexuality origin is key) seems mostly true when using homoeolog heterozygosity and/or composite heterozygosity which is not what most readers will usually think as "heterozygosity". This should be made clear by the authors mostly because this kind of heterozygosity does not necessarily undergo the same mechanism as the one described in Box 2 for allelic heterozygosity. If homoeolog heterozygosity is sometimes not distinguishable from allelic heterozygosity, then it would be nice to have another box showing the mechanisms and evolution pattern for such cases (like a true tetraploid, in which all copies exist).

      The heterozygosity between homoeologs is always high in this study while it appears low between alleles, but since the heterozygosity between homeologs can only be measured when there is a hybrid origin, the only heterozygosity that can be compared between ALL the asexual groups is the one between alleles.

      Both in the results and the conclusion the authors should not over interpret the results on heterozygosity. The variation in allelic heterozygosity could be small (although not in all asexuals studied) also due to the age of the asexual lineages. This is not mentioned here in the result/discussion section.

      6) Regarding the section on Heterozygosity structure in polyploids.

      There is inconsistency in many of the numbers. For example, A. vaga heterozygosity is estimated at 1.42% in Figure 1, but then appears to show up around 2% in Figure 2, and then becomes 2.4% on page 20. It is unclear is this is an error or the result of different methods.

      It is also unclear how homologs were distinguished from homeologs. How are 21 bp k-mers considered homologous? In the method section. the authors describe extracting unique k-mer pairs differing by one SNP, so does this mean that no more than one SNP was allowed to define heterozygous homologous regions? Does this mean that homologues (and certainly homoeologs) differing by more than 5% would not be retrieved by this method. If so, then It is not surprising that for A. vaga is classified as a diploid.

      The result for A. ricciae is surprising and I am still not convinced by the octoploid hypothesis. In Fig S2. there is a first peak at 71x coverage that still could be mostly contaminants. It would be helpful to check the GC distribution of k-mers in the first haploid peak of A. ricciae to check whether there are contaminants. The karyotypes of 12 chromosomes indeed do not fit the octoploid hypothesis. I am also surprised by the 5.5% divergence calculated for A. ricciae, this value should be checked when eliminating potential contaminants (if any). In general, these kind of ambiguities will not be resolved without long-read sequencing technology to improve the genome assemblies of asexual lineages.

      7) Regarding the section on palindromes and gene conversion.

      The authors screened all the published genomes for palindromes, including small blocks, to provide a more robust unbiased view. However, the result will be unbiased and robust if all the genomes compared were assembled using the same sequencing data (quality, coverage) and assembly program. While palindromes appear not to play a major role in the genome evolution of parthenogenetic animals since only few palindromes were detected among all lineages, mitotic (and meiotic) gene conversion is likely to take place in parthenogens and should indeed be studied among all the clades.

      8) Regarding the section on transposable elements.

      The authors are aware that the approach used may underestimate the TEs present in low copy numbers, therefore the comparison might underestimate the TE numbers in certain asexual groups.

      9) Regarding the section on horizontal gene transfer.

      For the HGTc analysis, annotated genes were compared to the UniRef90 database to identify non-metazoan genes and HGT candidates were confirmed if they were on a scaffold containing at least one gene of metazoan origin. While this method is indeed interesting, it is also biased by the annotation quality and the length of the scaffolds which vary strongly between studies.

      10) Regarding the use of GenomeScope2.0.

      When homologues are very divergent (as observed in bdelloid rotifers) GenomeScope probably considers these distinct haplotypes as errors, making it difficult to model the haploid genome size and giving a high peak of errors in the GenomeScope profile. Moreover, due to the very divergent copies in A. vaga, GenomeScope indeed provides a diploid genome (instead of tetraploid).

      For A. vaga, the heterozygosity estimated par GenomeScope2.0. on our new sequencing dataset is 2% (as shown in this paper). This % corresponds to the heterozygosity between k-mers but does not provide any information on the heterogeneity in heterozygosity measurements along the genome. A limitation of GenomeScope2.0. (which the authors should mention here) is that it is assuming that the entire genome is following the same theoretical k-mer distribution.

    3. Reviewer #1

      This paper addresses the very interesting topic of genome evolution in asexual animals. While the topic and questions are of interest, and I applaud the general goal of a large-scale comparative approach to the questions, there are limitations in the data analyzed. Most importantly, as the authors raise numerous times in the paper, questions about genome evolution following transitions to asexuality inherently require lineage-specific controls, i.e. paired sexual species to compare with the asexual lineages. Yet such data are currently lacking for most of the taxa examined, leaving a major gap in the ability to draw important conclusions here. I also do not think the main positive results, such as the role of hybridization and ploidy on the retention and amount of heterozygosity, are novel or surprising.

    4. Preprint Review

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


      This paper addresses the question of whether there are distinct genomic features in animals that reproduce asexually. The authors examine a range of features in the genomes of 26 species representing 18 independent evolutionary origins of asexuality. The reviewers were unanimous that this is an interesting question, and find that exploring it in a broad evolutionary context is the right approach. However, they raised questions about biases in specific analyses that complicated their interpretation, and the extent to which the central claims can be supported without comparison to closely related sexual species.

    1. Reviewer #2

      I very much like the general idea of this paper, but my opinion is that this is not an idea that can/should be applied to these data. As elaborated below, the ABIDE data are from numerous sites with different scanners, imaging acquisition sequences and parameters, sample ascertainment, etc, The methods used in the current paper rely on there not being such heterogeneity; and its presence can either render true ASD-related deviance invisible, or create an illusion of ASD-related deviance where there is none. Such heterogeneity is, of course, problematic for more conventional approaches; but is far more problematic for the methods proposed here.

      Major Issues and Questions:

      1) The authors are critical of case-control models but do not present an alternative to dealing with the heterogeneity in the data. Indeed, linear models are inadequate to deal with the heterogeneity in the ABIDE data given the lack of overlap in the data for different sites. But the normative approach presented here seems to not deal with the problem at all, potentially transforming what would be taken out by a nuisance variable into an alteration in ASD-related deviance.

      2) The sparsity of the data beyond childhood is extremely problematic for this approach. The approach of taking data in one-year bins requires large amounts of data within each bin to make the means and standard deviations reliable. By the teenage years, this is clearly not the case. The authors limit age bins to having at least 3 control points; this is clearly wildly insufficient, and would be even if there were no issues with site heterogeneity. Conventional linear models are to be preferred to normative models under these conditions.

      3) The comparison of results from a case-control model versus a normative model seems misleading. A case-control model approach requires a specification of the age at which the comparison is made. This is not provided, leading one to suspect that the age data were not centered, but were absolute, and thus the differences were essentially projecting backwards to birth. (This is, I believe, a common mistake.) The model specification is also completely lacking. Moreover, a case-control approach does not preclude the possibility of centering the data at different ages (as in e.g. Khundrakpam et al. (2017)). Between this and the problems with heterogeneity for the normative models, it is unclear how to interpret these results.

      4) The idea that individuals that are more than 2 stddevs away from the mean of the controls are outliers and should be eliminated from the analysis seems mistaken. If all individuals with ASD are substantially far from the mean of the controls, they are clearly not to be treated as outliers.

      5) The impact statement claims that "normative modelling has the potential to isolate specific highly deviant subsets of individuals with ASD, which will have implications for understanding the underlying mechanisms and bring clinical impact closer"; there is no indication that that is the case. The normative model has identified primarily children, and has identified nothing in particular about those children. Case-control models have done the same.

      6) It appears to this reviewer that this paper outlines an approach which could be worthwhile in a data set without massive heterogeneity, but within the context of the ABIDE data actually seems harmful.

    2. Reviewer #1

      This paper describes the impact of outliers in normative cortical thickness (CT) measurements when examining those suffering from autism spectrum disorder (ASD). The authors used the ABIDE sample and binned subjects by age, and assessed outliers as a function of a "w-score" which they estimated across CT parcellations across the entire cortex. They then demonstrate that cortical thickness differences that can ascribed to ASD can essentially be attributed to a small number of outliers within the sample. They also demonstrate that this w-score may be sensitive to clinical variables as well.

      Overall, it is unclear to me what the exact goal of the work is: To describe the anatomy of ASD better? To subtype? Or is there another "take-home" message of this paper? I would imagine that the case-control differences in most neurodevelopmental disorders with high heterogeneity and high variability would demonstrate a similar kind of trend. And thus, at the end of the day, I am not sure how much this technique advanced our understanding of ASD.

      Issues and Questions:

      1) It is unclear from the methods how the authors deal with motion and image quality. Recent work by Pardoe and Bedford demonstrate the importance of dealing with this issue, particularly in the context of the ABIDE sample. This would likely have a significant impact on any of the results. It's unclear if the use of the Euler index at the extremes of the distribution of the dataset being used is sufficient. How did the authors come up with their Euler number cut-off?

      2) The W-score could use a much better explanation. It is not clear to me as to what it is and how this should be interpreted. The lack of information regarding the number of age-bins used also makes interpreting these findings confusing in my mind.

      3) The authors report that, "The median number of brain regions per subject with a significant p-value was 1 (out of 308), indicating that the w-score provides a robust measure of atypicality." I guess this could be true, but given the variation in normative ageing and development, I suspect this would also be true of a large number of TD children. That being the case, would it be worth doing a permutation test to determine the threshold of how man "atypical" areas one could expect by chance?

      4) The authors note "Unfortunately, despite a significant female subgroup, the age-wise binning greatly reduced the number of bins with enough data-points in the female group." I understand that this could indeed be a problem. However, I think it would be good for the authors to provide more details. Potentially a histogram to demonstrate the issue. My feeling is that with sex difference with respect to ASD, the more information that could be provided the better. Overall, it is unclear to me as to how useful a sex-specific analysis may be in this particular context given the sample sizes available in ABIDE.

      5) Results, page 8: "Because we also had computed w-scores from our normative age-modelling approach, we identified specific 'statistical outlier' patients for each individual region with w-scores > 2 standard deviations from typical norms and excluded them from the case-control analysis."

      I'm not sure I agree with the premise of this statement. First, it is hard to know without seeing all of the data, but based on Fig 1, it seems that there are ASD individuals that fall on both sides of this distribution. So if there are effect sizes that can be gleaned, this would be in spite of the variability. Second, it would be paramount to determine how many people are outliers-by-region. This, in and of itself, would be useful information. If a significant proportion of individuals can be identified as outliers, this suggests that variability is the norm rather than an exception. I'm skeptical as to whether you get interesting information from removing these individuals from analyses.

      6) Result, page 9: "While the normative modelling approach can be sensitive to different pathology." I don't think you're capturing anything interesting about pathology with this method, especially as it pertains to CT values.

      7) Result, page 9-10: I'm still confused by this notion of atypicality. Presumably this suggests that 5-10% of all ASDs are more than 2SDs from a normative distribution. But is this at both tails of the distribution? There are significant interpretational issues with this. thus, it is imperative on the authors to do a better job of describing these distributions.

      8) Part of the rationale of this paper is that using the w-score is far more robust than using simple CT values. I'm sure that residualized CT values could have been used for any of these analyses. If that were to be done how would this change the results?

      Minor comments and suggestions on presentation:

      1) While this paper has some merits, I found it hard to read. There is not a clear delineation between the methods and the results, and some methodological considerations are written into the results section and vice-versa.

      2) In the introduction, the authors use the word "deviance" to describe what appears more to me like age-related variation and heterogeneity in ASD. Deviance may be too strong a term and easily mis-interpretable. I would suggest replacing it with something a bit more like variation. Also, the work at the institution of the main author (for example by Baron-Cohen and authors) really champions the use of terms like "neurotypical" rather normally developing. I think, in general, the authors may want to take their cues from this type of language.

      3) This passage in the Introduction need of references. The work by Hong (in Boris Bernhardt's group), Bedford (in Mallar Chakravarty's group), Schuetze (in Signe Bray's group), and Meng-Chuan Lai all come to mind.

      "Even within mesoscopic levels of analysis such as examining brain endophenotypes, heterogeneity is the rule rather than the exception (Ecker, 2017). At the level of structural brain variation, neuroimaging studies have identified various neuroanatomical features that might help identify individuals with autism or reveal elements of a common underlying biology (Ecker, 2017). However, the vast neuroimaging literature is also considerably inconsistent, with reports of hypo- or hyper-connectivity, cortical thinning versus increased grey or white matter, brain overgrowth, arrested growth, etc., leaving stunted progress towards understanding mechanisms driving cortical pathophysiology in ASD."

      4) I found the Discussion missed the mark. It was mostly written as a rehash of the results, with no real biological interpretation. There is not a sufficient examination of the relationship of these findings to other important papers (Kundrakpham, Bedford, Hong, Ecker, Hyde, Lange, etc...).

      5) Figure 3 - The colour bars should be labelled.

    3. Preprint Review

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


      This paper uses data from the Autism Brain Imaging Data Exchange (ABIDE) to model the relationship between cortical thickness in different brain regions and patients with autism spectrum disorders (ASD) compared to neurotypical controls. The reviewers appreciated the goals and approach of this paper, but, as described below, had questions about the suitability of the data for this analysis, the ways in which the data were processed, the way in which the results were interpreted, and the significance of these findings for understanding autism spectrum disorders.

    1. Reviewer #3

      This study by Kiss and colleagues reports the findings of proximity biotinylation experiments for the discovery of novel RAB18 effectors. The authors perform careful proteomic analysis that appears well-controlled and successful in recapitulating known interactions. That small GTPase interactions can be identified with this approach has been previously demonstrated, though the application of this approach to RAB18 is novel and of interest to the field. A number of intriguing findings with potentially important implications are reported. However, this manuscript has several weaknesses.

      Major concerns and questions:

      1) As the authors report, proximity biotinylation may not reflect direct protein-protein interactions but simply colocalization of bait and prey proteins. A true protein-protein interaction ideally would be further supported by ancillary experiments such as in vitro binding or co-immunoprecipitation, including an assessment of whether the interaction is affected by the GTP- or GDP-bound state. While co-IP in WT and GEF-deficient cells was performed for 1 candidate interactor (TMC04, Figure 6C), protein-protein interactions were not tested for the other 2, with the latter relying on either repeat BioID (SPG20, Figure 3A) or reciprocal BioID (SEC22A, Figure 5B).

      2) Putative RAB18 interactions may be affected by the BioID fusion itself or by heterologous expression. While it is reassuring that known interactors were detected with this approach, the conclusions would be better supported by testing the localization of the fusion protein in comparison to endogenous RAB18, and/or by rescue of a phenotype associated with RAB18-deficiency.

      3) Conclusions about the dependence of RAB18 interactions on its GTP or GDP-bound state rely on differences observed in cells with deficiency of RAB18 GEFs. It is certainly possible however that RAB3GAP may serve as a GEF for other GTPases, or have other functions, that cause the observed differences in labeling. The conclusions would be strengthened by additional experiments showing a direct effect - e.g. reproducing the disrupted labeling of candidate effectors with a GDP-locked RAB18 point mutant, or showing that RAB3GAP deficiency reduces binding of a candidate effector to RAB18.

      4) The putative role of SEC22A in regulating lipid droplet morphology relies on siRNA perturbations that are prone to off-target effects. This is especially concerning given the high degree of sequence similarity between SEC22A and SEC22B, the latter of which has a known role in regulating LD morphology. Rescue of this phenotype with a siRNA-resistant SEC22A cDNA would rule out this possibility.

      5) The finding of SPG20 protein abundance being affected by RAB18-deficiency relies on immunofluorescence with an antibody exhibiting cross-reactivity. While the authors do attempt to adjust for this non-specific background fluorescence, this conclusion would be strengthened by immunoblotting for a change in abundance of the specific band corresponding to SPG20. If confirmed, measurement of SPG20 transcripts levels would also help clarify the level of regulation for the altered protein abundance.

      6) The influence of stable expression of a RAB18 GTP-locked point mutant on cholesterol metabolism is intriguing but the experimentation appears perfunctory. For 14C-CE cellular levels in 14C-oleate-loaded cells (Figure 7A), the most striking difference is the greatly enhanced synthesis level of CE at t=0. Is the subsequent drop due to an effect of RAB18 on efflux, or simply a consequence of the higher starting level at t=0? For efflux assays on 3H-cholesterol-loaded cells (Figure 7B), the data is only presented as a ratio of 3H activity in media relative to lysates after a 5 hr incubation with HDL. Interpretation of these results would be aided by a more detailed analysis. How does 3H-cholesterol uptake compare after 24 hr incubation but prior to addition of HDL (t=0)? After the 5 hr HDL chase, are the differences in the ratio driven by an increase in extracellular activity, a decrease in intracellular activity, or both? Ultimately these conclusions would be better supported by a more detailed analysis. Does disruption of the candidate effectors phenocopy the effect of RAB18 disruption? Are any known mediators of cholesterol efflux affected by RAB18 disruption? While a comprehensive mechanism may be reasonably considered beyond the scope of this paper, some additional descriptive analysis would be useful in interpreting these findings.

    2. Reviewer #2

      This study used WT and mutant RAB18 to look for interacting proteins in normal and GEF-deficient cells. A catalog of interactions that are regulated by nucleotide binding and/or GEF activity were uncovered. Among identified proteins, there are known/established ones and there are some new ones. Initial validation was carried out for some newly identified effectors such as TMCO4 and Sec22A.

      Major concerns and questions:

      1) While the addition of new RAB18 effectors is useful to researchers who are interested in RAB18, the overall conclusion that RAB18 may regulate membrane contacts and lipid metabolism is not new.

      2) Figure 7: the effect of RAB18 on cholesterol esterification and efflux may arise from multiple causes. This set of experiments do not provide any real insights into RAB18's role in cholesterol metabolism.

      3) Given RAB18's interaction with ORP2, TMEM24 and OCRL, perhaps the authors may examine plasma membrane PIP2. The results would be more specific and novel.

    3. Reviewer #1

      This manuscript used proximity biotinylation to discriminate functional RAB18 interactions. The authors provide some evidence for several of the interactors and some functional data supporting a role for RAB18 in modulating cholesterol mobilization.

      Major concerns and questions:

      1) Based on the spectral counts, the author calculated a mutant:WT ratios as a readout to identify nucleotide-binding-dependent effectors. But it is important to show that WT protein and mutant protein have similar expression level to begin with. And the intracellular localization of the mutation and WT should also be determined. Do they show the similar intracellular localization?

      2) The ratio of mutation:WT is useful to remove some background. But this may omit some very highly interacting proteins just because their fold change is low. The converse is true for rare proteins. It would be better to have a list of candidate effectors based on the absolute counts.

      3) Sec22A knockdown will change the morphology of lipid droplets. A knockdown efficiency test and some representative fluorescence images here would make this data more compelling.

      4) Same comment for the cholesterol mobilization experiment. Expression level of the protein is needed. Figure 7A is rather confusing, as the Gln67Leu mutation already has higher CE before loading HDL. Why is this this? Better uptake or reduced efflux? What is the de novo cholesterol synthesis activity in this cell line?

    4. Preprint Review

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


      As a possible path to better understand and develop treatments for Warburg Micro Syndrome (WMS), the authors have investigated the networks of protein-protein interactions involving genes mutated in this rare genetic disease. The goals of the work are to identify new proteins involved in the pathophysiology of the disease and to better understand the molecular and cellular effects of disease-causing mutations. The data will likely be of interest to researchers studying WMS and RAB18, the protein focused on here, but reviewers expressed some concerns about the validation and interpretation of the presented protein interaction data.

    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 19 May 2019.]


      This paper describes five cryo-EM structures of ribosomal complexes apparently representing different stages of RF2-catalyzed translation termination. The novel observations here are that the tip of domain 3 of RF2 undergoes a rearrangement from an a-helical conformation to a b-hairpin conformation during termination that likely facilitates exit of the newly synthesized protein from the ribosomal polypeptide exit tunnel and that the ribosome can undergo two thermally activated, spontaneous conformational changes, a relative rotation of the ribosomal subunits and a swiveling of the 'head' domain of the small subunit, during termination that likely facilitate dissociation of RF2 from the ribosome. These are interesting observations that significantly extend our understanding of how class I RFs and ribosome conformational changes drive important steps during termination and, as such, all three reviewers recommended publication provided the following comments are addressed adequately.

      Essential Revisions

      1) The maps provided through the eLife system seemed to be unsharpened, as they showed very little detail. However, even after sharpening them with a B-factor of -100A2, they still did not show the expected features for their respective resolutions. My suspicion is that FREALIGN has been used to overfit the data. This should be addressed in the revision. It should be indicated whether gold-standard separation of halves of the data sets were used in the final refinements, or whether those were limited to a specific spatial frequency (like was done in the classifications). If the latter, those frequencies should also be stated in the manuscript, and they should be significantly lower than the claimed resolutions.

      In addition: a lot of basic cryo-EM information is missing: the authors should include: a) at least one micrograph image b) some representative 2D class averages c) local resolution maps of the five structures. Also, because the density of important parts of the maps seems to be a lot worse than the resolution claimed, it would be good to explicitly mention the local resolution of the important features discussed in the main text. d) for each structure, some zoomed-in figures with the density on top of the molecular model. These figures should be chosen as to validate the resolution claim. For example, in structures I, II and V, the RNA bases should be well separated (they do so at 3.6A), and in structures III and IV beta-strands should be well separated, and many (larger) side chains should be visible. In addition, some panels with density for the most important features of each structure should be shown. e) FSC curves between the refined PDB models and the cryo-EM maps are missing from the manuscript. These should be included. In addition, to evaluate potential overfitting of the models in the maps, for each structure, the authors should also include the FSC curves between a model that was refined in half-map1 versus half-map1, as well as the FSC curve between _thesame model versus half-map2.

      2) There appear to be many self-citations, and there are also a few places where relevant citations are missing or are mis-cited. There are too many to list individually, but, just a few examples: Page 4: the only citation for the phrase "recent biophysical and biochemical findings suggest a highly dynamic series of termination events" is a Rodnina paper. There are many, earlier papers from Ehrenberg, Gonzalez, Puglisi, Green, Joseph, etc. that should be cited here. Page 5: The only citation for the sentence "By contrast, biochemical experiments showed..." is a Green paper. There are earlier papers from Ehrenberg characterizing the effects of the GGQ-->GAQ mutations on the ability of RF3 to accelerate the dissociation of class I RFs from termination complexes that should be cited here. Page 5: There's a sentence that refers to X-ray, cryo-EM, and smFRET studies, but only provides citations to two smFRET studies (Casy et al, 2018 and Sternberg et al, 2009); Page 5: Moazed and Noller, 1989 identified and characterized the P/E hybrid state, but they didn't report that a deacylated P-site tRNA 'samples' the P/E hybrid state 'via a spontaneous intersubunit rotation'--that was later work from Noller and Ha; etc. There are several other instances of missing citations or mis-citations. We would ask that the authors review their citations with an eye for excessive self-citations and for missing citations or mis-citations. In this context, "Ensemble-EM" is also cited as a specific method in the introduction (Abeyrathne et al., 2016; Loveland et al., 2017). However, this method is more commonly known as (3D) classification of cryo-EM images, and there are many older, more appropriate citations.

      3) The sample imaged is a model sample generated by in vitro assembly with purified components of a termination complex. In order to mimic a bona fide termination complex, a short messenger RNA with a strong Shine-Dalgarno sequence followed by a start codon and immediately after by a stop codon was used (mRNA sequence: 5'-GGC AAG GAG GUA AAA AUG UGA AAAAAA-3'). Similar constructs were used to crystallize termination complexes in the past and it has been proven by smFRET experiments that, at least regarding ribosomal inter-subunit dynamics, this model sample behaves similarly to a real termination complex with a peptide linked to the P site tRNA. However, the nature of this model sample should be apparent for the non-specialist reader, highlighting its similarities with a real termination complex but also its possible limitations, especially regarding the "artificial" nature of having a stop codon so close to the Shine-Dalgarno sequence, a situation that never happens in real mRNAs. The authors should explicitly acknowledge this and discuss its implications in the main text.

      4) The authors set up a couple of somewhat 'strawman' arguments in claiming that: (i) there are discrepancies in the X-ray, cryo-EM, and smFRET literature with regard to whether ribosomes can undergo intersubunit rotation while bound to class I RFs or whether the non-rotated conformation of the ribosome is stabilized by bound class I RFs and (ii) class I RFs are able to terminate translation and dissociate from the ribosome without the aid of RF3. In the case of (i), it is obviously possible for class I RF-bound ribosomes to undergo intersubunit rotation while still favoring the non-rotated conformation of the ribosome. Moreover, there are enough differences between the cited studies, both in terms of the experimental conditions as well as the technical limitations associated with the various experimental techniques, that it is easy to rationalize differences with regard to whether the class I RF-bound ribosomes would be expected to undergo intersubunit rotation and/or whether the researchers would have been able to capture/observe intersubunit rotation. In the case of (ii), decades of biochemistry from Buckingham, Ehrenberg, Green, and others had already demonstrated that class I RFs are able to terminate translation and dissociate from the ribosome without the aid of RF3, and that the role of RF3 in termination is to accelerate the spontaneous dissociation of the class I RFs. If the authors want to highlight discrepancies in the literature, they should frame them in the context of differences between the studies, experimental design, limitations of the approaches/techniques in the cited papers that might account for such discrepancies. Re-writing this paragraph also in the light of addressing the missing citations and mis-citations pointed out under (2) will further help in toning these arguments down, which would strengthen the manuscript's scholarship.

      5) Class I RFs are post-translationally methylated at the Q residue of the GGQ motif of domain 3 and Buckingham, Ehrenberg, and others have shown that this methylation accelerates and/or facilitates class I-catalyzed termination both in vitro and in vivo. Nonetheless, Svidritskiy et al do not report whether and to what extent their RF2 is methylated. Was RF2 overexpressed in a manner that ensured homogeneous methylation or lack of methylation? If they are overexpressing prfB and not overexpressing prmC, it is likely that they have a mix of methylated and unmethylated RF2. Assuming they are using the wt E. coli prfB gene, then the residue at position 246 is a T, rather than an A or S, and Buckingham has shown that, in the wt T246 background, a lack of methylation at Q252 is either seriously detrimental in richer media or lethal in more minimal media. It was felt that a discussion of this issue was not needed in the main text, but that it would be helpful if the authors would include the important/relevant experimental details in the Methods section, for example, did they use the T246 wt E. coli variant of RF2; and did they overexpress prmC along with prfB?

      6) Structure I is denoted and treated as a pre-termination complex, but that does not seem at all possible given that the sample was prepared by incubating a pre-termination complex for 30 min in the presence of excess RF2, conditions that Figure 1-Figure Supplement 3 suggest results in robust termination. Structure I is more likely the non-rotated conformation of a post-termination complex that is in equilibrium with its rotated counterpart, Structure V. Based on my reading of the manuscript, it is likely that the authors understand this point, but are nonetheless using this structure as a mimic/analog of a pre-termination complex. If so, I think this is fine, but the authors should explicitly state that this is what they are doing. Related to this, the authors should clarify the description of their activity assay, show the raw data, and/or report 'Released [S35]-fMet (%)' instead of 'Released [S35]-fMet, CPM' on the y-axis of Figure 1-Figure Supplement 3; as the activity assay is currently described, reported, and plotted, it is impossible to determine whether RF2 is 1% or 99% active in termination.

      7) The final sentence of the manuscript reads: "Translation termination and recycling of the release factors and the ribosome therefore rely on the spontaneous ribosome dynamics, triggered by local rearrangements of the universally conserved elements of the peptidyl-transferase and decoding centers". There are a couple of problems with this sentence as written. First, smFRET experiments by Gonzalez, Puglisi, and Rodnina have previously shown that "Translation termination and recycling of the release factors and the ribosome therefore rely on the spontaneous ribosome dynamics" and the relevant articles should therefore be cited here. Moreover, given the data are static structures solved using a sample that is at equilibrium, it is not clear how the authors determined that these spontaneous ribosome dynamics were "triggered by local rearrangements of the universally conserved elements of the peptidyl-transferase and decoding centers". Isn't it equally possible, given the data presented, that the local rearrangements were triggered by the ribosome dynamics?

    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 24 May 2019.]


      The manuscript from Munkley, Elliott and colleagues shows that the epithelial splicing regulator ESRP2 is transcriptionally upregulated by the androgen receptor (AR), an observation based on a previous study of gene expression changes in response to androgen in the androgen receptor positive LNCaP prostate cancer cell line by some of these investigators. ESRP2 upregulation leads to a series of changes in alternative splicing, including switches with potential effects in disease relapse and metastasis which correlate with disease outcomes. Prostate cancer is driven by androgens via AR, and therapy involves androgen deprivation (ADT) to slow progression. However, it has also been reported that ADT promotes epithelial mesenchymal transition (EMT) (e.g. Sun et al, 2012), which might be related to the common progression to castration resistant prostate cancer following ADT. Munkley et al show that levels of ESRP2 are reduced after androgen deprivation in 7 prostate cancer patients. A number of other analyses using additional cell lines, a xenograft model, and data from other published prostate cancer samples leads to a general proposal that a decrease in ESRP2 expression (but not ESRP1) and some splicing changes associated with its depletion following androgen deprivation may be associated with prostate cancer progression and worse outcomes. One highlighted example is exon 30 in FLNB, skipping of which is associated with metastatic progression in breast cancer.

      A number of papers describing roles for ESRP1/2 in various cancers including breast, colorectal, lung, and ovarian carcinomas have yielded conflicting conclusions on the role of ESRPs or epithelial-specific isoforms it regulates, such as CD44, in cancer progression and/or patient outcomes. In some cases ESRPs are proposed to be tumor suppressors, whereas in other cases they are proposed to promote more aggressive cancers (see, for example, Zhang et al., Genes and Dev 33: 166-179 and references therein). As cited by the authors, a recent manuscript reports that duplication and increased expression of ESRP1 (which would largely promote the same splicing events as ESRP2) is associated with more aggressive human prostate cancers. Thus, a central question is whether the current manuscript can provide further clarity regarding the general role of ESRPs (including ESRP2) in cancer, including prostate cancer.

      Munkley et al raise the clinically-relevant point that current treatments for prostate cancer might have undesirable side-effects by inhibiting ESRP2 mediated splicing events. Overall, the manuscript is clearly presented. The data documenting the ESRP and AR regulated splicing program, and the restriction of tumor growth by ESRPs (Figs 1-4, 6) are very clear with very nice correlations between responses to ESRP overexpression, knockdown and androgen stimulation.

      Essential Revisions

      1) A key concern relates to the relative levels and effects of ESRP1 and ESPR2 under conditions of androgen induction or ADT in prostate cells. The authors do a good job documenting that ESRP2 is under transcriptional control of the androgen receptor, while ESRP1 is not, and that there is a 2-fold reduction in ESPR2 expression post-ADT in cancer samples. On the other hand, a) both ESRP 1 and 2 seem down-regulated at the protein level in androgen receptor-negative prostate cancer cells lines (probably by different mechanisms), b) both ESRP1 and 2 mRNAs are up-regulated in tumor samples compared to controls, c) both ESRP1 and ESRP2 are up- regulated in a cohort of metastatic patient samples, d) the correlation between ESRP levels and recurrence free survival is a more significant for ESRP 1 than 2, and e) a number of functional assays from this manuscript and other publications argue that both ESRP1 and ESPR2 can contribute to regulate overlapping targets relevant for epithelial-specific splicing. Therefore one key question that remains is to what extent the androgen-mediated transcriptional regulation of ESRP2 does contribute to splicing regulation in the context of the relative levels / activities of ESRP1: while a number of the results presented show that androgen treatment can promote splicing towards a stronger "epithelial" pattern, the authors should make additional efforts to demonstrate that ablation of ESRP2 alone (in the presence of ESRP1) leads to substantial changes in splicing that would be expected to explain the association of a loss of ESRP2 with worse outcomes, which is an essential point for the validity of their model. For example, an analysis similar to that of Figure 1A for ESRP1 should be included, as well as other experiments aimed to determine whether the activity of ESRP1 can buffer the effects of ATD on ESRP2.

      2) There is also a need for clarity in terms of the coherence of the predicted biological effects of the alternative splice site switches and at least one proof-of-principle demonstration that they are relevant for any property of prostate cells relevant to cancer, as it is difficult to draw firm conclusions from the data presented as to whether the regulation of ESRP2 by androgens is definitively associated with prostate cancer progression or outcomes in a positive or negative manner.

      a) Figure 5A shows exons that are more included or skipped in prostate cancer vs normal using TCGA data. But only 6 of the 44 ESRP-AR regulated events are highlighted on the plot, two of which do not change significantly, including FLNB which is highlighted in the abstract and is the only event used to test the response to the AR antagonist Casodex. All of the events from Fig 3 should be highlighted in Figure 5A, with ESRP activated and repressed exons clearly distinguished by colour or symbol. The authors should explain -when known- the nature of the differential activities of the isoforms and whether the isoform switch observed in the presence of androgens / mediated by ESRPs is predicted to contribute, repress or be neutral to tumor cell growth, apoptosis, motility, metastasis, etc. and therefore whether a functionally coherent program of alternative splicing is coordinated by ERSPs or whether various contrasting contributions are predicted whose relative significance will depend on context, etc. If not, is it possible to stratify the data e.g. by tumor grade, or by ESRP expression level? Would this for instance, reveal different classes where events such as FLNB do show a difference between cancer and normal in some classes?

      b) In Figure 6, why is FLNB e30 the only splicing event monitored for response to Casodex - especially since this is one of the events that is not altered between prostate cancer and normal tissue-? This Figure should be more systematic with more splicing events.

      c) Increased inclusion of exon 30 in FLNB (which occurs for example upon androgen stimulation) is consistent with inhibition of EMT (something that could be stated more clearly in the text). But there is no mechanistic model presented as to how a change in FLNB splicing (or other targets) impacts prostate CA. What about the other alternative splicing events highlighted in Figures 4 / 5? Even if FLNB splicing switches have been shown to influence expression of EMT markers in breast cancer cells (Li et al 2018), it will be essential to show that the degree of switch observed in prostate cancer cells (for FLNB or any other gene) has a relevant biological readout.

  2. Sep 2019
    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.]


      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.]


      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.