The preprint by Bertels et al.  reports an interesting application of the well-accepted idea that positively selected traits (here variants) can appear several times independently; think about the textbook examples of flight capacity. Hence, the authors assume that reciprocally convergence implies positive selection. The methodology becomes then, in principle, straightforward as one can simply count variants in independent datasets to detect convergent mutations.
In this preprint, the authors have applied this counting strategy on 95 available sequence alignments of the env gene of HIV-1 [2,3] that corresponds to samples taken in different patients during the early phase of infection, at the very beginning of the onset of the immune system. They have compared the number and nature of the convergent mutations to a "neutral" model that assumes (a) a uniform distribution of mutations and (b) a substitution matrix estimated from the data. They show that there is an excess of convergent mutations when compared to the “neutral” expectations, especially for mutations that have arisen in 4+ patients. They also show that the gp41 gene is enriched in these convergent mutations. The authors then discuss in length the potential artifacts that could have given rise to the observed pattern.
I think that this preprint is remarkable in the proposed methodology. Samples are taken in different individuals, whose viral populations were founded by a single particle. Thus, there is no need for phylogenetic reconstruction of ancestral states that is the typical first step of trait convergent analyses. It simply becomes counting variants. This simple counting procedure needs nonetheless to be compared to a “neutral” expectation (a reference model), which includes the mutational process. In this article, the poor predictions of a specifically designed reference model is interpreted as an evidence for positive selection.
Whether the few mutations that are convergent in 4-7 samples out of 95 were selected or not is hard to assess with certainty. The authors have provided good evidence that they are, but only experimental validations will strengthen the claim. Nonetheless, beyond a definitive clue to the implication of selection on these particular mutations, I found the methodological strategy and the discussions on the potential biases highly stimulating. This article is an excellent starting point for further methodological developments that could be then followed by large-scale analyses of convergence in many different organisms and case studies.
 Bertels, F., Metzner, K. J., & Regoes R. R. (2018). Convergent evolution as an indicator for selection during acute HIV-1 infection. BioRxiv, 168260, ver. 4 peer-reviewed and recommended by PCI Evol Biol. doi: 10.1101/168260
 Keele, B. F., Giorgi, E. E., Salazar-Gonzalez, J. F., Decker, J. M., Pham, K.T., Salazar, M. G., Sun, C., Grayson, T., Wang, S., Li, H. et al. (2008). Identification and characterization of transmitted and early founder virus envelopes in primary HIV-1 infection. Proc Natl Acad Sci USA 105: 7552–7557. doi: 10.1073/pnas.0802203105
 Li, H., Bar, K. J., Wang, S., Decker, J. M., Chen, Y., Sun, C., Salazar-Gonzalez, J.F., Salazar, M.G., Learn, G.H., Morgan, C. J. et al. (2010). High multiplicity infection by HIV-1 in men who have sex with men. PLoS Pathogens 6:e1000890. doi: 10.1371/journal.ppat.1000890
The revised version by Bertels et al. shows a considerable improvement when compared to the previous version. It has a better flow and is much easier to read. For this, I would like to congratulate the authors for the effort and work they have put in this revised version. This was worth it. The first reviewer has no further major comment but the second reviewer (reviewer 3 of the previous version) is still unconvinced by the conclusions. I have to confess that I am still myself unsure that the patterns reported here constitute strong support for selective effects, although they can be considered as good clues. I however found that the approach proposed here is clever and is worth delivering to the community. Thus, I think that on top of the major improvements the authors have made so far, some extra work (mostly on writing) is still needed before I can recommend this preprint.
While revising this ms, please keep in mind that:
Personal suggestion for improvement:
To assess the independence between the mutations (current rev 2), the authors could first test for recombination (using 4-gamates like test or decay in LD or any \rho estimation method) and, if no recombination, built phylogenetic trees with ancestral states reconstruction for each sample (and even use the MRCA sequence to orientate if they include an outgroup). They could then see whether convergent mutations occurred 1 or several times in the samples and eventually test if they hitchhike on each other (please take this only as a suggestion, not as mandatory extra work).
The remark of the ex-reviewer 2 of the previous version is still valid. Why 10/11 of the non-synonymous convergent mutations are either G->A or A->G. It deserves at least to be reported in the results and discussed in the article. Do you observe the same for the synonymous convergent mutations? If you would assess the expected number of convergent mutations by types of mutations (and not globally) is this still very unlikely?
The level-off of the decline reported for Figure 1 may be slightly overclaimed (L120). This is based on 11 mutations that cannot be below 1 (while the null model can go well below 1). What do you observe for the synonymous convergent mutations?
The paragraph L382-L388 needs to clarified.
On a didactic level A Black&White version of this ms is almost impossible to follow as the colors on the plots look identical. May I suggest that you use filled and empty circles and dashed, pointed and continuous lines on top of the colors (if you like colors) in all figures? Another possibility is to use dark vs light colors.
Typos: - L43: remove 'will' to change the sentence into present time - L411: positions -> position (delete the 's')
To conclude, I think this ms is evolving in a right direction although it still deserves some extra work. I almost convinced that the next version will be ripe for recommendation. Take all the suggestions of the reviewers as constructive feedbacks (or genuine incomprehensions) and include a point by point response to all comments along with your next version.
I am satisfied by the comprehensive revisions as performed. A few minor points for consideration:
1) It looks like only the maximum likelihood "model selection" clusters from MACML have been used / displayed. Model selection (linear hot/cold cluster detection) appears to have been informative in this way, but if it was not examined already it is worth mentioning that it may be illuminating to use the computationally intensive model averaging (over "hot" and "cold" spots hierarchically detected) to provide a pseudo-continuous profile of clustering across sites. See flag -m in the MACML user manual.
2) line 36, no "," after "are"
3) line 60, needs "," after "load"
The ms by Bertels et al. has been reviewed by three independent experts in population genetics and molecular evolution. All three reviewers found that this ms has a good potential but also raised important points that need to be addressed before it can be recommended by PCI Evol Biol. Reviewers 1 and 2 suggested several articles that the authors must read and potentially include as references in their revised version. Reviewers 2 and 3 were convinced that the convergence approach is interesting but at the same time show some concerns on the power and the reliability of the method. I also agree with reviewer 3 that this study should not be oversold, as results are not extremely robust as they are.
Please address carefully all points raised by the reviewers and revise you manuscript accordingly. A point by point response to their comments must be included along with your revised version of the ms.
The ms by Bertels et al. reports an analysis of nucleotide convergence pattern in HIV. It reads well, is mostly sound and quite easy to follow. I only however few remarks that could potentially help improving its content.
:: Major ::
Although the authors demonstrate clearly that some positions have mutated several times independently in different patients, I am not convinced this is really due to selection. One important part of the puzzle (that is never discussed) is the type of mutations the authors have found independently repeated. A summary table listing all types recurrent mutations (i.e. the type of nucleotide change) is required in the main text. As they are mostly G->A mutations (Table S1), this is suspicious as HIV has a very strong mutational bias in that direction. It would be much more convincing to find that the apparently selected mutations are not all of the same nature. If I understood Table S1, all are G->A or A->G, but the latter could simply be mis-oriented mutations (see the minor points below).
I am not sure how to interpret biologically the value of H. H mixes drift, selection and recurrent mutations. Some other metrics such as the number of alleles (2, 3 or 4) are more directly measuring the number of mutations at a site.
As a general comment, I think there is room for improvement in the general flow of the article. While reading it few times, I am still confused about the statements. Casual readers could easily get lost.
The weak overlap between the author list of potentially selected mutations with the one from Wood et al. can suggest that the data are quite noisy and the overall power of the method(s) are simply quite weak. Although I believe this was a clever method, more discussion on this point (limitations of the method) would be welcome.
:: Minor ::
l142 - why did the authors chose to report only the results for >= 3 populations ? What about providing the full distribution ? Can the authors also give the raw number (and not only the %). Furthermore, although this is statistically significant, it leaves 30% that are outside the gene. This cast doubts on the strength of the reported pattern.
l70 - the dN/dS strategy would also work if selection affect less dS than dN, not necessarily that dS has to be immune to selection.
l303-307 - the ancestral sequence is not always the consensus. Mutations could simply reach high-frequency. This is true even in the standard neutral model (see expectation of the unfolded SFS). So I guess the direction of mutations may be unsure and therefore authors may want to pool symmetrical mutations (i.e. G->A with A->G and if mutations can occur in the two strands also with C<->T).
l309-315 - why doing an alignment with a reference sequence ? (and not only all sequences together without the ref). This seems odd.
l348 - Did you consider using an entropy between 0 and 1 instead of [0,2] ? You would need to use log4 instead of log2. Eventually, you could change the base of the log depending on the number of alleles.
l220-l223 - Please clarify as it is slightly confusing as it is.
By re-analyzing 95 independent full-length HIV env genes this study relates the extent of (genotypic) convergent evolution to the presence of selection acting on specific mutations. The authors find an excess of convergent mutations in the gp41 region of the env gene when compared to a neutral model, supporting the view of positive selection acting on these mutations as has previously (partially) been found by Wood et al. 2009 using dN/dS approaches. One advantage of their approach to the former though is that is allows identifying positively selected synonymous mutations. Furthermore, the authors found "convergent mutations" are not more likely to be non-synonymous than under a neutral model. Overall the authors conclude that the extent of convergent evolution can be a good predictor of positive selection.
GENERAL OPINION AND MAJOR POINTS
I am a bit split on this paper, and I think the reason is that it tries to convey an easy to grasp story ("Convergent muts are under pos select and private muts under neg selection during acute infection of HIV-1" as one of the authors put it on Twitter), while exactly this simplification makes it sometimes sound like a slight oversell.
First, this paper does not introduce a real statistical method to detect selection. To be fair though this is not what the authors claim (or what they are trying to do). However, if the authors were thinking about making it a "real" method, it would most certainly require intensive simulations of genomes under selection (along independent replicates) to assess the power of the method, and under which situations it is able to detect it. Despite not being a method paper though, the latter point needs to be addressed more thoroughly I feel. There are a couple of crucial assumptions that probably for the sake of conciseness have not been discussed: For this method to work the viruses (or the system to be studied) need to be "unconditionally selected", i.e., selection pressures/environmental conditions and mutational effects need to be (close to) identical. This, however, implies that epistasis does not affect the evolutionary dynamics, and/or that the genomic basis / mutational target size for this trait is small. For instance, if a trait with a highly polygenic basis and thus a large mutational target size was under selection, this approach will probably not perform well (note that selection strength is potentially equally crucial here). Thus, viruses might really be the perfect if not only system where the authors' approach can be applied. Thus, I think the real advantage of this approach comes out when relating and "benchmarking" it to the results by Wood et al. which focus on the same gene (env; and its gp41 part), but relies on a dN/dS approach, and thus cannot identify synonymous mutations and lacks power when applied to population genetic data (as the authors rightfully cite Kryazhimskiy & Plotkin 2008 here). Invoking selection on a part of the genome that has been shown to be under selection is furthermore not very exciting unless the results are related to an earlier study as proposed. Furthermore, the idea of using convergent evolution to detect targets of selection seems a bit trivial when having some background in experimental evolution, where independent experimental replicates are a requirement for invoking selection on a genetic variant (and getting the result published). Note that Andreas Futschik has recently developed an just uploaded a paper on arxiv called "An omnibus test for testing global null hypotheses.", where he derives a statistical framework for inferring sites under selection where that have not been selected uniformly across all replicates (i.e., where not all experimental lines show convergent genotypes). However, when seen as a "proof-of-principle" paper though and results are related to the Wood et al findings, and the underlying assumptions are discussed a bit more in detail, this manuscript can turn into a very nice and stimulating paper.
More specific, minor points (line L; referring to the authors' line numbers) separated by section:
Thank you for the line numbers. Please check your spelling of "re-analyzed vs. reanalyzed" and be coherent.
L23 "highlighting the highly..." But this statement strongly depends on the effect-size of the selected sites. Also shouldn't it be non-synonymous?
L41 "small genomes, high mutation rates,..." The mentioning of high mutation rates is a bit misleading here since you have not defined on which scale you consider genotypic convergent evolution. If you were considering haplotypes or entire genomes, high mutation rates probably won't facilitate convergent evolution.
L54 "Convergence is also..." I thought that convergence is an outcome rather than an initial state. Do you mean reduced diversity here?
L62 "These mutations seem to be..." This paragraph is way too long and complicated. Please consider splitting into two.
L72 "is less reliable when..." Consider adding the point that synonymous mutations cannot be detected by this approach either.
L83 "convergent mutations" I think it was OK for the abstract, but you should give a formal definition of what you actually mean by that here. E.g., you could introduce the term more formally in line 80 at the end of the first sentence.
L85 "private mutations" Please add formal definition here.
Figure 1 On the y-axis: You probably mean "Mean Number ..." right? Otherwise non-integer numbers (10^-2) are a bit weird/unclear. What are the dots (means?) and the lines (standard deviations?). Please add in legend.
L106 "Whereas ..." To me it rather seems that 1-3 mutations are more or less equal between the two groups.
L118 "In total ..." Is there a list of these 19 candidates? If so please add reference.
Figure 2 I would switch the two axis such that it rather looks like a Manhattan-Plot. You could then add a line where HIV populations = 5 above which you consider all mutations as potential candidates of selection. I dont think that the black line is needed here. Also, I do not understand the meaning of the red lines here? What is meant by "within one category" (L127)
L127 "position" typo -> positions
L140 "single population mutations" Do you mean mutations that only appear in a single population?
L142 "in only a single..." Do you really mean individual here? It's a bit misleading after you have talked about populations the entire time.
L143 "p-Value" typo -> p-value
L164 "Interestingly, we found..." 1. Change in tenses 2. Where is this result shown?
L167 "are under positive selection" But this would also require different selection pressures that you somehow ruled out, right?
Figure 4 What is happening for HIV Pop = 6? Is this actually discussed somewhere in the text?
L178 "We obtain a significant ..." Are these results shown somewhere and what does "significant" mean here (which test; p-value)?
L188 "On the other hand..." See comment above.
Figure 5 I don't think it's necessary to show that wide range (y-axis). Could you zoom in and add more ticks/lines?
L270 "higher than the median..." How meaningful are these diversity values if the distribution seem to span almost the entire range?
L279 "Nevertheless ..." Without any idea about epistasis or mutations at other genes -- since these mutations could also just be compensatory mutations for "true" underlying adaptative mutations with pleiotropic side effects, I don't think you can make any statement about effect sizes. Actually, I am also not quite sure that without prior knowledge about potential targets of selection you would be able to make any statements whether convergent mutations are primary mutations (i.e., mutations that actually rise in frequency due to the selective pressure applied such as a special drug treatment) or secondary mutations that compensate for the deleterious side effects of the primary mutations (as often observed for resistance mutations).
L283 "Finally..." First, and just to point out the obvious: To make use of this approach you need a lot of (independent) data. While it is intriguing that a frequency of 15% of convergent mutations is enough to make statements about potential targets of selection, you clearly would not be able to make these statements if you observe a mutation in one out of 7 populations (i.e., the power rather comes from absolute than from relative numbers). Thus, I would make the first point and also rather state absolut numbers as these relative numbers seem misleading.
Second, how independent are your "independent samples". Is there a chance that some patients might have been cross-infected which could introduce correlations/relatedness between samples? Relatedly, are those 15% of the strains carrying the most frequent convergent mutation more similar to one another (e.g., in terms of diversity) than the rest (which could maybe be checked with some permutation test)? If so that could be indicative of the mutation being genotype dependent (i.e., epistasis).
MATERIALS AND METHODS
L300 "founder strain" Full stop missing
L300 "those sequences" typo -> sequence
L312 "alignments were performed" Please specify the options used for reasons of reproducibility.
L322 "Neutral mutation distribution model"
I have several related questions on your neutral model. First, regarding your definition of a convergent mutation. Since you are using different consensus sequences, what if one of the consensus sequences was already carrying the "convergent mutation" (or rather nucleotide)? Would it still be called (and counted) as a convergent mutation? Or in other words, is a mutational event required for calling something convergent mutation?
Second, is your model truly neutral? I was wondering whether using the (upscaled) empirical transition rates in the substitution matrix isn't actually a mutation bias, since you only observe those mutations in your sequences that are not selected against (or filteder by selection for that matter)? Wouldn't equal mutation rates be more congruent with the neutrality assumption?
Finally, maybe a statement about the (simulation) program/software that has been used would be good, as well as putting a file for re-doing the simulations in the SI.
L378 I am not sure the editor is usually mentioned.
SI txt: Maybe some additional text explaining the content of this file would be nice.