Journal

Ecology and Evolution

Fields
Ecology
Nature and Landscape Conservation
Ecology, Evolution, Behavior and Systematics
Reviews

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Reviews

  • In the manuscript “Revisiting the phylogeny of Wolbachia in Collembola”, Ma and coworkers sample Wolbachia strains from various springtail host species and investigate their phylogeny. Wolbachia are the most common invertebrate symbionts and are found in most hexapod orders. However, the Wolbachia found in Collembola are genetically very distinct from all other Wolbachia strains, and are thought to be involved in creating parthenogenesis in many collembolan taxa. Therefore, this study is relevant to the field of endosymbiont research and entomologists alike. The main findings are 1) All Wolbachia from springtails form a monophyletic group, hereby correcting a previous study; and 2) Wolbachia has multiple origins in springtails. The manuscript is well written, the figures are clear and visually appealing, and the phylogenetic analyses are detailed and thorough. I believe the paper will be a valuable contribution to the Wolbachia literature. One critical point would be how the authors show that Wolbachia from Nelipleona are supergroup E strains and not a distinct strain. In the 16S+ftsz analyses, 3 species of Nelipleona are included, but in the MLST analysis, only a single species is analysed. To exclude this is simply a sampling artifact, the authors should perform an additional 16S+ftsz analysis using only the taxa used for the MLST analysis. If the single Nelipleona Wolbachia is distinct from supergroup E in there as well, this would support the author's argument even further. I also see a few problems and errors with how phylogenetic terms are employed and think that the paper could be improved by discussing not only Wolbachia phylogeny, but also its implications for Wolbachia evolution in springtails. Please find more details on these and other points below, hopefully constructive.

    Line 54–55 There is no direct evidence for Wolbachia– mediated speciation. This makes it sound as if there is.

    Line 90–91 This sentence, and other similar ones in the manuscript, is very problematic. Collembola are not an “ancient group of arthropods”. Arguably, all recent taxa have evolved for the same amount of evolutionary time. Also, collembolans did not “branch off” anything. What you may want to say is that the last common ancestor of Collembola and Insecta is very old.

    Line 116–117 I would advise against using terms such as “intermediate”, “basal”, “in between”, etc when describing phylogenies, this is simply wrong. Trees show sistergroup relationships and should also be described as such. For example, instead of saying “taxon x” is the “most basal” taxon in this tree, one should use “taxon x is the sistergroup to all other taxa in this phylogeny”. Please see Krell & Cranston (2004: Which side of the tree is more basal? Systematic Entomology 29, 279-281) for more details.

    Line 303 I don't see the point of “data available on request” statements. Including the results of recombination analyses in the supplementary files does not require a lot of work.

    Line 311 Please rephrase problematic formulation: “were separated by wThou“

    Line 313 Please rephrase “outermost taxon in clade E”

    Line 337–348 I don't think it is necessary to mention this in the manuscript. Maybe just drop an email to the database curators?

    Line 368–370 How can non-matching phylogenies be “intensified” by long branches? To match phylogenies, one only looks at branching patterns and not at branch lengths.

    Line 371–375 Here you use the 16S+ftsz phylogeny to argue that geography has played a role in diversifying Wolbachia from springtails. However, just in the paragraph before you make the point that this phylogeny is “insufficient” for classification of Wolbachia strains.

    Line 377–379 It would be interesting to read a little more on how you would interpret the non-matching phylogenies of Wolbachia and Collembolans.

    Line 393–394 In your Figure 1, Supergroup E is sister to Supergroups A+H; Supergroup B is the sistergroup to the former 3! You should also mention that this phylogeny is not very well supported, except for the monophyly of most supergroups.

    Line 399–404 Gerth et al did not claim E is “basal” to all other supergroups, but rather that it is the sister to all other >investigated< supergroups. Also, the LBA problem has been thoroughly addressed in the cited study. I am not saying that there may not have been a problem with LBA in this study, but if you make this argument here, it should be explained better.

    Figure 1 shows an unrooted tree, which I think is fine. However, I wonder why you displayed in this way, and not as a truly unrooted phylogeny. The way the reader perceives this tree is that it is rooted with supergroup C. I think it is always best to show unrooted phylogenies in an unrooted manner.

    Table A3 is huge and only repeats information from PubMLST database. Maybe think about omitting it.

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  • The authors present a study on a rare spider restricted to a particular environment (salt crusts of dry water bodies). Although the focus of this work is determining the interconnectivity among populations by means of molecular markers, it is worth to mention that the sampling effort was also informative to the distribution of the species which was poorly known. The methods to address the question are appropriate but a larger number of markers (which might not be easy to obtain in non-model species) would have been more powerful. I recommend the publication of this work but not before some issues (listed below) have been addressed.

    1. In the introduction (page 3, lines 49-53) it is stated that “previous studies have established a correlation between the hydrographic history […] and the distribution of aquatic organisms”. Could you provide further detail? Do you mean genetic structure of populations or species diversity distribution, or something else?

    2. I think figure 3 is superfluous and confusing. I found clearer the text in pages 4-5 (lines 84-103) that the figure itself. I suggest to remove it. Alternatively, I would introduce the following changes: first, since it shows theoretical/potential patterns, I would remove any reference to the real data and I would based the figure on some ideal species with hierarchical geographical structure. Then I would include some map (invented, just for illustration of this ideal species) to make spatially explicit the phylogeographic pattern that the figure is intended to show.

    3. Although phylogenetic analysis was performed on each locus separately, results of those analyses are not presented in detail (but mere describe in two sentences, lines 241-244, ). I think that given the difference of intraspecific polymorphism between markers (table 3) it is important to show the result for each marker separately.

    4. Three analysis of genetic differentiation were carried out with the software ARLEQUIN 3.5. There are several details from these analyses that are not clear. First of all, how the two loci loci were used? Were the sequences concatenated or were analyzed separately? Also, authors use a method that they describe as percent sequence divergence among populations. I am not sure to which of the many analysis implemented on ARLEQUIN this refers to. Was it the “compute pairwise differences” option? Please include the reference to the original method/statistic (e.g. Nei and Li, 1979 if it is indeed pi what is reported) and, optionally, a more clear reference to the nomenclature used by ARLEQUIN.

    5. For the analysis performed with IM it is necessary to define ESS (line 222) and what are the “parameters” m1, m2, 95Lo and 95Hi (line 223, note that 95Lo and 95Hi are not parameters). The presentation of the results of the IM analysis could be improved: Why are not the Highest Density Probability intervals reported? What are the HiPt values and why “confidence intervals” do not include the reported HiPt value (Table 8)? What were the ESS for each run? Why is each run analyzed separately? I think the analysis of the different runs combined will be more accurate and will provide with a smaller figure 5 (which could also be plotted as a line instead of “cloud of points” for a more easy interpretation). Also, the evidence for incomplete lineage sorting (ILS) as source of shared haplotypes is very weak, not to say null. The results are showing clearly that a low migration rate cannot be excluded. This is not surprising, since the power for such analysis come from having data from many independent loci and this study has only two. Abstract, discussion and conclusion should not include the message that the IM analysis nor the genetic data suggest the absence of gene flow. If authors want to favor the ILS explanation they should based it on other evidence (e.g. absence of observed ballooning in the species, etc) but making it clear that the IM analysis could not determine the presence or absence of gene flow.

    6. In the beginning of the discussion it is said that “three alternative hypotheses were tested” (line 292). I think the wording of this sentence could be more accurately. First, no formal test was performed (at least not to test between dispersal during intermittent flooding and frequent aerial dispersal), results are discussed around those hypotheses. Also, we could argue that reality is more complex having elements from those hypotheses (some population might be completely isolated while others might exchange individuals through different dispersal mechanisms); so these hypotheses are not necessarily “alternative”.

    7. Clarification about my answer to the question on the number of figures (Manuscript Structure/Number of figures is: Too many): I find that the choice of figures could benefit of some revision. As suggested above, I would remove figure 3, I would simplify figure 5 to reflect only the combined analysis of the four IM runs. Also figure 1 seems redundant with figure 2. However, I would show (in figure 4) the phylogenies estimated for CO1 and H3 in addition (or instead) of the phylogeny estimated from the concatenated data.

    8. Clarification about my answer to the question on the number of figures (Manuscript Structure/Number of tables is: Too many): Table 8 could be removed

    Ongoing discussion