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Dear Dr. Vitales and colleagues:
Thanks for revising your manuscript based on the minor concerns raised by the reviewers. I now believe that your manuscript is suitable for publication. Congratulations! I look forward to seeing this work in print, and I anticipate it being an important resource for researchers studying Phaeophyceae biology and seaweed phylogeography. Thanks again for choosing PeerJ to publish such important work.
Best,
-joe
# PeerJ Staff Note - this decision was reviewed and approved by Patricia Gandini, a PeerJ Section Editor covering this Section #
Dear Dr. Vitales and colleagues:
Thanks for submitting your manuscript to PeerJ. I have now received one review of your revision (the original reviewer 1), and as you will see, this review is now also very favorable. Well done! Nonetheless, the reviewer raised some very minor suggestions, and areas where the manuscript can be improved. I agree with the reviewer, and thus feel that his/her concerns should be adequately addressed before moving forward.
Aside from the criticisms raised by the reviewer in his/her report, be sure to thoroughly evaluate the marked-up manuscripts kindly provided by the reviewer.
Therefore, I am recommending that you revise your manuscript accordingly, taking into account all of the issues raised by the reviewer. I do believe that your manuscript will be ready for publication once these minor issues are addressed.
Good luck with your revision,
-joe
The revised manuscript fullfil the requirements and the authors have worked well through the comments. The present version improves the otherwise already good version submitted in the first round, by including a new phylogenetic analysis and a very comprehensive discussion, which tackles in my opinion all the relevant hypothesis that may explain the obtained results.
Please find just some minor corrections and suggestions for rephrasing in the attached pdf. Most of the rephrasing suggestions are indeed just suggestions subject to the author’s criteria. See also two comments about the methods (sect 2 experimental design). The manuscript is in my opinion almost ready for publication.
Lines 149-151: It is not stated how the sequence evolution models are selected. I guess it was directly done with PartitionFinder at the same time the partitions were selected.
Lines 159-162: Need to state that the partition is the same as in BI, or that has been chosen with PartitionFinder. But why is the sequence evolution model different? Please provide some information here.
no comment
Dear Dr. Vitales and colleagues:
Thanks for submitting your manuscript to PeerJ. I have now received two independent reviews of your work, and as you will see, the reviewers raised some concerns about the research. Despite this, these reviewers are optimistic about your work and the potential impact it will have on research communities studying Phaeophyceae biology and seaweed phylogeography. Thus, I encourage you to revise your manuscript accordingly, taking into account all of the concerns raised by both reviewers.
Remarkably, both reviewers provided edits on marked-up versions of the manuscript. Be sure to address these issues as well as those raised in their general reviews. While most of the concerns of the reviewers are relatively minor, this is a major revision to ensure that the original reviewers have a chance to evaluate your responses to their concerns.
I look forward to seeing your revision, and thanks again for submitting your work to PeerJ.
Good luck with your revision,
-joe
The article is generally well written. I just found a few mystakes which are annotated in the attached pdf. Find also annotated in the pdf suggestions for rephrasing.
References used are complete and the background provided is clear and sufficient to show the state of the art of the topics addressed. The article clearly contributes to the topic with its results, and in fact proves false a previous hypothesis, so they are no doubt relevant to the topic.
Introduction
Line 40: I suggest rephrasing, as genetic data cannot be “a step” per se: “the increase of molecular genetic data has been a key step to achieve a better understanding of biodiversity, including fields like taxonomy and systematics”. If not, replace has by have as data is plural.
Paragraph 1: consider including the concept of integrative taxonomy as it claims for taxonomy to reflect evolutionary patterns (Stuessy, 2009, Plant Taxonomy, second. ed.; Schlick-Steiner, 2010, Annu Rev Entomol, 55: 421–438)
Line 61: I suggest “recolonized” instead of “reinvaded”
Line 90: “based on a fairly limited inter-population sampling for these taxa”: the sampling does not seems too low compared to the present study: 18 sites for D. fascicola and 7 for D. mediterranea (for the psbA analysis, table S1 of the cited study). Please specify what is meant with this statement. How is your sampling significantly better?
Line 94: I suggest rephrasing: “as the only example of Dictyota species having evolved from a common ancestor and also sharing their distribution along the Mediterranean Sea and the Atlantic Ocean” -> “as the only example of two sister Dictyota species occurring along the Mediterranean Sea and the Atlantic Ocean”. And please consider moving it as the last sentence of paragraph
Line 107: I suggest rephrasing: “we discuss the contribution of our results to the knowledge about the Atlantic-Mediterranean transition…”
Material and Methods
Line 156: cite PopART: Leigh, JW, Bryant D (2015). PopART: Full-feature software for haplotype network construction. Methods Ecol Evol 6(9):1110–1116.
Results
Line 199: uniform the paragraph please. When describe the parameters you can choose whether to put the values in brackets or not, but do the same for all parameters. I would suggest to at least write the symbol used in the table, while the values are probably not necessary since they are easy to reach in Table 2.
Line 201: nucleotide diversity is average number of nucleotide differences per site, so in my opinion a difference of 0.0008 should not be considered. I would be better to say that the 2 regions showed very similar nd.
Population codes: using simpler population codes would help the reader (e.g. M1.1: D. mediterranea pop 1 individual 1).
Figure 2: Please consider to invert the tree in B, so that the terminal nodes are on the left and the root on the right. This would help to graphically compare the two trees. In this case the pairs of incongruent individuals could be linked with lines to make it easier to find them.
Figure 3: See annotated comments in the pdf. I suggest to make a loop between M13 and M10, or any other graphical resource to avoid the crossing lines. Indicate the number of unsampled intermediate when there are more than 4-5 would be helpful. Same fig S1.
Sampling is said to be one of the majors improves of the study. Although sampling is indeed relatively high, sampling sites are often extremely close to each other and the sampling of Tronholm et al 2010 seems to be not that lower (18 sites for D. fascicola and 7 for D. mediterranea). Sampling for phylogeographic purposes should be planned in a way that the distribution of the species analysed is representatively sampled. I am however aware that it is not always possible to plan a perfect sampling campign. However I would suggest adding the D. mediterranea sequences from the Adriatic (from Tronholm et al. 2010) to partly fill the sampling gap for this area.
Considering that the sampling is partly overlapping with that of Tronholm et al 2010, it seems that a more efficient approach would have been to use their published sequences and sample the extra populations sampled. Thus resources could have been directed to sequence some more regions, which as the authors state (line 239), is one of the weaknesses of the study. This would have increased the relevance of the present study. However, I am aware that this would be a different study and therefore I do not ask for any change in this direction.
To improve the replicability, it would be helpful to use an aligning algorithm at least for the first step (e.g. as implemented in Clustal), and thus minimize the adjustments made by hand.
I suggest an additional phylogenetic ML analysis to complement the Bayesian Inference. That will most probably not change the essential results but obtaining redundant results from two different approaches increase the robustness of the results.
I agree on not concatenating the two alignments, since they are loci that undergo independent evolution. I suggest however to mention it and cite some of the revisions discussing the topic (e.g. Degnan & Rosenberg, 2009, Trends in Ecology and Evolution, 24(6), 332–340). It would also be useful a short description of the properties of the two genomes analysed here (ie cpDNA and mtDNA), such us inheritance pattern (see e.g. Peters et al., 2007, Europena Journal of Phycology, 39, 235-242).
PopArt default settings: since not only the most parsimonious paths are considered, it would be useful to describe these settings with more detail.
Line 163: n=18 is a value you choose or it is fixed by the program developers? please argue why using 18 if you chose it.
The manuscript is a significant contribution to the systematics of the seaweed species studied and to the biogeography of the Atlantic- Mediterranean transition. Despite the existence of two comprehensive phylogenetic studies on the genus Dictyota, the current paper contributes with a wider sampling and a zoomed perspective that contradicts a previous hypothesis on the biogeography of the 2 species, although it could be better explained how the current study overcome the previous ones (see my previous comments on sampling).
The authors in general interpret well their results, propose hypotheses to continue the study of the topics raised and properly stress the limitations of their own study, avoiding too much speculation. However, a limited sampling and the use of only 2 molecular markers challenges the prevalence of the results obtained here.
Furthermore, I suggest to add an alternative interpretation of the phylogenetic results in the discussion. Reading the section: “Systematic and taxonomic implications”, it seems that there is no congruence at all between taxonomy and the phylogenetic trees obtained. Instead, the major pattern shown in the figure is a monophyletic D. fascicola nested in a paraphyletic D. mediterranea. This pattern could be reflecting an anacladogenetic speciation process, which often renders an ancestral paraphyletic species. Several studies discuss this type of speciation and the need of accepting paraphyletic taxa (e.g. Hörandl, 2006, Taxon, 55: 564–570; Crawford, 2010, Taxon, 59(5), 1413–1423; Anacker & Strauss, 2014, Proc. R. Soc. B, 281, 20132980; Kuchta et al., 2018, Zoologica Scripta, 47(3), 285–299; Smith et al., 2018, Plant Systematics and Evolution, 304(4), 511–519). This hypothesis should be also considered and discussed by the authors, additionally to the already discussed hypotheses of a complex of cryptic species and a single polymorphic species.
Although it is true that there are a few individuals of both species that are nested with individuals of the other species, this is more an exception than the rule. A bit more discussion on this specimens should be conducted. Some of the possible lines of discussion are:
• Misidentification: as said in line 83 the two species are difficult to identify, have the identity of the “misplaced” individuals been rechecked? In this case it would be good to mention in to rule out the possibility of misidentification.
• Putative hybridization is vaguely introduced in lines 235-238, but it should be more developed. What kind of conflicts are the authors talking about? Were there intermediate individuals? Were they included in the molecular analyses?
• e.g.: ind M-Bany2 is placed with D. fascicola. In the same population the 2 species co-occur, and the rest of D. mediterranea individuals from Bany are far from M-Bany2. I would therefore suspect hybridization or misidentification in this case.
Although it is not necessary to speculate the reasons for every misplaced individual, some explanations are necessary. Furthermore, a short discussion on the possible source of incongruence between the two markers is also necessary. I appreciate the final remark of the section, indeed nrDNA and morphological analyses might be needed to clarify the conflict pointed out by the authors.
Some more specific comments are listed below:
Section “Phylogeography and diversification within D. fasciola – D. mediterranea complex”
Lines 256-257: or could not, take into account the uncertainty of dating. The HPD ranges approx. from 10Ma-4Ma in Tronholm et al., 2012.
Lines 256-265: the possibility of survival for seaweeds in the Mediterranean during the MSC has to be discussed, as it has been stated in the introduction that the most accepted hypothesis is no survival in the Mediterranean. The authors have to discuss how their results contradict this hypothesis and refer to other studies reaching similar conclusions.
Line 262-265 and 268-270: Although I admit that colonization of the Atlantic Ocean after the MSC seems feasible, remember 1) the uncertainty of dating in Tronholm et al. (2012) and 2) that your phylogeny is not dated and you cannot therefore infer when the colonization of the Atlantic occurred. The data shows clearly that it had to occur later in the diversification of the complex, but not exactly when.
In general, the manuscript is clear, well written and structured. However, I think there is an overuse of sentence connectors such as indeed, this way and in this context. The use of many connectors gives the perception of a slow pace and a bit distracting. I would recommend to use them only when it is necessary to emphasize an idea.
The references are sufficient to explain the problem to be addressed and provide a good background in the field.
The results obtained are relevant and addressed the objectives of the paper.
The aims of the paper are in general well defined, although the second one is a bit confusing (see PDF file attached).
The analyzes are sufficient for the purposes of this work. The images are clear and self-explanatory.
The methods are short but well described and referenced.
This paper helps on the understanding of the diversification processes in seaweeds, particularly Dictyota fasciola and D. mediterranea in the Mediterranean Sea. The results obtained are also intriguing due to what were considered two distinct species, the new evidence suggests a complex of species with rich genetic diversity. In addition, this work will contribute to understanding the diversification of species on the coast of the Mediterranean Sea and Eastern Atlantic.
Here I include some comments that must be clarified.
The species complex D. fasciola and D. mediterranea.
Tronholm et al. (2010) are cited as the main reference for the taxonomic status and phylogenetic relationships of the two species. At that time, there is no evidence of any species complex and including it in the introduction is bias.
The speciation of D. mediterranea.
Tronholm et al. (2010) are cited again to test the hypothesis of speciation, diversification, and invasion of these two species. However, the authors in that paper only speculate about possible scenarios given the available data. It is also speculated that the speciation of D. mediterranea from D. fasciola occurred within the Mediterranean Sea as D. mediterranea is not distributed in the Atlantic. This should be considered for the discussion.
I feel the discussion regarding the discovery of the species complex is short. The evidence provided by Tronholm et al. showing a clear-cut between both species of Dictyota seems convincing (many molecular markers and morphology). Is there any other reason other than sampling to explain such differences?
In general, the manuscript is clear and well written. However, I think there are some issues that must be addressed and clarified before publication (see report and PDF file attached). In addition, the captions for Fig. 3 is exactly the same as Fig S1. Please add further descriptions to differentiate them properly
I hope the comments on this work would help to improve the manuscript.
Best regards.
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