Preprint reviews by Mikhail V Matz

Epigenome-associated phenotypic acclimatization to ocean acidification in a reef-building coral

Yi Jin Liew, Didier Zoccola, Yong Li, Eric Tambutté, Alexander A. Venn, Craig T. Michell, Guoxin Cui, Eva S. Deutekom, Jaap A. Kaandorp, Christian R. Voolstra, Sylvain Forêt, Denis Allemand, Sylvie Tambutté, Manuel Aranda

Review posted on 18th December 2017

This is a very timely and extensive study of DNA methylation in a basal metazoan organism. Roles of DNA methylation in Metazoa remain unclear (beyond promoter methylation that is repressive but specific to vertebrates) and this study provides very important fundamental information. Fig. 1 is one beautiful example – and surprising, too! I totally did not expect to see prevalence of methylation in introns (just change the title to “DNA methylation landscape”, “epigenetic” is too broad). Overall, the experiment and sequencing effort are extensive and the quantitative results are very solid. My concerns are mostly about presentation and interpretation of the results.

Lines 75-91 and title of Fig 2 contain several sweeping claims that methylation actually causes things, such as suppression of transcriptional noise and suppression of variability of expression. Meanwhile, the evidence is purely correlational – given the data, it is impossible to say what causes what, or all these are caused independently by some unobserved factor. Please make sure, throughout the paper, that causation is never claimed (or otherwise implied by the context) based solely on correlation. Use language “linked to”, “associated with”, “correlates with”.

Lines 86-87: “consistent with the repressive nature of methylation on expression.” This is a very confusing phrase since it directly contradicts the data presented (Fig. 2 a,b) as well as several previous studies. Unlike promotor methylation, gene body methylation (GBM) is not associated with lower expression, instead, it is more prominent in highly expressed genes. GBM and promoter methylation are entirely different in function as well as in evolutionary history (promoter methylation is specific to vertebrates). This distinction is essential to maintain, so the statements “the function of methylation is conserved” is quite confusing (which methylation are we talking about? GBM? We are still not sure what the function is. Promoter? It is not conserved itself)

I have a problem with the notion that high-number exon prevalence over exon 1 in RNAseq data is good evidence of spurious transcription initiation. Please provide references to the literature where this has been experimentally established, because I can easily think of several alternative explanations.

I do like the methylation~noise association! But since you have distinct gene classes, can you plot them as more conspicuously different point colors? Also, I am surprised to see three gene classes – according to Dixon et al and other GBM papers, two classes make the most sense. Do you have a justification for three?

L121-123: “Analyses on laser-microdissected oral and aboral tissues further highlighted that most of the selected genes displayed strong and consistent tissue-specific methylation patterns, similar to findings in vertebrates” – this is an important result, can we have a figure illustrating it? And more details about how the methylation differences were quantified in this case?

One of my major concerns: I always strongly oppose discussions of detailed gene-interaction networks in non-model organism based on model organism data, such as Fig. 3 b, lines 143-146, 164-174, Extended data Fig. 1 and 2. Call it my private peeve, but I do not believe such detailed discussions are justified since (i) annotations of individual genes across great phylogenetic distances are often missing, uncertain or just plain wrong, to an unclear extent, and (ii) the degree of conservation of gene interactions is entirely unclear. Moreover, typically gene-wise discussions are little more than enumerating observations that fit some pre-conceived idea, without a clear null hypothesis (i.e, there is no robust criteria to tell whether the apparent support for the idea is stronger than expected by pure chance). The problem is, genes are many and data are noisy, making possible to find support for practically any idea, if one only looks hard enough. I therefore urge the authors to stay at the level of broad changes that can be associated with clear statistical significance measures, such as whole GO terms and/or pathways (Fig. 3 a, b), and abstain from discussing individual genes or their interactions.

That said, discussion of TRAFs might be interesting, not in context of JNK pathway but in the context of prior literature. TRAFs in corals appear to be unusually diverse and keep surfacing again and again under various environmental treatments, potentially constituting an important coral-specific plasticity mechanism not found in other creatures.

L 197-210 and Fig. 4: Change in cell size and skeletal morphology is a very cool result! The paper is written in a way suggesting (L197) that the hypothesis of larger cell size came *after* seeing specific genes doing something. If the authors can attest that this indeed was the order of events, and not the other way around (noticed larger polyps => found larger cells => picked genes that “made sense” to explain this), I will be completely fine with keeping the connection between gene-wise expression and larger sizes (this would be really awesome, in fact). But if not, not – because then it would be an example of a tendency I lamented about two paragraphs ago.

L225-241: I feel like this part of discussion/conclusions, talking about possible functional link between methylation and phenotype, its specific molecular mechanisms, and adaptive value, goes way beyond what is warranted by the data. The data do not establish the functional connection between methylation and phenotypic plasticity, and they do not show that observed changes really led to better fitness under new conditions.

The authors also take it as a given that plasticity would facilitate evolution by allowing “more time for genetic adaptation to occur” (L236-237). However, it more common to assume that plasticity would reduce the strength of selection and therefore slow down genetic adaptation. Please provide references from theoretical evolutionary biology supporting your view.

Lastly: one specific hypothesis I would really like the authors to consider: that observed methylation changes could be due to change in cell type proportions (which are differentially methylated), rather than being a result of methylation adjustments within each cell type. Perhaps data on methylation differences among microdissected tissues (mentioned briefly on L 121-123) could be used to explore the validity of this hypothesis?

cheers - and please review my bioRxiv preprints!


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Genetic architecture drives seasonal onset of hibernation in the 13-lined ground squirrel

Katharine R Grabek, Thomas F Cooke, L. Elaine Epperson, Kaitlyn K Spees, Gleyce F Cabral, Shirley C Sutton, Dana K Merriman, Sandy L Martin, Carlos D Bustamante

Review posted on 05th December 2017

Fun study!
A few thoughts :

My greatest concern for GWAS is that many individuals are related, which (as far as I could see from the methods) was not accounted for in GWAS analysis. As a result the analysis would have fished out predominantly markers that best discriminate between distinct relatedness clusters (as these clusters are also highly different in torpor onset, since heritability is close to 1). Although the true torpor-driving SNPs would probably be among those, my intuition is that the confidence would be greatly inflated since all related individuals are considered as independent samples. Is there a way to perform GWAS while controlling for relatedness?

If we account for relatedness, the next concern will be the small sample size (for GWAS), which is expected to lead to many spurious associations (considering that the amount of markers profiled ). The qq plot is not terribly convincing in this case. It would be best to use randomized data to generate a null distribution of pvalues. Randomizing would be trivial if all individuals we unrelated (just shuffle phenotypes), but to be honest I am not sure how to perform shuffling in this case - but it feels like there must be a way.

Third, eQTLs: please show that your top-GWAS SNPs are more likely to be eQTLs for hybernation-associated expression than a random choice of SNPs.

Fourth: I would like to discourage the authors (and everybody else) from weaving extensive "just so stories" about genes that seem to "make sense". It is a slippery slope - you start telling what *you* think should be going on rather than objectively summarizing the data. That said, this paper is not too bad in this respect, I've seen much worse.

Minor stuff:

"genetic architecture" in the title is misplaced (as has been pointed out by a few tweeps already), it would be more appropriate to say "Natural genetic variation underlying onset ..." or something like that.

Make sure all the labels in the figures are described in the legend, for example what are the "States" in Fig 6.

Very minor: I would use points instead of population names in Fig 2 B - the names overlap too much, looks funky.



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