Ancient DNA Contradicts the Presence of Social Voles (Genus Microtus, Subgenus Sumeriomys) in the Late Pleistocene of Western Europe

Round 1

Reviewer 1 Report

This manuscript brings to the scientific debate the need to rely on genetic studies when identifying new taxa of micromammals, as the classical metric study of teeth is not enough.

The authors start from the hypothesis that, specifically, a new taxon defined in an Upper Pleistocene site in France is not a taxon at all, but rather some individuals with aberrant forms of dentition. The authors find, after an extensive review of the literature, that aberrant forms exist in many taxa, so that morphology alone cannot resolve taxonomy.

The experimental design for the genetic study is very complete, well explained, reproducible and adequate to test the hypothesis presented. I assume that in addition to depositing the sequences obtained in GenBank, the authors will provide supplementary material with the results of all the techniques used to validate the results of the genetic study.

The figures are sufficiently illustrative and easy to interpret.

The authors show full consistency between the hypothesis to be tested and the interpretation of the results obtained; they also advance logical explanations for the presence of these aberrant forms in certain populations of micromammals.

In general, the article represents an important advance in the taxonomy of fossil micromammals, pointing out the possibility of important errors when this taxonomy is based only on morphological traits. Indeed, one of the most interesting conclusions is that morphological variability in the dentition of micromammals of the same species may be greater than expected.

In summary, the paper is in my opinion relevant for publication, and I have only found three very minor details that in my opinion need to be corrected:

Lines 34-36

"The central and most specious genus of Arvicolinae is Microtus Schrank, 1798 with ca. 60 species when we narrowly define this taxon (excluding Lasiopodomys Lataste, 1887, Neodon  Horsfield, 1951 and Alexandromys Ognev, 1914) [1]."

When the authors say "we narrowly define this taxon...", do they mean that they are the ones who decide on this definition, or that it is the criterion followed by the authors of the quote [1]?

Lines 70-72

"We investigated teeth of various morphology of the anteroconid complex (ACC) and different degrees of development of BSA 4, BSA 5, LSA 5 and LSA6 as well as T6–T9 to preserve intraspecific morphological variation."

Please define the meaning of these acronyms, or better, explain that these anatomical landmarks are shown schematically in figure 1a.

Line 355

"flat occlusal surfaces with enamel cutting ages ..."

 Do you mean cutting edges?

Author Response

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Author Response File: Author Response.docx

Reviewer 2 Report

I was asked to review the manuscript by Nadachowski and colleagues submitted for publication to Diversity. In this work, the authors use ancient DNA (aDNA) analyses to debunk the identification of a separate species of vole of the genus Microtus from the Late Pleistocene French site of Petits Guinards (Creuzier-la-Vieux, Allier), previously preposed based on some “aberrant” specimens that exceed the morphological variability of the rest of the sample. Nadachowski and colleagues further put the emphasis on using aDNA for supporting taxonomic decisions.

I think that the emphasis put on the “molecular vs morphological data” is too stressed and that the taxonomic reassessment in itself does not represent a marked advancement. Indeed, the establishment of Microtus (Sumeriomys) bifrons by Jeannet and Fontana (2015) did not receive much attention until now, probably because the identification was not considered reliable even on a “traditional” morphological viewpoint. I suggest polishing this aspect, underlining that morphological and molecular data are actually complimentary tools that should be coupled whenever possible, and that identifying few morphological peculiar specimens within a large sample as a separate species is generally discouraged even in “traditional” morphologic studies.

Said that, the study represents an interesting contribution (also in the way it discusses of morphological variability!) worth consideration for publication in Diversity.

The language of the work is generally easy to understand but there are some typos, some issues with plurals-singulars, synonyms, punctuation, and sentences that are not grammatically correct… I would recommend a careful check prior to resubmitting the manuscript.

There are also extensive inconstancies in the references, I took ten random references and always found some mistake, being this either in punctuation, font style, abbreviations… This must be fixed.

Works reported as authorships (e.g., Microtus Schrank, 1798) should be included in the bibliography whenever possible.

I think it would be also better to call out author names when cited in sentences like “according to Smith [x]”, rather than “according to [x]”.

I think the formatting of lines 169-180 should be checked.

In sum, there are two points that are, in my opinion, important to revise. First, the emphasis put on the “molecular vs morphological data” (see previous comment). Second, the language, formatting, and style of the manuscript.

Author Response

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Author Response File: Author Response.docx

Reviewer 3 Report

This paper presents a nice example of ancient DNA contradicting paleontological inferences, and demonstrates that for the species examined, morphological variation in extinct lineages exceeds that of modern specimens.  The paper is simply and effectively written and the results are convincing.  The authors might address the points listed below to improve their manuscript.

1) line 31.  "still undergoing speciation" reads a bit oddly.  Aren't all lineages potentially prone to future speciation?  Or, do the authors mean that speciation in the group has happened over very recent history, or some other? 

2) line 34.  'speciose' instead of 'specious'?

3) line 97.  'tree'?

4) line 101.  Are there NUMT (nuclear copies of mitochondrial genes) in these rodent genomes?  Are there any stop codons or frameshifts apparent in any of the reads mapped to the mt protein coding genes? 

5) line 114.  What were the authors finding regarding DNA damage?  Were the results consistent with authentic ancient DNA, or if not, is some sort of contamination from recent DNA a possibility?

6) line 118.  Why infer phylogenetic placement by number of reads mapped to different species?  Shouldn't the consensus mt genome or particular reconstructed mt genes from the Pleistocene samples be placed by phylogenetic analyses in addition to the approach taken by the authors?  The only trees show relationships within single species.  Why not show larger trees with many species to clearly show that phylogenetic analysis, not just mapped reads, places the sequences within the species that the authors argue the ancient samples fit into?

7) line 368.  Change 'hypothesize' to 'hypothesized'?

8) I generally defer to other reviewers in assessing the appropriateness of ancient DNA methods and pipelines used in the paper.

Author Response

Please see the attachment.

Author Response File: Author Response.docx