A genomic perspective is needed for the re-evaluation of species boundaries, evolutionary trajectories and conservation strategies for the Galápagos giant tortoises

Dear Dr. Loire and Galtier,

We have received two thoughtful reviews of your pre-print manuscript entitled "Preserving microsatellites? Conservation genetics of the giant Galápagos tortoise." Both reviewers agree that this is a valuable and interesting letter which raise important points and issues regarding the ongoing conservation practices of the Galapagos Giant tortoises based in insufficient genetic data. However, both reviewers also raised important issues and reserves regarding the current version. Both reviewers felt that the authors should do a better job at explaining the context, the actual issues, and limitations of previous studies. Furthermore the results provided in this current version as an attempt to illustrate the poor representativeness of a dozen of loci to delineate the genetic structure and taxonomic delimitation are based on another data set which also raise a lot of questions. The two reviewers have made extensive recommendations which could greatly improve the current version and I encourage the authors to address them carefully in revised version in order to be consider for a recommendation by PCI Evol Biol.

Thanks for this. Please find below our detailed, point-by-point response to the reviewers' comments.

Very briefly:

• we agree with many of the suggestions regarding the presentation of our work, which we have substantially amended; in particular, we clarify that we are not criticizing the usage of microsatellite loci, but rather of an insufficient number of loci;

• we give more details about ancient and recent conservation initiatives in C. nigra, the influence of published genetic data analyses, and our suggestions for improvement;

• we discuss in more detail the controversy between various sources of data, existing biases in published analyses, and the potential and limitations of our approach regarding substructure detection and species delineation; we now refer to the Roux et al (2016 PLoS Biol) study, which was yet unpublished when we first submitted this manuscript;

• we have updated estimates of piS and F thanks to a recent improvement of our SNP-calling algorithm (Ballenghien et al 2017 BMC Biol) accounting for cross-contamination and similar sources of noise in read counts.

Reviewed by anonymous reviewer, 2017-04-13

This paper serves to highlight the previous transcriptome work of the authors (Lore et al 2013) demonstrating that there is low genetic diversity in Galapagos tortoises and make comment on the current conservation management based primarily microsatellite data. The authors have re-used transcriptome data from 5 wild caught individual zoo animals (Lore et al 2013) who’s collection data was not known but genetically assigned to 3 species/subspecies (Russello et al. 2010). They reconfirm they have found very low level of genetic diversity and the taxonomy of the group needs to be addressed. They compare the diversity within Galapagos tortoises to a range of other species diversity and finally compare the difference to a pair-wise comparison of transcriptome data from across the tree of life. They question the usefulness of the current management plan for Galapagos turtles based on microsatellite diversity.

I found this article thought provoking based on an interesting group, however found the discussion of the taxonomy, current management plan and evidence of natural hybridization in the system requires more work, the limited data and the conclusions drawn overreach the evidence as currently presented.

Thanks for this comment. Please note that our "conclusion" is mainly a message of prudence and a call for more data to be generated, given the conflicts that exist between currently available data sets.

Comments: There is a general lack of background regarding the taxonomy of the Galapagos turtles. The recognition of separate species or interbreeding subspecies is at the heart of the authors argument. More therefore could be written regarding the taxonomic status as currently recognised Whether the taxa are species or subspecies does not affect their need for conservation. However, their ability to hybridize and whether or not that should or shouldn't be prevented when populations are so small is what is the issue is here. The management program I am assuming from the authors summary removes “hybrids” from the breeding pool; with the assumption, that hybridization is due to anthropogenic interference rather than natural causes. (This needs more references to demonstrate this is what is happening).

However, lineage fusion is also being argued for the diversity found in C. becki (Garrick et al 2014). C. becki one of the 3 species chosen in their sample, seems to be well established as a taxon that has mixed ancestry (e.g. (Poulakakis et al. 2012)). 50% of the sampled individuals have mixed ancestry (Garrick et al. 2012). Only 29% of the PBL population were found to be pure-bred individuals (Garrick et al. 2014), but crucially in support of the authors argument lineage fusion is thought to predate human mediated translocations. More should be written about this species to support the authors’ view point.

Good point. We added a sentence highlighting the commonness of hybrids in the field (l 86).

The heart of this paper is based on the provenance of the 5 samples and the robustness of their assignment to different species/subspecies tortoise. I recommend these data be presented in a table in the supplementaries. There seems to be conflicting results for species assignment using microsatellite data for 3 of the 5 samples between studies (Russello et al. 2007; Russello et al 2010). Russello et al. (2007) states the differences between MtDNA and microsat assignment for these samples is due to them having mixed ancestry, the different methods also assign them differently. After adding data from a new population, he reports different assignment again for the same samples, with lower q (Russello et al. 2010). Could the authors add a sentence or two, to assure provenance. ZUZ10/ZUZ20 are reported as mixed up when the authors sequenced their transcriptome and assigned them GA05H and GA05G in the original transcriptome paper (Lore et al 2013). It is therefore not clear which microsatellite data belongs to which transcriptome. The same samples that were assigned to PBL in 2007 but were assigned to different populations in 2010, both were thought to mixed ancestry. All 4 samples had q-values below 0.79, there seems to be no data on the 5th sample.

Can the authors comment on these samples population assignment. Is it unclear? 1. Can you provide evidence that the samples are not from mixed ancestry? The micosats suggest all 4 samples are. And if they are, comment on how that would affect your conclusions about panmixa? 2. The fifth sample added to the data set in 2013, has a MtDNA assignment but I could not find a microsatellite profile for comparison. 3. Does mixed ancestry explain the genetic differences found for GAO5H mentioned in the text? 4. Do the authors have evidence that the microsatellites are not robust at identifying populations with confidence? It would strengthen the authors point.

The reviewer considers an interesting possibility, which is that there would actually be substantial population structure in C. nigra, but that our sample would not reflect it because it would by chance consist in individuals of "mixed ancestry". We, of course, cannot formally reject this hypothesis. Still, please note that the total amount of nuclear genetic diversity we detect in this sample is extremely low, compared to typical multi-species samples. The reviewer's hypothesis would imply that (i) the distinct C. nigra entities have diverged by no more than ~0.1% genome-wide, and (ii) hybridization is so common that hybrids dominate in our random sample.

Again, we perfectly agree that this sample of size 5 is not sufficient, far from it. It is just a demonstration that more data are needed before making drastic management decisions, since the first genome-wide data set gathered in this species contradicts the hypotheses on which management policy gas been based so far. We modified the text in several places to account for this comment, explicitly stating that our sample is insufficient to provide a definitive answer on population structure in C. nigra (l 138-139).

Coding data is usually constrained and this will not necessarily reflect the historical process. The authors have a clear expectation that the coding proteins would be divergent and demonstrate measures of selection, and write as if surprised by these low Fit levels, despite the many other papers demonstrating low nuclear divergence in the turtles (e.g. (Burns et al. 2003)).

Speciation can be driven by small areas in the genomic landscape and not observed by a statistical average across all variation (Fit). The genetic differences between the pied and collared flycatcher for example closely related species but still able to hybridize, were found to be small, restricted to a small part of the overall genome that control the production of gender cells, chromosome structures, rather than gene adaptation (Ellegren et al. 2012). It may not be until speciation is further along in the evolutionary process that divergence will be evidenced in the proteome. The lack of diversity may therefore be because it is transcriptome data rather than genomes-scans.

We fully agree: the level of population differentiation is expected to vary between regions of the genome, as observed in many published data sets. This is exactly why we argue that a dozen of loci is not a sufficient sample. This rationale is at the heart of our recent Roux et al (2016 PLoS Biol), in which we show that accounting for among-loci heterogeneity in gene flow is required for reliable species delineation and inference of population history. The Roux et al (2016 PLoS Biol) paper is mainly based on transcriptomes, similar to the data set discussed in the current manuscript. We agree that genome-wide data would be even more informative, and indeed urge C. nigra population geneticists to move to the genome scale. We now cite Roux et al (2016 PLoS Biol) as an additional demonstration of the need for genome-scale data in population/conservation genetics.

The authors argue that tortoises have not accumulated diversity of well-established species, and compare it to a range of pair-wise species comparisons, some of which are highly divergent, which has the effect of inflating this point. The pair wise comparison of (Microtus arvalis + Microtus glareolus); these actually represent two different genera; “glareolus” is Myodes glareolus (the European common bank vole).

I find the gap in the graph between the single species and pair wise data needs a little bit further explanation. Could sampling pairs that are incipient species fill this gap?

Transcriptomes of other relatively young radiating species, maybe a more relevant comparison to include; e.g. cichlids (Brawand et al. 2014), rather than different subgenera of hares. If Fit is greater in young divergent taxa (which it is for cichlids) this would add more support to your conclusion. Or comparisons with Darwin’s Finches?

In this manuscript we do not aim at sampling the continuum of divergence. Our goal is rather to illustrate that (1) C. nigra harbours less genetic diversity and population structure than many species of animals that nobody would think of splitting, and (2) the typical level of population structure in multi-species samples is much higher than the one we observe in C. nigra. To make this rationale, we need a random sample of species and species pairs. This is why we used the Romiguier et al (2014 Nature) and Galtier (2016 PLoS Genet) data sets, which have been gathered independently of population structure and species delineation issues.

Adding taxa that are intermediate between the "one species" and "several species" status, such as cichlids and Darwin's finches, would be very interesting in principle – this is the idea of the Roux et al (2016 PLoS Biol) paper – but would not add much to the argument that C. nigra clearly falls in the "one species" side. One strength of this data set, furthermore, is homogeneity of data type and data analysis pipeline (Gayral et al 2013 PLoS Genet, Ballenghien et al 2017 BMC Biol). Adding data from other studies would make the comparison less clear-cut. The M. arvalis/M. glareolus twospecies sample was removed from the analysis.

Management implications: If a view is taken that the turtles represent 1 species and multiple subspecies, should their present management plan be changed? The authors, I am sure would not want to retain unnatural crosses brought about by translocation in a system. Apart from stopping the current inbreeding and sterilization program, the authors have not offered an alternative management plan, and their opinion is not based on data that is expansive (taxon sampling) or conclusive (genomic wide sampling). Putting this in context with the C. becki “natural” fusion would help strengthen the arguments to leave populations alone (if that is their view).

Does it automatically follow that we should assume the populations are not in a process of separation and therefore manage them as a single population based on a single Fit measure ?

We are not saying that, or have strong recommendation at this stage. Rather, we suggest that part of the money devoted to conservation in this taxon should be used to generate genome-wide data in a large sample of Galapagos tortoises and access to the relevant information, rather than pay for transportation of animals by helicopter in order to recreate genotypes that have no demonstrated value, or species that have no demonstrated existence. We make this suggestion even more explicit in the last paragraph of the revised version, which was fully rewritten.

The group clearly appears to be a species undergoing radiation, with mtDNA and microsatellites showing structuring that is significant between populations ((Russello et al. 2010, Garrick et al. 2012). The tortoises are famed for demonstrating speciation in progress as Darwin himself observed morphological differences related to the environmental selection.

Arguments could be made about what constitutes a good species, what species concept is being followed, but non were made. Apart from morphological, MtDNA and microsat evidence is there any evidence of incompatibility between subspecies; e.g. lower fitness, breeding avoidance? If not, this would add support to your argument (see Garrick et al 2014).

Such evidence does not exist, as far as we know. Very little is known on the relationship between genotypes, phenotypes and fitness in C. nigra, as we recall in the revised version. For instance, whether shell shape is heritable in C. nigra is unknown (Fritts 1984 Biol J Lin Soc, Chiari et al 2009 PLoS ONE), in absence of common garden experiments or crosses specifically addressing this question. Current efforts to avoid "hybridization" are in no way based on arguments suggesting that hybridization could be harmful to fitness. Rather, inbreeding depression was explicitly identified by, e.g., Milinkovitch et al (2013 Evol Appl) and Edwards et al (2013 Biol Conserv) as a potential problem in C. nigra repatriation programs.

I am sure the authors could add more discussion regarding the founder effect, bottle-neck, life history and demographic effects on Fit; compare the data to other island endemics that have experienced recent bottleneck e.g. lemurs are in the dataset.

Lemurs have been on Madagascar for dozens of millions of years; they do not appear to be particularly informative on island-induced founder events. Our data set includes a large number of species, each with its own history of fluctuation in Ne, isolation and secondary contact. We did not modify the manuscript based on this comment.

The authors write: “…current practice whereby so called “purebred” individual are crossed is pointless”. Could you reference this please, I could not find reference to this in the management plan nor, any of the papers quoted in the article.

This sentence was replaced by a longer description of past and current management plans. We now refer to Cayot (2008 Galapagos Res), Milinkovitch et al (2007 BMC Ecol) and Edwards et al (2013 Biol Conserv). Milinkovitch et al (2007 BMC Ecol) indicate that an individual carrying the "wrong" genotype was removed from an island to make sure it would not participate to reproduction – despite the acknowledged risk of inbreeding depression (Milinkovitch et al 2013 Evol Appl). Edwards et al (2013) make recommendations, based on genotypes at microsatellite loci, on which individuals should be crossed with which, and which should be released in the field.

Apart from referring to a news and views article, there is limited evidence presented of what the current management plan is for the Galapagos turtles. For those less familiar with this system it would help if the authors could provide references to the management plan itself, especially that demonstrates that it is being conducted primarily on microsatellite data a central theme to the paper. The microsatellites confirm morphological described subspecies/species also delimited by MtDNA (Ciofi et al. 2006). I understand they are not using microsatellites to delineate taxa, they found microsatellites to delineate the already morphologically described taxa and using these markers to identify hybrids (Russello et al. 2007; 2010; Garrick et al 2014) and make breeding decisions in captivity (Milinkovitch et al 2004).

We now describe in more detail the management strategy in C. nigra (l 60-80), based on the report by Cayot (2008 Galapagos Res). The management plan started in the 60's long before genetic data were available, and relied on the idea of restoring islands independently (Cayot 2008 Galapagos Res), which was probably a wise decision given the available information at that time. MtDNA and microsatellite data revealed some genetic structure between islands, and between populations within large islands. Genetic data lead to a taxonomic revision of the taxon that split C. nigra into 13 distinct species, partly in agreement with the pre-existing subspecies. Genetic data have significantly influenced management plans in, e.g., promoting the re-creation of so-called "extinct lineages" (Edwards et al 2013 Biol Conserv, Nichols 2015 Nature) or removing so-called "hybrids" from the field (Milinkovitch et al. 2007 BMC Ecol). More generally, publications based on genetic data have promoted the view that there exist "purebred" Galapagos tortoises, each belonging to one particular species, and individuals of "mixed-ancestry", most of which are supposed to originate from unnatural causes.

We disagree with this interpretation of mtDNA and microsatellite data C. nigra, which we think is biased towards over-splitting and based on a simplistic model of population history, in which gene flow is a priori assumed to be of human origins. We predict that by adding more loci, a different picture might appear, in which assigning individuals to "species" will be more and more difficult. At any rate, our main point here is not to criticize previous work, but rather to call for prudent decision making, knowing the limited power of existing genetic markers, and the unexpected results reported by Loire et al (2013 Genome Biol) and the current analysis.

The Galapagos Islands conservation program states they are “continuing using advances in genetic to refine tortoise conservation”. Is NGS therefore already in progress as part of the management plan?

It would seem there are large numbers of blood samples of tortoises (>1700 samples from Volcano Wolf alone, Garrick et al. 2014), more data is therefore feasible to get and is required to make such strong statements on management plans.

This is what we are asking for. One of our goals with this manuscript is to put pressure on C. nigra population geneticists so that they generate and publish genome-wide data in this taxon. Our group is not in position to do that – we do not have access to the samples, besides the five we collected in European zoos.

Minor recommendations: There are 54 animal species reported but, 52 in graph and with 4< individuals and in the supplementary table 1. There are more than 54 animals if the single and pair data are compared.

We now clarify that our data set includes 53 species, i.e., the 54 species of Romiguier et al (2014 Nature) with at least four individuals minus harvest ant Messor barbarus, in which F is strongly negative due to a highly specific mating system (Romiguier et al 2017 Mol Ecol).

116 species listed in the supplementary table S1, but there are 44 species pairs in Galtier et al 2016 (on Git hub). Where is the data from? Access to the data, could be improved with accession numbers, and a list of what individuals were pooled as the populations’ esp. in the pair wise comparison in Table S1. This will also hopefully include some sampling localities, as it is difficult to understand what sampling regime has been used e.g. which 4 samples were chosen to represent humans, or where the ants were sampled, from a single colony, are they actually clones? Are all transcriptomes of a similar tissue type? Or mixed? I would like further clarification on the data used; i.e. how many loci were in each set, what proportion loci analysed were used, what is the portion that shows no variation, all this could be added to Table S1? A table of the genetic variation between the 5 samples would be useful. I am sure this won’t change the overall conclusion reached, but a little more transparency would make reading the paper easier.

This information is available from the main text or Supplementary Information of the source articles Perry et al (2012 Genome Res), Romiguier et al (2014 Nature), and Galtier (2016 PLoS Genet).

This transcritpome data is also taken from only 1 tissue type (blood) while this is understandable on live animals, there is no discussion regarding the limitations of expression and therefore data from 1 tissue type. Neither do we get to know what type of tissue the other transcriptomes are from.

This information is provided and discussed in Gayral et al (2013 PLoS Genet), Romiguier et al (2014 Nature) and Galtier (2016 PLoS Genet).

The authors write; “C. nigra harbours lower genetic polymorphism and population structuring than most vertebrates or other animal species…” However most of the vertebrate samples are mammals (16/22), (more comparative reptiles (n=1) would be appropriate in this dataset) and 32% have lower Fit values than the turtles.

A low Fit, originally proposed as a measure of inbreeding, does not per se mean there is no population structuring. Ideally the two components of within and between population diversity need to be assessed but with only 5 individuals, makes what can be done inconclusive. Fit is below 0, which means there are slightly more heterozygotes than expected than a panamictic scenario; the cause of this could be discussed- mixed ancestry samples, or deleterious mutations?

We agree that our negative estimates of F were reflecting a bias in our approach. This is why we decided to take a comparative approach rather than commenting on the estimated values. In the revised version we used an improved SNP-calling method (Ballenghien et al. 2017 BMC Biol), which accounts for cross-contamination or other sources of read count overdispersion (see below response to reviewer 2).

Figure 1: the square on the human in the graph needs to be shifted so it does not overlap with the turtle.

Main conclusion: Conserving microsatellites? I think the inference about the conservation program is premature. I fully support the authors’ desires to encourage NextGen data to be completed across the Galapagos tortoise group. However, they have demonstrated that transcriptomes from blood may not be the most useful dataset, but there may be other genomic islands of diversification for example in the sex chromosomes or non-coding regions as found in other groups.

The tortoises are clearly a recent incipient speciating group, undergoing a radiation and suffered from multiple anthropogenic threats. Determining definitively whether these populations are species or subspecies, or populations, requires more data. No one will argue with the need to preserve all subspecies and populations, but the question remains on how to treat mixed ancestry individuals as natural or non-natural outcomes of habitat and species interference.

The authors here, suggest a halt to the practise of preventing these “hybirds” to contribute to the mating population. I have empathy with their view that sterilization seems a very extreme measure, as does crossing “purebreds”, but I am not persuaded yet, by their argument as presented that hybrids from the islands should not be removed. Writing further on the significance of lineage fusion (Garrick et al. 2014), the ability to identify recent (<200 years vs older hybridization events) would strengthen their argument.

I have empathy with the authors, but unfortunately these data, and current literature review of other evidence are not enough to say these turtles are panmictic. A more measured approach to writing an article about these issues I do think however has merit.

Thanks for your time in reading and commenting on our ms. We hope having clarified our view and improved the manuscript based on your comments. Regarding your very last comment: we do not mean to argue that C. nigra is a panmictic entity, and have modified the manuscript to avoid suggesting it. We rather state that our approach revealed no obvious departure from panmixy in C. nigra, whereas it did so in many other species of animals and vertebrates.

Reviewed by anonymous reviewer, 2017-04-13

The letter by Loire and Galtier provides an interesting provocative reflection about the “current” strategies/practices in conservation biology relying on classical (some may say outdated) approaches in conservation genetics. They present this opinion in the framework of the conservation of the giant Galapagos tortoises, where multiple species have been suggested based on genetic data such as short sequences of the mitochondrial genome and a dozen of microsatellite loci, but also backed up by morphological and geographical differences. Here, the author underline how poorly reliable such species definition based on:

1- the low number of genetic loci used to identify and characterize the distinct species (mainly mitochondrial and ~10 microsatellite loci); 2- the low mitochondrial sequence divergence between the recognized species, which is typical of the amount of divergence seen within species in reptiles; 3- that hybrid genotypes or unexpected mito-types were considered as originating from non-natural causes and were removed from previous analyses, thus artificially increasing genetic distinctiveness; 4- and finally, that links between morphological and genetic variation was anything but clear, with the “saddleback” morphotype being observed in unrelated species.

Given the limited and conflicting amount of evidence used to delimit those species, the authors question the drastic/spectacular conservation initiatives that are currently being taken to preserve the threatened tortoise species, which involve (among other) translocating animals, conduct breeding program to reconstruct original gene pools (some being extinct), based on the limited amount of genetic information currently available. The authors call for a much more extensive genetic survey based on genome-scale data in order to reconsider the taxonomic status of the species currently recognized.

Globally, I fully agree with this assessment. In such circumstances, conservation assessment should make use of the now affordable genome-scale dataset, especially when conflicting evidence occurs. This would ensure that population and species identification is reliable enough to justify and lead the conservation initiatives, that estimation of connectivity (gene flow) between distinct groups and admixture proportion are accurately estimated and accounted for in management programs, and that characterization of the gene pools are actually representative to the entire genome, not just a few microsatellite and mitochondrial loci. However, I have a few reserves regarding the way this letter is currently written, and how the argumentation is build, before I can recommend this manuscript.

Thanks for your excellent assessment and suggestions.

1- This letter looks like a late reaction to the comment in Nature of Nichols (2015) and a critic about how species identification has been identified based on the papers initiated in 2002 (by Caccone et al. and Ciofi et al. 2002) and updated in 2015 by Poulakakis et al. using the same methodology (low number of loci, morphology and geographic data). I am thus wondering why the authors decided to write this letter now, almost 2 years after the publications of those previous papers which presented the conservation initiatives undertaken at that time, and 4 years after the publication of the paper of Loire et al 2013. I understand that this paper was already discussing (I suppose) the poor representativeness of the genetic data collected to establish the conservation units, and was ignored by the scientific community leading these conservation initiatives. To me, this is not clear why in the present letter is coming so late. I think the author should clarify why they are reacting now. The issues raised in the current letter are indeed timely needed and should be heard by the conservation politics and managers. May be the authors could also provide an update of the status of the ongoing conservation initiatives, instead of just referring to the 2015 comments (of this information are available, of course).

Our research group has no specific focus on the Giant Galapagos tortoise. This species was one out of the ~100 we selected for a long-term project on comparative population genomics in animals (e.g. Gayral et al 2013 PLoS Genet, Romiguier et al 2014 Nature, Galtier 2016 PLoS Genet, Roux et al 2016 PLoS Biol). Unlike most of the species sampled in this project, we decided to specifically analyse the C. nigra data and write a paper on it (Loire et al 2013 Genome Biol) because: (1) we have an interest in reptile and turtle molecular evolution (e.g. Lourenco et al 2013 J Evol Biol, Figuet et al 2014 Genome Biol Evol), (2) we had detected interesting patterns of sequence variation, potentially reflecting adaptation to local environmental conditions, (3) C. nigra is an iconic species and a conservation target, so publishing the first genome-scale data in this taxon was, we thought, useful, and (4) our data did not appear consistent with the prevailing view regarding the taxonomy of this group, i.e., the existence of several species – even though we clearly stated that our sample was insufficient to draw firm conclusions.

Having published this, we were expecting C. nigra population geneticists to seize the problem, address the conflict by generating genome-wide data in a sample of sufficient size, and draw the appropriate conclusions regarding conservation. To our surprise, the following publications on C. nigra population genetics (Garrick et al 2014 Mol Ecol, Garrick et al 2015 Ecol Evol, Poulakakis et al 2015 PLoS ONE, Jensen et al 2016 Peer J) did not mention our 2013 paper or consider its message, but rather continued to rely on the same interpretation of the same mtDNA and microsatellites, as if our data were non existent. Our surprise further increased when we read the comment by Nichols (Nature, december 2015) and realized that this same 12-locus dataset was still taken as a justification for spectacular, costly interventions that may well be just irrelevant or even harmful to the animals.

Bewildered, we questioned the pertinence of our 2013 analysis and decided to check our results by adopting a comparative perspective across the many species of the project. The results were (we think) clear-cut: our approach apparently has the power to identify strong population structure and obvious species boundaries when they exist, and these apparently do not exist in C. nigra. We contacted Prof. Caccone in order to share our result, ask her opinion and hopefully make progress regarding the discrepancy – without success. Hence our decision to publicize this analysis, to at least let people know that the controversy exists, that more data are critically needed, and that important management decisions are made in spite of the conflicting pieces of evidence.

2- The authors state that mitochondrial and microsatellite data do not fully agree in the definition of the conservation units without providing any details on the actual issues and discrepancies. However, this is a central argument justifying the doubt raised by the authors about the validity of the currently recognized conservation units, populations, and species identification. Yet the authors do not really enter in any details and just quote Poulakakis et al (2012) as a reference, and stop short after that. The authors must make a better job at describing the actual conflict between loci, the potential or real issued in the interpretations and definitions of the conservation units, etc. If the species are actually not reproductively isolated pools, but are still very distinct populations, would that change the conservation initiatives?

This is a difficult question, which goes beyond the scope of this very manuscript. There are well known pros and cons of protecting local populations. Promoting gene flow between populations can act against local adaptation, but forced inbreeding can have deleterious consequences as well – only to speak about genetic aspects. Another related, difficult question is which level of gene flow is "natural", and whether we should intervene in order to decrease, increase, or equate the "natural" level of gene flow. All these questions are, in our opinion, regrettably not addressed in current literature on C. nigra conservation genetics.

Conservation of giant Galapagos tortoises clearly is a success in that population density has dramatically increased over the past five decades, thanks to a breeding/repatriation program that was decided and implemented before genetic data were generated, as we now clarify. We are here criticizing the most recent decisions – sterilization/removal of so-called "hybrids", relocation of animals, re-creation of so-called "extinct lineages" – which are said to be justified by genetic data. We disagree with the interpretation of existing genetic data, and ask for more data to be generated before such extreme decisions are taken.

We do not have strong recommendations yet, in absence of sufficient information. But if genomescale data and a large sample did concur with our preliminary data that population structure in C. nigra is "naturally" weak, then for sure we would recommend that these initiatives be discontinued. We added a section explaining our view in more detail (last paragraph of the revised manuscript). We suggest that, based on the existing data, C. nigra might well be best described as a perturbed metapopulation, not a collection of endangered species, which would make a big difference in terms of management.

3- The authors also present the microsatellite loci as poorly representative of the nuclear diversity. However, I have the feeling that the authors are mixing different aspects leading to a lot of confusion.

a. The heart of the author’s arguments is the low number of loci used to identify distinct gene pools, population and species rather than the type of markers. If I am mistaken, then the authors provide much more details about why microsatellites are not appropriate. Both mitochondrial and microsatellite data were used to recognized distinct populations and species in this system, not just microsatellites. So why stigmatizing the usage of microsatellites (see below)?

A very good point – see our response below.

b. The title of the paper even question whether we should keep using microsatellite loci at all in conservation genetics. Later in the text the authors question how representative the diversity at microsatellite level are compared to the genetic diversity of the genome. These points make little sense. Indeed, this is the low number of loci which is the real problem, not the type of loci. Hundreds and even thousands of microsatellite loci occur in genomes, but conservation geneticists usually use a dozen of them in their studies for practical reasons. Hopefully this is about to changes with the new NGS approaches (Gymrek 2017). Yet microsatellite variation is part of the diversity of genomes, among other source of variation such as SNPs, inversions, CNVs, etc. Furthermore, microsatellites display some appealing features making them very useful and informative even today. Their very fast evolutionary rate can be useful to track recent divergence, admixture proportion, very recent gene flow between population, and very recent changes in demographic histories provided that enough loci are used. Studies on model species showed how fast evolving these markers are (Gymrek 2017), how performant they can be to address key questions related to population structure and evolution within species, e.g. population structure, admixture and gene flow, such as in human (Rosenberg et al. 2002), chicken (Rosenberg et al. 2001). Furthermore these markers also show a remarkable clockwise evolution in human and potentially also in other species, making them very suitable for retracing the evolutionary history over recent time scale (Sun et al. 2009), and can also be linked with gene expression, making them more and more interesting as well (Gymrek et al. 2016). The main problem with microsatellite data is related to the difficulty and labor intensive work they require to optimize and score them accurately with classic approaches, which limited the number that can be handled. However, new NGSbased technics can solve this kind of limitations. Thus, these types of makers are still potentially very useful for tracking very recent population split, interruption of gene flow between groups, even if the level of divergence between these groups is low.

c. Although the very fast evolutionary rate of microsatellite loci can be very useful to address some questions happening at very recent time scale, they show a lot of limits related to homoplasy at larger evolutionary timescale, making them less suitable for addressing population and species evolution at larger timescale, of course. Thus, these markers might indeed not be so adequate, but it does not invalidate their usage when divergence is low. However, the authors do not really discuss any of these points, and just question their relevance without providing any details.

Now, I do not think the issues the authors want to raise is really about which type of markers should be used, but whether enough coverage of the genome has been achieved to resolve the taxonomic status of the different populations of tortoises. In the present letter, this is really that a dozen loci which is poorly representative of the genetic variation across the genome of the tortoises. This argument would have been equally true with only a dozen of SNPs scattered across the genome. I would thus suggest to change the title, removing the question “Preserving microsatellite?” and adjust the argumentation around the number of loci instead of stigmatizing the use of microsatellite loci.

We totally agree. The problem is the small number of loci, not the nature of these loci, and the manuscript was perhaps in part misleading in this respect. Our point is, because they only rely on these 12 specific loci, what people actually do in the first place by enforcing crosses between "genetically similar" individuals and removing "hybrids" is to favour specific allelic associations across these very loci – which might or might not correspond to true gene pools.

In the new version we try and make it clear that what matters is the number of loci, not the fact that these are microsatellites. We modified the last section of the text to clarify our point. We recall that there is no documented genetic incompatibility between gene pools in this species, no documented relationship between genotypes and fitness, no evidence for local adaptation, no demonstration that the major polymorphic phenotype, carapace shape, is heritable, and doubts regarding the very existence of population substructure. This is why we suggest current practice might not preserve anything biologically relevant besides particular combinations of alleles at ~12 specific loci.

4- There seems to be some confusion around the definition and identification of conservation units, populations and species in the previous papers and the authors in the present MS does not provide much clarification. The authors could shed some clarity on the biological units (populations and species) and what this could mean in term of conservation units for the present case of the groups giant Galapagos tortoises.

a. Indeed, based on previous mitochondrial data, the authors state that the level of divergence between named species observed are not higher than typical amounts of within species variation. They also show this with their own transcriptome data previously published in Loire et al (2013). However, the authors could certainly be more explicit and phrase it in term of level of divergence along the speciation continuum, and that this level of divergence is typical of what we see between populations within a given species. I suppose that the 4 to 11 individuals in each species considered in Romiguier et al (2014) included individuals from distinct populations. If correct, the authors should insist on that fact. Otherwise, the argument is falling short if the individuals considered in these studies only come from a single population or if this information is not known.

True: samples in Romiguier et al (2014 Nature) consist in individuals from distinct populations, as we now indicate (l 111).

b. In addition, there is a common confusion among conservation geneticists (and even more among conservation biologists in general) about the difference between genetic divergence between species and genetic differentiation between populations. The authors should make sure that this terminology is clear and accessible in their MS. Indeed, the divergence between the named species seems quite low and comparable to the divergence we see between populations within species. Thus, I agree that calling these groups as distinct species may seems exaggerated. However, this is a semantic discussion of what do we call distinct populations and distinct species, and how should be defined the conservation units, based on what variables and where do we put the threshold on genetic divergence? Answering these questions are certainly quite hard, subjective and at even philosophical. However, the authors limit their argumentation mainly to genetic divergence and make an attempt on genetic differentiation (although see my comment below about that), but does not enter into any details and consideration of how should we define conservation units, based on what criteria. If the authors want to have a real impact on the decisions and be heard by the manager, they have to provide more details and be more specific.

See above our response to comment 3. Again, we think that this complex issue goes beyond the scope of this piece. Not only scientists have their word to say here. The idea of reintroducing and protecting giant Galapagos tortoises in every island and every volcano of the archipelago is perfectly fine with us irrespective of population genetics.

Our only concern here is that decisions are currently made about which individual should be crossed with which, and at which place they should be located, based on questionable genetic data and analyses. We oppose the suggestion that some C. nigra individuals would have less value than others (e.g. Edwards et al 2013 Biol Conserv), and should be sterilized, kept in captivity or translocated only based on their 12-loci genotypes in a context of uncertain population genetic structure.

c. Since viable hybrids seems to exist, the distinct named species are apparently still interfertile. Thus calling them distinct species seems exaggerated (following the classic evolutionary definition of a species). That being said, this does not mean that these groups (populations) are not very differentiated populations. Actually, Poulakakakis et al 2015 showed, based on a descent sampling for the two groups (20 to 30 individuals for each) they have studied with a dozen of microsatellite loci and mitochondrial data, that the 2 populations were very differentiated from each other with remarkably high FST and RST values for microsatellite data (respectively 0.20 and 0.30 in average, Fig.5 of Poulakakakis et al 2015). This already quite high for such type of loci (Jakobsson et al. 2012). In contrast, Loire and Galtier contest these results using FIT values estimated for thousands of SNP loci from only 5 individuals (one or 2 in each named species). They show in their MS that FIT values are very low, and actually negative, and conclude that population structure is actually almost inexistent. Although I agree that the Loire et al 2013 data set offers a representative genomic sampling with ~1000 of loci, 1 or 2 individuals per named species (or population) and 5 individual total does not offer at all a representative sampling of the allele frequency spectrum in each group, which is required to estimated such FIT values (FST, or FIS). Tracking departure from Hardy Weindberg Equilibrium (HWE) based on 1 or 2 individuals per population is completely inappropriate, even with ~1000 loci, because there is no way the data can be informative on the distribution of the homozygotes and heterozygotes genotypes at given locus and test for departure from HWE expectations. FST, FIS and FIT are based on allele frequency calculation, which cannot be estimated with 1 or 2 individuals per group and a total of 5.

There is indeed a conflict between the microsatellite analysis of Poulakakis et al (2015 PLoS ONE, and previous papers by the same group) and our transcriptome-based SNP analysis regarding population differentiation. Before responding to this comment, we would like to recall that we do not claim having the final say on this issue, but rather call for additional data to be generated.

On Poulakakis et al (2015):

First, a rectification: the values for Fst and Rst between the two Santa Cruz populations reported in Figure 5 of Poulakakis et al (2015 PLoS ONE) are [0.07; 0.14] and [0.14;0.21], respectively, not 0.20 and 0.30 as suggested by your comment (see dark grey bars in their Figure 5; 0.20 and 0.30 correspond to the mean/median across many pairs of C. nigra populations). So these newly defined "species" differ from each other by Fst of the order of 0.1, which is similar to estimates reported, based on microsatellites, between pairs of human populations, somewhat reinforcing the parallel we are making. Secondly, and most importantly, their analysis (and previous analyses by the same group) only includes so-called "purebred" individuals, meaning that individuals carrying recombinant/mixed/intermediate genotypes have been removed. Obviously, such a pre-filtering of individuals inflates the observed level of differentiation between populations. So this Fst~0.1 is an overestimate – yet the two populations have been called distinct species by Poulakakis et al (2015 PLoS ONE). We describe this analysis in more details in the revised text and explain that comparing the published microsatellite-based Fst in C. nigra to estimates obtained in other species is tricky given their methodology.

On our measure of Fit:

We understand the concern about sample size, but still argue that our approach has the potential to detect departure from the Hardy-Weinberg equilibrium. Our analysis considers a single population and calculates the expected number of homozygous genotypes (summed across loci) under HWE. This number is compared to the observed number of homozygous genotypes (summed across loci), and inbreeding coefficient Fit, a measure of homozygote excess, is calculated based on these two numbers. We use the estimator of Weir and Cockerham (1984 Evolution), which is unbiased even in case of small samples. The sampling variance of one-locus Fit scales inversely with sample size (i.e., number of individuals, Curie-Cohen 1982 Genetics). Given the way data was here combined across loci, the sampling variance of our multilocus Fit also scales inversely with the number of loci (SNPs), assuming they are independent. So the two dimensions (individuals, loci) are essentially equivalent in terms of sampling variance at equilibrium. Empirically, our comparative approach demonstrates that this index has the power to detect strong population structure when it exists – just compare one-species vs. two-species samples in our figure 1. Roux et al. (2016 PLoS Biol) is another illustration of the potential of this kind of data to inform on population history and species boundaries.

Let us be clear: we do not mean to argue that sampling 5 individuals is an optimal way to measure population differentiation. Rather, we simply note that if population structure was strong, we would expect to detect an excess of homozygous genotypes in this sample, which according to mtDNA and microsatellites, consists in individuals from several distinct "species". One source of confusion might be that our analysis considers a single population per species, whereas the Fst/Fis/Fit framework normally involves two levels. In single population analyses, Fit equals Fis and Fst is not defined. To try and avoid confusion we now call the statistics F, introduce it as the inbreeding coefficient, and describe our calculation more thoroughly in the text and the legend to figure 1.

We added these additional pieces of information in the revised version, in which we highlight the need for new data and unbiased assessment of population differentiation in order to resolve the conflict between existing datasets.

d. Furthermore, the authors try to provide an ad-hock comparison of the FIT value between tortoise and human, in order to provide a comparative picture of the amount of genetic structure seen in the two species. They show that the negative FIT values found in human are comparable with those found in tortoises, arguing how absurd the is currently the species delimitation. However, the authors should note that FST and FIT values between human populations estimated in the literature are far from being negative, questioning how their estimated value is representative of differentiation among human population. Sticking with microsatellite loci for comparative purposes with the Galapagos tortoise case, Rosenberg et al (Rosenberg et al. 2002; 2005) showed that genome-wide estimates of FST values based on hundreds microsatellite loci across the genome can reach up to 0.12 between the most differentiated human populations, and is not at all negative as the authors seem to suggest. The authors should probably inspect the variance of their own FIT estimator before making any definitive conclusion. I suspect the variance would be very large given the very low (population) sample size. This also suggests that the averaged FST of 0.30 previously reported in Poulakakis et al (2015) between some turtle groups is extremely high and suggest very strong population differentiation. This is especially true since the maximum theoretical expectation for such highly polymorphic type of markers is usually bounded to a maximum of ~0.35 (Jakobsson et al. 2012). So even if the divergence between the groups is low, suggesting that population split very recently and did not accumulated much fixed differences, genetic differentiation between them is substantial. Now whether or not these should be called distinct populations, (sub)-species is a never-ending taxonomic debate in the divergence continuum of speciation, but they do certainly qualify as distinct conservation units. Now again, a dozen of loci might not be representative enough to estimates precisely population genetic parameters across the genome. More genetic data representative of the genome should thus be obtained, for sure. However, I don’t think the current comparison of FIT values between human and tortoise of Loire and Galtier is meaningful, since the data of Loire et al. (2013) and Romiguier et al. (2014) also suffer from such a small population samples size, that calculation of the allele (SNP) frequency and thus F-statistics are totally unreliable.

Regarding microsatellite-based Fst estimates in C. nigra and H. sapiens: see above our response to previous comment. Assessing the significance of published estimates of Fst in C. nigra is difficult because these have been obtained after so-called "mixed ancestry" individuals were removed from the data set. Comparison with analyses in other species or theoretical expectations is therefore tricky. Still, despite the upward bias, published Fst between "species" of giant Galapagos tortoise can be as low as 0.1 (Poulakakis et al 2015 PLoS ONE), similar to values reported between human populations.

Regarding our negative F estimates: this is indeed very unexpected – and one of the reasons why we decided to take a comparative approach rather than relying on the estimate itself. Clearly, our data contain more heterozygous genotypes than would be expected from natural samples, even in panmictic populations – and this is true of a substantial number of species, so that sampling variance is probably not a sufficient explanation.

Our hypotheses regarding this bias include sequencing errors, genotyping errors, hidden paralogy and cross-contamination. We recently analyzed patterns of cross-contamination in the Romiguier et al (2014 Nature) data set (Ballenghien et al 2017 BMC Biol). In this study, we developed an improved SNP- and genotype-calling algorithm that accounts for the overdispersion of read counts due to contamination or similar sources of noise. Compared to the original approach (Gayral et al 2013 PLoS Genetics), the new method typically yields lower estimates of piS and higher estimates of F (Ballenghien et al. 2017 BMC Biol), in agreement with our hypothesis that original estimates were biased.

The new, contamination-aware estimates of piS and F were used in this revised version. The text and Figure 1 have been modified accordingly. The point estimate for F is now significantly negative in only one species out of 53 (confidence interval obtained by bootstrap resampling). The overall message of the figure is unchanged, with single-species and two-species samples being well separated, and C. nigra clearly falling in the one-species side and very close to H. sapiens. This pattern – very low piS and F in C. nigra – is strong and robust to methodological artefacts.

In conclusion, I agree with the fact that not enough loci have been used so far to properly characterize the genetic structure and properly resolve taxonomic status of the giant Galapagos turtles. Additional genetic data representative of the genome should be obtained in order to refine the estimation of population genetic parameters and to resolve ambiguities. This should be done even before conducting any conservation initiatives. I do not think the authors are currently doing a very good job at showing the limitations and issues of previous studies. The arguments based on the low genetic divergence between named species could make sense, since calling them species may not be justified. However, the shallow genetic divergence does not mean that groups are not fully isolated. This can occur if populations have split very recently. Previous studies have shown substantial differentiation between groups. Even if this is based on a dozen of loci, this suggests that gene flow between them may be very limited or may have even ceased. A more representative assessment based on a genome-wide sampling is required, but this does not invalidate previous results that showed differentiated groups. Microsatellite can still be valuable markers to track very recent evolutionary processes. The argument about population structure being similar between what is seen in tortoises and in human makes no sense, given that estimated values for the Fstatistics are based the data set of Loire et al 2013 and Romiguier et al 2014, which include too few samples in each species leading to unreliable estimations of FIT. This preclude any proper test and accurate quantification of departure from HWE. Even if the data set include ~1000 of loci, accurate estimation of allele frequencies at each locus is required to test HWE and quantify departures from the expectations. Currently each species includes between 4 and 11 individuals, probably scattered across multiple populations. Theoretical and empirical studies show that about 30 individuals per population would be required. In the case of the tortoise, only 5 samples are available, and there I only 1 or two specimens for each group, which is totally insufficient to get any reliable estimate of any of the 3 F-statistics. I would thus suggest the author to remain focus on clarifying the current limitations of previous studies (low number of loci), the interpretation issues with the species delimitation and population differentiation, make sure that the terminology is clear even for non-specialists, and discuss what should be ideally done to resolve all the ambiguities. I would restrict the usage of the data of Loire et al 2013 and Romiguier et al 2014 to only estimation of the amount of divergence, but I would not use them to estimate any of the F-statistics, since the population sample size is too small. Previous studies reported strong genetic differentiation between at least between some of the groups, which then suggest that gene exchange between them may be quite low. Thus, these certainly qualifies as distinct conservation units. Should they be called populations, sub-species or species remained to be clarified. However more data are required to estimates accurately population genetics parameters, and these should be obtained based on an adequate sampling of the genome AND of the groups. The critics about the usage of microsatellite loci and the comparison of genetic structure between human and tortoises is not relevant in my opinion and risk to greatly reduce the impact of the message the authors want to share.

Thanks for your thorough, thoughtful review. Among other things, we hope having clarified that:

• we are not criticizing the usage of microsatellite loci;

• published estimates of Fst in C. nigra are to be taken with caution given the step of pre-filtering of individuals;

• our F estimator was indeed biased downwards due to experimental artefacts; correcting for these did not affect our conclusions.