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Research Article

Ancient DNA Elucidates the Controversy about the Flightless Island Hens (Gallinula sp.) of Tristan da Cunha

  • Dick S. J. Groenenberg mail,

    groenenberg@naturalis.nl

    Affiliation: National Museum of Natural History Naturalis, Leiden, The Netherlands

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  • Albert J. Beintema,

    Affiliation: Biowrite, Gorssel, The Netherlands

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  • René W. R. J. Dekker,

    Affiliation: National Museum of Natural History Naturalis, Leiden, The Netherlands

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  • Edmund Gittenberger

    Affiliations: National Museum of Natural History Naturalis, Leiden, The Netherlands, Institute of Biology, Leiden University, Leiden, The Netherlands

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  • Published: March 19, 2008
  • DOI: 10.1371/journal.pone.0001835

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Referee Comments: Referee 2

Posted by PLoS_ONE_Group on 21 Mar 2008 at 17:23 GMT

Referee 2's Review:

In this manuscript, Groenenberg and colleagues provide genetic evidence that Gallinula nesiotis and Gallinula comeri - two flightless hens - have lived in allopatry without gene flow before the former became extinct (XIXth century). Consequently, current hen individuals found on the Tristan da Cunha island are not local descendants of G. nesiotis but rather G. comeri immigrants (encoming from the island of Gough). As only one G. nesiotis specimen has been ever described (and sampled in 1864), the authors took advantage of ancient DNA technics in order to get cytochrome b sequence data. There is nothing really new in such an approach since several authors have already published such analyses in other taxa years ago (see for instance among many others, Paxinos et al. 2002 Orlando et al. MPE 2003, their Mesomys hispidus work, or Austin et al. 2003, 2004). I therefore strongly suggest to not publish this manuscript in PLoS One but strongly encourage the authors to submit this in one of the top-level journal related with molecular evolution and phylogenetics such as Mol. Phyl. Evol. I point several points though because, according to me, they will have to be addressed whatever the journal.

* The authors do not provide any information relative to the storage conditions of the 1864 specimen (e.g. was it stored with other hen specimens ? if so, which species ?). Such information is important to state for the potential level of contamination before the DNA analysis.

* It is a good point that PCR amplicons were cloned and up to 15 clones were sequenced in order to get a consensus devoid of DNA-damage induced errors. However, after reading carefully the mat & met section, I still have no idea of the number of different amplicons (per target region) that have been used to generate each consensus sequence of the 1864 specimen. Hofreiter et al. (2001) point that unless a minimum number of 2 (or 3 if any ambiguity is still present), ancient sequences should be regarded with great caution. Therefore, the authors have no choice but stating the number of their different amplicons to state for the authenticity of the final sequence.

* The authors should emphacize for what reasons they consider the 1864 sequence is not a numt. Orlando et al. 2003 and Binladen et al. 2006 have shown good evidence that numt could be preferentially retrieved from samples dating back the the Pleistocene period (up to 70,000 years ago). Besides citing those papers, the authors should provide (1) more comments on the amino-acid sequence of the 1864 specimen (is there any weird amino-acid ? etc) and (2) supplemental evidence at the bench (for instance, taking advantage of the G. nesiotis sequence to generate specific PCR primers and try to get amplicons from G. comeri extracts; negative results would seriously strengthen the conclusion of the authors).

* I don't believe that finding a very divergent haplotype in a single individual (the 1864 specimen) is a guarantee that they were actually two taxonomic groups in place for the following reasons:
(1) other individuals on Tristan da Cunha could have carried G. comeri like haplotypes (ascertainment bias)
(2) the only 4 G. comeri individuals that have been analyzed at the DNA level exhibit 4 different haplotypes, suggesting that the G. comeri would have even be more diverse. It is therefore still possible that G. nesiotis related haplotypes were (or are) present in the G. comeri population. If true, this would provide evidence for gene flow. I strongly ask the authors to genotype more G. comeri individuals, especially those that lived at the same time as G. nesiotis (and that have not been analyzed at the DNA level so far).
(3) what about the nuclear genetic diversity ? This is never addressed in the manuscript though mtDNA is transmitted only over maternal lineages (for instance, what about possible male biased migrations from Gough to Tristan da Cunha?). Rapid Genbank queries reveraled that nuclear markers have already been sequenced in G. chloropus. They could possibly used to gather nuclear data from those specimen described on table 1.

* a broader bibliographic survey should be done in order to show how ancient DNA data could be used in order to reveal cryptic species or to provide clues for conservation (use some of the references pointed in my first paragraph).

* what about bootstraps in the NJ-tree ? They have to be computed.

* why showing a cladogram after Bayesian analyses ? I think that we need to see the branch length to make the people realize that G. nesiotis and G. comeri are actually about equally distant than G. chloropus orientalis and other G. chloropus are, suggesting that G. nesiotis and G. comeri are rather subspecies than true species.

• why not computing ML trees ? I suggest to do such analyses since they will allow the authors to test for different topologies such as the NJ-one, or one alternative where G. nesiotis would be placed inside the G. comeri clade.

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N.B. These are the comments made by the referee when reviewing an earlier version of this paper. Prior to publication the manuscript has been revised in light of these comments and to address other editorial requirements.