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Good news - approval of your revision
Thanks & greetings
Michael Wink
AE
[# PeerJ Staff Note - this decision was reviewed and approved by Richard Schuster, a PeerJ Section Editor covering this Section #]
I thank the authors for their response. They have addressed all of my concerns.
no comment
no comment
All good.
The authors did overall a good job at taking into account my comments and I feel that the manuscript now present more correct and clear results. Despite this I still have the same concerns about the reliability of the MTML-msBayes, to be fair I'm pretty sure its wrong and the authors now acknowledge it even more clearly. I this context I can't really see the point of using this method which is not made for this kind of data and therefore gives problematic results.
Overall good except for the MTML-msBayes method
Overall mtDNA molecular and divergence time estimates are likely correct and usefull.
Please follow the recommendations carefully.
**PeerJ Staff Note**: Please ensure that all review, editorial, and staff comments are addressed in a response letter and that any edits or clarifications mentioned in the letter are also inserted into the revised manuscript where appropriate.
I appreciate the detailed reply and the track change version.
R2 response to question about looking at each mtDNA gene separately. While I agree they are linked, there are studies that show different patterns depending on which gene is used. Eg cyt b shows spp A and B are more closely related to each other than to spp C, but ND2 shows spp B and C are sister. I don’t understand their comment about most of the variation in mtDNA being non-coding. Do they mean most of the variation is in the control region or are they referring to the three genes they looked at all of which are coding?
I think regardless of the actual divergence dates, which the authors point out are depended on the rates used, the fact that many of them cluster together (Fig 2 nicely shows this) is interesting.
Minor
For L71-proper names, we can agree to disagree and put it down to style differences. Proper names are normally capitalized.
The other points, most of which were related to issues with tables and figures, have been addressed in the revision.
L78 kya instead of Kya
Table 1 Mya instead of mya (in the text you used Mya) and elsewhere in the text. Also mix of Mya and Myr and kya and kyr.
L414 I respectfully disagree with the statement about Sanger sequencing. It is ‘low’ coverage in that it looks at a single DNA sequence, but it is not low coverage in terms of how many DNA fragments are included in a single sequence read. The error rates for Sanger sequencing are a lot lower than for next gen sequencing methods (which you mention). You also have the advantage with Sanger sequencing of being able to literally read the sequences to check for errors in base calling which you don’t have with next gen sequencing. Also next gen sequencing produces lots of reads, but for multiple loci, such that reads per DNA fragment are going to be lower than for Sanger sequencing and next gen sequencing has much higher error rates. The benefit of next gen sequencing is you are looking at thousands of loci. Here you had an average of 101x coverage.
Fig 3 may need to be edited to make the font larger. I know there is a lot going on in that figure, but you need to be able to read the species names. Zoomed in at 200%, I could read them.
no comment
see comments in basic reporting
As you can see, your MS has been thoroughly checked by our reviewers. Please try to address all their suggestions as these reviewers will see your revision again.
Kind Regards
Michael Wink
Academic editor
This manuscript is written well. It uses professional standard language in a clear way - I have a few suggestions to make it easier to read that are detailed below.
One main area for improvement is in the figures. Because many readers will look at the figures first and even primarily, they should be arranged and labeled in a way that makes them understandable as stand-alone images. In this case, I encourage you to use a standard, accessible color scheme that is the same across all figures. This will reduce the reader's cognitive load and make the figures comparable. (more detail below) Figures also take up a lot of space in a paper, so they should provide a high level of detail that is best understood visually. In the case of the map, all areas that are discussed as important in the manuscript should be in the map.
The methods are sufficiently described and appropriate to obtain the results needed to address the proposed hypotheses. The dataset is quite large in terms of base pairs sequenced and taxa included. The taxa cover a wide breadth of avian biodiversity. It is not clear how the taxonomic selection compares to the total diversity of species with distributions across Beringia.
The research questions are explained well/simply and are interesting. The study addresses a known knowledge gap, however there is little discussion of insights gained from other studies of glacial cycles on avian divergence.
This study uses vouchered museum specimens, a rigorous practice that is important for validation and raises the quality and impact of the study.
The findings are valid with robust analyses. Some more explanation or evaluation of the influence of sequence selection and coverage depth would be helpful (more detail provided below).
Fig 1 – It would help the readers if the major features were all labeled directly on the map, such as labeling the “Arctic Ocean” and the “Kamchatka Peninsula”. The Mackenzie River as the eastern border is potentially confused with the Yukon River. Shifting that label even higher and/or adding an arrow to clearly distinguish these two rivers would make it clearer. You mention the Bering and Chukchi seas later in the manuscript. It would be helpful to have these features on the figure as well.
Please also explain the red and blue color significance in the legend here – it is helpful to the reader that this color is a significant distinguisher between the land masses that remains constant throughout other figures. The exact same colors should be used within and between figures. Did you check that it is an accessible color difference?
Abstract
Line 35-36 – can you also add in the number of recognized species addressed here? While I normally wouldn’t repeat information in an abstract, this seems like an important place to provide a full list.
Introduction
While this section should give a broad overview of existing knowledge, this section is currently a little too broad to someone not familiar with this study system. Here are some suggestions for increasing clarity and making this more useful to a broader group of biologists.
Lines 67-69 –what can be gleaned from the lower latitude studies about the influence of glacial cycles? How do you expect this study to be the same or different?
Line 78 – explain what you mean by smaller-scale studies. Fewer species or orders? Fewer samples? Fewer base pairs? And what did they find? Explaining their results will help provide necessary context for the hypotheses you propose below.
Lines 84-86 – do you mean that some of these pairs are only on one side of the contact zone? As in, some are continental old world species with a nearby old world northern endemic? If not, can you clarify this wording a little? The phrasing “within Beringia” is throwing off my read here. I think you are contrasting that with the populations described on line 81 of sister clades on opposite continents but it isn’t totally clear. Using parallel sentence structure could make that meaning easier to access. For example, phrasing something like this could help: Some sister lineages are separated in Beringia by being on different continents, while others are on the same continent but separated by…a river? Or while others are on the same continent but one population is distributed broadly across the continent while the other has a smaller endemic distribution.
Line 83 – Can you be more specific when you say “variable levels of intergradation and divergence.” What does this variation look like? How extensive is it? How does it compare to other study systems?
Methods
Lines 105.. – Given that museum specimen collections are known to be biased, how does this taxonomic selection compare to the avian biodiversity present in Beringia? What orders, families, genera are represented in the study compared to what exists in the wild? What types of bias are present? How would that influence interpretation of your results?
It would help to have a supplemental figure with distribution maps of the species pairs.
108-109 – include the sample size for old world vs. new world vs. holarctic
Line 132-133 Remove the hard return here so it removes the separate one-sentence paragraph.
Line 182-183 please provide more detail on how the base divergence rate was adjusted for non-passerine orders.
Line 233 - could you revise the word order to not start with a printed number, such as “Pairwise comparisons were made between 11 species, 12 subspecies, and 16 populations (Table 1)."
Table 2 – Could you show which results are significant different from each other with a superscript of A for pairs that are sig. different and B for those that aren’t? This was stated in the text, but would be helpful to have explicit in the table as well.
Tables 2 & 3 – could you align the columns so there is not a separate line just for the word mitogenome (maybe abbreviate to mtgenome)? This would make the full genome and ND2 sections visually matched for easier comparison. Otherwise, it gives more weight to the mitogenome data and makes the ND2 data look like a footer.
Fig 2 – Please make the blue and red used here the same as in Fig 1. Histrionicus histrionicus seems to be a new shade of blue while the other Eurasian taxa are in a greenish color. Please standardize the size of the font for each taxon. I appreciated how most taxa were lined up with blue/green on the left and red on the right so I could compare across taxa somewhat. Please flip diagrams for species that aren’t in that orientation (e.g. Corvus corax, Pica spp.). The seemingly random variation in line length between hatch-marks made comparisons more difficult. A standard scale would make it easier to compare across taxon pairs. Are the taxa ordered taxonomically? Putting the species-level comparisons in a box together and population-level and species-level comparisons in their own box would make it easier to understand the differences in divergence across taxonomic levels.
Fig 3 – What are the red triangles?
Fig 4 – Replace “that” with “than” in the legend:“for a single vicariance event that the ND2 subset. “
Discussion
Line 330”recently” should be “recent”
While it is known that illumina provides higher coverage than 454 and this dataset does have a high average coverage, 11 taxa didn’t have coverage over 20x. Luo et al (2012) found that 20x coverage was needed to reduce errors that could lead to erroneously higher levels of divergence. Given that Luo et al. included nuclear DNA which has 2 alleles versus a single expected mitogenome, lower levels of coverage on either platform closer to 10x could be sufficient to reduce errors. How does sequence coverage impact the results in this dataset? Is there evidence that lower coverage resulted in lower diversity?
Luo et al. also found that low G-C content areas tend to have higher error rates with 454 sequencing but this study and Lerner et al. 2011 both used avian mitogenomes that have notably high G-C content. This could reduce the 454 error rate and the impact of different sequencing technologies.
Did you consider using intergenic regions or 3rd-codon positions for taxa with recent divergences or coding 3rd codon positions as purines/pyrmidines (RY coding) to reduce the influence of substitution saturation in older divergences?
The study used mtDNA to examine divergence in Beringia birds at either population, subspecies or species level using mtDNA dataset. The authors used ND2 gene for most analyses, but for a subset of comparisons used the 3 gene (COI, ND2 and cytb) or complete mt genome (19/39 comparisons). Fig 3 is an excellent summary of the results (though there is no information in the tables as to what numbers correspond to what taxonomic comparison). I am not sure if I’d expect divergence times to occur in discreate bursts as when populations are isolated and when genes show divergence won’t be coupled as the later is dependent on gene flow and drift and driven by population size as well as time.
My main problem with the manuscript in its current form is inconsistencies in numbers, tables and figures and finding the data to back up some of the statements. Eg the authors state divergence in Aythy marila occurred 629 kya (L340) and refer to table 1 (Table 1 has a list of sample sizes and what comparisons were done), yes fig 3 clearly shows that divergence (red circle #7) at well over 1 mya.
I would also like to see a better review of the published literature, as I mention below there are at least three review type articles on avian divergence in the Pleistocene and none are cited, as well as a few sentences on what causes divergence. There is separation of populations and cessation of gene flow, but how that corresponds to divergence times is a balance between gene flow and genetic drift and also depends on population sizes.
I have included more detailed comments at the end (under additional comments).
Impressive diversity of species and samples. How were species chosen for species level comparisons? Ie simply the fact that they are the same genus and species are on either side of the Bering Sea or are they sister species split by the Bering Sea?
For sequences, was there any filtering done to remove low quality reads? It says low quality bases were removed, but not what criteria was used (eg phred score <30).
You generated sequences for three mtDNA genes (ND2, cytB and COI). Why only use ND2 for the trees/networks, etc? You mention the fact that all three genes are linked, but do they show the same patterns? We know different mtDNA genes can be under selection.
It will be a nice addition to the literature, but you leave out a few key references and as currently written the data required to reach the same conclusions as the authors are missing in places or don’t match what is in the text. As mentioned in the basic reporting section, parts of the manuscript are hard to follow as the wrong table or figure are cited or the data aren’t presented such that the reader has to trust that what you are saying is correct rather than looking at the numbers (ie divergence times-you report divergence rates in a table, but don’t convert that to dates, but the dates are what you refer to).
Comments:
L65 missing key references. There were three papers published on this about 20 years ago. Lovette (2005, TREE) discusses all three in detail (Weir and Schulter, Johnson and Cicero and Klicka and Zink). There are also other review style papers (non-bird ones) that also talk about the importance of glaciations (Shafer et al 2010 Mol Ecol) from a North American perspective.
Minor
L64 I’d change to Populations have the …while separated. Otherwise ‘separated populations’ and ‘apart’ are redundant
L71 ‘Rivers’ capitalized as proper name (same as you’ve done for ‘Sea’ and ‘Peninsula’), similar comment L82 (‘Seas’) and elsewhere.
L111 I count 12 subspecies and 16 population level comparisons on Table 1, not 11 and 17 respectively. Later on L234 you say 12 subspecies and 16 population pairs as well.
Table S1 has details for 422 samples not the full 437 mentioned in the paper.
L231 says 38 lineages, elsewhere says 39.
L239 Check numbers in text vs those in table 2 as they don’t match. Eg species pairs avg JC divergence in text is 2.44 +/- 1.01, but in table 2.44 +/- 1.05, same with populations and subspecies. Also if reported in the text, do you need the table? Table does have min and max, but otherwise data are repeated in text.
L244 check numbers in text vs table. For full mitogenome looking at min and max divergence times in table 2, the smallest is 29,000 (not 20,000) and largest is 2.12 mya (not 1.4 mya); table s5 doesn’t have divergence dates, it has corrected mutation rates. L248 overall average for ND2 in table is 586,000, text says 582,400.
L253 Hochberg (correct in lit cited, but not in text)
L298 refer to fig 3, not fig 2 as fig 2 is the individual networks and doesn’t have divergence dates. Fig 3 does show most population divergence was recent, but there are more than two points with dates larger than 250 ky. If you use 1 my or 700 ky, I’d agree that there are only two that are older.
L330 more recent than…
L335 Fig 2 and table 1 don’t contain the data you are referring to. Fig 3 does. For table 1, you could easily add the divergence time as another column and it is a good spot to include it.
L344 I’m not sure where you are getting this from? If I look at fig 3 (not fig 2 because it doesn’t have dates), I see quite a few before 1.8 mya. Even if I only look at one level (eg spp), there are divergence dates before 1.8 mya.
L363 Illumina will have a higher error rate than Sanger (cite reference), is there a way to account for this-eg only look at parsimony informative sites, thereby removing any variable sites that are only found in a single individual.
Table 1 While the definition for OW states they are Eurasian species, for NW it simply says they were sampled in North America-are NW species/subspecies/populations defined as only being present in the NW (aside from the odd individual that got blown off course)?
Fig 2 hard to see blue colour. Not the same shade as in fig 1 where it stands out.
Fig 3 caption refers to table s5 for taxon pairs, but they are not mentioned in table S5. What are the red triangles? Average dates for each level? The bimodality of the subspecies divergence is really interesting (ie <1 my or 2-3 my).
Fig 5 why not add the colours for populations, subspecies and species comparisons?
I didn’t check the references, but some scientific names need to be italicized.
First round of review of the paper intitled Mitogenomes reveal the timing and distribution of divergence events among trans-Beringian birds (#100524) by Collier et al.
The Beringia is a biogegraphic region that have been shown to be important in the divergence and the speciation of numerous taxa, notably of birds, due to its successive opening and closing during Pleistocene glacial and inter glacial period alternance. The authors aimed at estimating the timing of divergence between multiple bird taxa pairs from various taxonomic levels distributed on each side of the Bering strait. Furthermore the authors aimed at identifying potential burst of divergence events during potentially more favourable periods of the Pleistocene. To do so the authors gathered a very large and comprehensive datatset of sample from museum collections and produced a large full mitochondrial genome sequence dataset using NGS methods. Even if the asked quetion are of broad interest and the study sampling is well made I have numerous majors concerns which need to be adressed before this paper could be considered suitable for publication.
Major issues are given in subsequent parts
More minor comments :
L57 : « avian speciation is considered to be primarily due to selection (Price 2008). » : Selection is very vague (natural ? sexual ?), this sentence should be claryfied.
L87 : Consider rewording, maybe « This study adresses two major questions about the Beringian system… »
L123-128 : These sentences are not really clear to me, the libraries were prepared two times in different labs and then pooled, if yes, why ? if not it needs to be clarified.
L134 and then L140-142 : The authors obtained published references MT genomes for each pairs (of the species or of closely related species) but the separation of these sentences make it difficult to understand, consider uniting the sentences and rewriting.
L 150-154 : The authors produced full MT genomes but then decided to trim them into gene sequences, this approach could be questionned and should therefore be justified here.
L162-166 : The Jukes and Cantor genetic distance is quite outdated now and was not designed to take into account now well known limitation of genetic distances (saturation ; translation – transition ratios ; etc.). I would really like to see the same analysis but using more up to date and reliable genetic distance model and with the search of the best-fitting substitution model (Mega-X offers this option) for each dataset (one per taxa pair). This would not preclude the comparision with previously published work as J-C based analysis have already been done.
L171-173 : This analysis is interresting but is higly sensitive to the followed taxonomy and therefore needs to be clearly explained and taken into acount (see above in major issues).
L180-183 : Such adaptation of previously published substitution rates is important but could also largely influence estimated divergence times and should therefore be more deeply explained. Consider also reading/using the results published by Nabholz et al. (2016 ; Molecular Ecology).
L198-199 : As the auhors are working on mtDNA wich is basically an unique non recombining locus I can’t see how gene flow could be invocked like this here. The authors should better call it haplotype sharing due to either introgression, incomplete lineage sorting or very recent divergence. This part needs clarification.
L 204-207 : The authors need to explain/clarify the rationale to subsample their complete MTgenomes to only three genes and their choice of those 3 genes.
L 208-215 : As this method and its parameters could be new/unclear to many readers the authors should better explain the way the work, what the parameters mean, how they chosed their prior values and the influence of these prior choices.
L 221-225 : The allowed migratory rates and ancestral population sizes priors can have strong influences on this kind of analysis’ results and the authors must therefore explain more clearly their prior’s choices and their meaning.
L 239-240 : « but not subspecies pairs (1.36 + 0.93; p = 0.19). » this could be linked with unapropriate taxonomic choices. Could be tested with other taxonomic choice but needs at least to be discussed in a « limitation of the study » paragraph.
L 244-250 : Table S5 is cited but does not contain this information. The authors write « ranged from 20,000 years to 1.4 Mya » but the some divergences are dated up to 4 Mya in Figure 3 ! This needs to be fixed/clarified. Figure 2 is cited but this figure shows haplotype networks not divergence times.
L 249-254 : This is dependent of taxonomy and needs to be corrected if taxonomy is changed.
L 255-268 : Quite difficult to understand consider rewriting. Explain what you mean about gene flow (Haplotype sharing ?). Figure 3 is cited but Figure 2 should be cited. Doniol-Valcroze et al. 2023 should be cited as prior work showing strong divergence patterns.
L 298 : Wrong Figure citation.
L 302-303 : Should be corrected here and in the rest of the paper (L 343-351, there it would completly change the paragraph) as the divergence times in Figure 3 are comprised between 0 and 4Mya therefore spanning Pleistocene (2.58 - 0.011Mya) and a large part of Pliocene (5.33 - 2.58Mya).
L 326-332 : This paragraph is quite misleading and largely depends on the followed taxonomy (as said above). Don't the author think that taxonomic level is largely based on divergence depth? As you explain that time in allopatry and therefore divergence strengthen reproductive isolation and as species are defined by reproductive isolation levels (Biological Species Concept of Mayr, 1942).
L 333-337 : Wrong Table and wrong Figure cited. Can’t see any cluster between 1.3 and 1.6Mya, in fact it is quite an empty period, consider correcting/rewriting.
L340-L342 : « the only population-level comparison outside of this cluster (Aythya marila, ~629 Kyr; Table 1) » what about Uria lomvia (pair 23) which is estimated to diverge about 2Mya ago!
L 352-358 : The quality difference between Sanger and Illumina sequencing should be strongly mitigated as Sanger sequencing is known to have very high accuracy (>99%) like Illumina (Shendure & Ji 2008 Nature Biotechnology).
L 358-354 : The analysis of the Sanger sequencing data and its comparison with Illulmina results is not properly mentionned in the Methods and Results parts were its needed for reproductibilty.
L 365-372 : I can see how inadequate calibrations could impact the estimated divergence times but there is plenty of literature and ways to correct it or find a more appropriate one, the authors could try other calibrations to try to resolve this. If already done as suggested by the next paragraph then there is no point to these complex explanations. On the other hand I can’t see how using calibrations designed on Sanger sequenced mtDNA can produce divergence time estimation errors when applied to NGS sequenced mtDNA as the sequenced DNA is the same. Please explain your rationale or delete.
L 385-396 : Due to the problematic use of MTML-msBayes the authors struggle to explain their results which are in fact probably wrong, I suggest to rewrite this paragraph following the choice to rerun correctly the method or to delete its use from the paper.
L399-408 : Needs to be claryfied/rewriten/mitigated in light of comments above.
Table 1 : The very high number of suplemmentary tables, some of which are redundant with the table S1 and the presence of very important information in suplemmentary materials make the understanding of the paper very difficult. I urge the authors to rethink those tables to help the reader. I would recommend the authors to display Taxon number | Taxon | Taxonomic depth | Total samples (OW samples/samples) | % Full MTgenome J-C distances/% ND2 J-C distances | Full MTgenome DA/ND2 DA | Taxonomy account (needed if other potential taxonomic treating exist : e.g. other consideration by checklists ; previously published work suggesting split) in Table 1. Example/suggestion of « Taxonomy account » for A. rubescens : « proposed to be treated as separate species by Doniol-Valcroze et al. 2023 (Zootaxa), folowed by Clement’s checklist ».
Tables 2 & 3 : Those tables with the same structure should be merged to avoid having to many tables with redundant columns.
Figure 1 : Could be usefull to add a panel with the ice cap extent during glacial periods (maybe maximal) as it also have really important biogeographic consequences as much as land bridge formation.
Figure 2 : Check citation in the text (often inverted with Figure 3). Text size and resolution are way to small to allow the reader to understand the figure and the patterns. Taxon pair numbers (1-39) need to figure next to the taxon pair names to help the understanding. Size of circles should also be changed to help the reader.
Figure 3 : Check citation in the text (often inverted with Figure 2). Relying on taxon pair number makes it difficult for the reader to undertsand, having these numbers on Table 1 will help but the authors should consider finding a way to display taxon pair names somewhere on the figure. The meaning of the traingles (mean per taxonomic depth I suppose) are not explained in the legend.
Figures 4 & 5 : keep only if the analysis are maintained and could be send to suplemmentary material otherwise.
Taxonomy
The authors cite the IOC taxonomic list (L56 ; by the way IOC recognise > 11 000 species and its correct citation should be « Gill F, D Donsker & P Rasmussen (Eds). 2024. IOC World Bird List (v14.1). doi : 10.14344/IOC.ML.14.1. ») but then state that they follow the AOS (2023) taxonomy (L112). As those two taxonomic lists have different criteria they do not support the same taxonomy and its especially relevant for some of the analysed taxa (e.g Numenius phaeopus – N. hudsonicus ; Anas creca – Anas carolinensis ; Larus vegae – Larus smithsonianus ; Larus canus – L. brachyrhynchus are considered as separate species by the IOC but not by the AOS) and could therefore impact the results of the study and their interpretation. The athors should therefore clearly state which list they follow and why. I would recommend following the IOC as it is the more up to date and largely followed list but the authors could have other reasons to follow another list (e.g. Clement’s cheklist which is the one used by the largely used eBird platform but also differ in species list e.g. split of Anthus rubescens – A. japonicus following Doniol-Valcroze et al. 2023 Zootaxa). In any case the authors should at least cite and maybe briefly discuss the taxa pair they analyse and for which different checklist have different taxonomic levels (Whimbrels ; Teals ; Gulls ; Pipits ; etc.).
Sequencing strategy
The authors gathered a considerable sample of numerous taxa pairs and used recent NGS techniques to obtain high depht sequence data. They made the choice to analyse complete mitogenomes to estimate divergence times between the analysed taxa pairs to anwser the questions of their study. Mitochondrial DNA is now know for a while to have strong limitations for this kind of sudies (maternal inheritance, no recombination, mutational saturation, potential for haplotype capture and replacement). Using the same sampling and sequencing effort but targeting nuclear DNA (e.g. sequencing of UCEs ; RADsequencing) would have allowed more reliable divergence estimates but also alowed estimations of past/present gene flow and strenght of reproductive isolation between the taxa pairs. The authors should therefore clearly justify their choices about sequencing strategy as well as clearly explain the limitation of it.
MTML-msBayes analyses
The authors used the previously published MTML-msBayes pipeline which is suposed to use genetic data to estimate the number, the timing and the temporal distribution of main divergence event accross all the considered taxa pairs. The authors themselves strongly doubt about the results of this analysis (L 277-280 ; 281-288 ; 304-323 ; 385-396) and I also think that its results are very dubtfull given the estimated divergence ranges and their distributions. I can’t trust that the divergence event between Histrionicus histrionicus populations (virtually 0y) and between Tringa brevipes / T. incana (nearly 4Mya) happened during one unique divergence event between each sides of Beringia. I think that either there is something wrong with the use of the methode either their data does not match the requirement for such method but in any case this analysis is problematic (the authors already recognise it in L 304-323). I recommend that the authors rerun their analysis trying to fix this problem and/or get in touch with the authors of these methods (Huang et al. 2011 ; Overcast et al. 2017) to solve these issues. If the results are still biologically that inconsitent I strongly suggest removing this analysis, as almost suggested by the authors L 304-323, which gives wrong conclusions and complicate the output and the understanding of the study.
Incoherences
My reading of this paper was largely impacted by numerous incoherences between the text, the figures and the suplementary material. Here are a few that I managed to understand and pinpoint but I suspect that many more exist and urge the authors to very carrefully check their manuscript to fix them :
- The first sample of Phylloscopus borealis kennicotti (UAM 34615 in the Table S1 and in the Alaskan Museum) I checked because of the very high divergence time estimates is labelled as a captive individual of Polyplectron napoleonensis (a South-East Asian Phasanidae !!!!) in the ARCTOS Collection Database. This issue and the potential other ones extremly concerning and could really cause the surpising results of the study on the P. b. borealis – P. b. kennicotti pair if its really a Phasanidae sample which was sequenced. This issue raises caution about the rest of the samples which I of course did not checked, this is very problematic.
- Figure and supplementary material labelling is very skewed as Figure 2 and 3 are inverted all over the text as well as numerous Supplementary files. The authors must carrefully check the figure labelling, numbering and citing in the text.
Discussion of divergence times
I would also like the authors to add a discussion paragraph which discuss about their finding about divergence times between taxa pairs in regard to subjects like previous findings/publications, taxonomy debates (see above for species that are not treated the same by different checklists, the authors should check for other ones that I may have forgot to pinpoint), discuss very surprisingly strong (e.g. P. b. borealis – P. b. kennicotti which were find to not diverge at all by Alström et al. 2011, Ibis) or weak (e.g. Plectrophenax nivalis / P. hyperboreus) divergence times of some taxa pairs and last, open the way to future studies which could try to decipher the evolutionnary history and taxonomic status of such taxa pairs.
See major comment on experimental design
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