All reviews of published articles are made public. This includes manuscript files, peer review comments, author rebuttals and revised materials. Note: This was optional for articles submitted before 13 February 2023.
Peer reviewers are encouraged (but not required) to provide their names to the authors when submitting their peer review. If they agree to provide their name, then their personal profile page will reflect a public acknowledgment that they performed a review (even if the article is rejected). If the article is accepted, then reviewers who provided their name will be associated with the article itself.
Please read the article again carefully for typing errors. The decimal comma should be replaced by the decimal point.
[# PeerJ Staff Note - this decision was reviewed and approved by Julin Maloof, a PeerJ Section Editor covering this Section #]
[# PeerJ Staff Note: Although the Academic and Section Editors are happy to accept your article as being scientifically sound, a final check of the manuscript shows that it would benefit from further editing. Therefore, please identify necessary edits and address these while in proof stage. #]
The authors have carefully addressed the reviewers' comments. There are a few lingering problems, which the reviewers highlighted. After these recommended, minor revisions, the manuscript will be acceptable for publication.
The authors have made satisfying efforts to revise the manuscript according to the suggestions raised by me and improved the manuscript substantially. However, in my view, some things still need to be adapted.
In my opinion, it is very difficult to interpret STRUCTURE results using non-neutral loci and the emphasis should be put on analyses performed with neutral markers. I think the Results section “Structure analyses” should be adapted accordingly by prominently presenting results for STRUCTURE and MavericK using 11 neutral markers. STRUCTURE results using nuSSR and EST-SSR markers only are, in my opinion, interesting additional information for the supplementary section and can be mentioned briefly but are not very relevant for the analysis of population structure.
I have some additional minor suggestions that might be worth to be addressed.
Titles and subtitles: In my opinion, the word “analyses” should be in singular in all the titles and subtitles.
Line 138: Are the authors sure about the higher error rate of SSRs compared to SNPs? Please consider to remove this statement or support with literature.
Line 150: “populations” should be singular.
Line 174: “and the distribution” could be changed to “together with the distribution”.
Line 267: “using, respectively,” should be changed to “, respectively, using”.
Line 315: “at populations” should be changed to “in populations”.
Lines 317-325: Please consider reformulating these sentences with emphasis on the neutral data set and consider trying to report Fst values more objectively. It is a bit difficult to me to understand what the authors mean with e.g. “using the “neutral” data set confirm the differentiation of the group formed by sites Lazio, Sicily, Sardinia and also of Corsica“. Is it the differentiation that formed the group or is this group formed by other factors?
Line 411: Line 331: “13 loci PCA scatterplots” should be replaced with something like “The PCA using 13 loci…”.
Line 546: “The existence of more than two clusters” should be changed to “The possible existence of more than two genetic clusters”.
Line 549: What do the authors mean with “population clusters”? Do you mean genetic clusters? Please specify.
Line 550: It is not very clear to me what is meant with “and the existence of several glacial refugia” in this context. Please consider to revise this sentence.
Line 907: There is a point after the question mark that should deleted.
Legend Table 2: “coefficient(Fis, Weir and Cockerham 1984)” should become “coefficient (Fis, Weir and Cockerham 1984)”
Table 2: In my opinion, genetic diversity estimates (observed &expected heterozygosity) should be presented per population here. This is a standard for reporting genetic diversity statistics and is interesting for the reader. Differences in genetic diversity between populations are not apparent in Table 1. Furthermore, I recommend to consider presenting the values using neutral markers instead of all 13.
Legend Figure 2: “Clustering plots from the analyses of the full data set and the neutral data set” is obsolete. Please adapt or remove.
Figure 3: In think an unrooted tree would be more appropriate instead of a phylogram.
Figure 4: The amount of variance explained per axis should be added to the figure or at least be mentioned in the figure legend. Knowing how much variation is contained in a single axis is very relevant for the interpretation of a PCA. The same is true for the supplementary Figure S3.
Figure S1: It is still not clear from the figure legend what the black line indicates. I think the answer of the authors to my initial comment on Figure S1 was related to Table S1.
no comment
no comment
First of all, I’d like to apologize to the editor and the authors for the delay in submitting my report. I had a very close familiar hospitalized and I had to postpone all my academic duties to take care of him. I hope this delay will have no impact in a fast publication of an article that I consider now suitable for publication in PeerJ.
After reading carefully the revised version of the manuscript and the answer provided by the authors to my previous comments, I am quite satisfied and think that the manuscript has been considerably improved and that most of the weaknesses of the first version have been solved.
I agree with the authors when they consider the manuscript is not a review, but I think that now they offer the reader a complete view of the ample literature in the manuscript topic. Moreover, they have included relevant references that support and/or highlight their findings (Lines 409-422; Lines 530-533; Lines 557-570). I must say that I still disagree with the consideration of the PCA results as significant, and I must insist that a 6% of variance explained by the first two components using this type of markers running a PCA should not “be expected with a multidimensional data set such as this one”. In any case, the additional support for the presence of a cluster in Corsica might be sufficient to justify the authors’ hypothesis. I also appreciate the inclusion of a sentence justifying those “black regions” that could not be sampled because they were not present in the provenance trial.
Therefore, I consider now the manuscript is suitable for publication almost as it is. I have only three minor comments (one of them merely formal) that might be considered by the authors prior to definitive publication:
Lines 499-500: “Results from PCA and CA analyses also clearly distinguish the group formed by Lazio, Sicily and Sardinia, and separate Corsica from the remainder”. I must insist that the percentage of variance explained by the principal components is not significant. I suggest to remove “clearly”, regarding Corsica.
Figure 3: Please, consider using some bootstrapping or permutation procedure to estimate the significance of the UPGMA branches. Possibly, taking a look at the Fst matrix in the supplemental files, the Corsican branch would be robust (> 75).
Line 531: Q. suber in italics, and homogeneize the species nomenclature across the text (Q. suber or Quercus suber).
Thank you for giving us the opportunity to review your manuscript for publication in PeerJ. The reviewers have found the manuscript of interest, but have raised a number of concerns that will require your attention. As these concerns are of some gravity and will entail substantial changes to the manuscript, you are likely to need additional time to address them. We cannot, therefore, accept the manuscript in its present form. Nonetheless, if you are able to address the points raised in review, we would welcome your resubmission of a manuscript that incorporates your responses.
[# PeerJ Staff Note: Please ensure that all review and editorial comments are addressed in a response letter and any edits or clarifications mentioned in the letter are also inserted into the revised manuscript where appropriate. #]
I think this study could be a valuable contribution to expand and complement the existing knowledge about the population dynamics of Q. suber. The introduction is well written and guides the reader towards the necessity of Q. suber population genetic studies and the value of different insights from different datasets.
My main concerns relate to the presentation and interpretation of the results. In my opinion, the present manuscript could be greatly improved by adjusting some of the analysis, simplifying the presentation of the results and by modifying figures. In addition, the wording in some paragraphs should be revised carefully.
You find my specific comments in the sections “Validity of the findings” and “Additional comments”.
The dataset with 17 populations and 22-30 samples per population is a solid basis for the study presented here and is sufficient to address the research questions of this manuscript. The statistical data analysis of the microsatellite markers appears to be sound and the methods are generally well described, with some exceptions (further details in the sections below).
Genetic markers used for analysis:
The test for marker neutrality is a valid approach to identify outlier loci. Using only the eleven neutral loci as identified by the BAYESCAN approach would improve the interpretability of the downstream analysis of genetic diversity and population structure. In the main figure 3 for example, the authors present the PCA of the neutral loci whereas the population genetic statistics in table 2 and pairwise FST-values are based on all 13 loci (if I understood correctly, not very evident from the text). I think it would be worthwhile to move analysis performed on the other sets of markers to the supplementary information or justify the inclusion of non-neutral markers in the analysis of neutral genetic structure.
Inference of genetic clusters:
The claim of the authors to have identified three genetic clusters is not enough elaborated in my opinion. It is not very clear to me, why the mavericK analysis (which does not include location information and correlated allele frequencies) is weighted more heavily than the structure analysis to infer genetic clusters. In my view, the identification of the number of K genetic clusters in this manuscript is relying too much on the methods for the inference of K, which are known to have their biases. I can very well imagine that, if there is substructure in these populations, comparing structure results for K=2-3 using the 11 neutral loci would also reveal a third cluster similar to the mavericK results pop up for K=3. Independent of the number of clusters identified by the Evanno method, this would provide evidence for further substructure in Q. suber populations. Instead of showing the plots for different numbers of loci and different software used in figure 2, I would recommend to show structure results for e.g. K=2-4 (or until no more new clusters pop up) for the analysis of 11 neutral loci. The existence of three or more genetic cluster could be further undermined with e.g. a neighbor-joining tree of pairwise Fst estimates and the PCA that is already presented.
Diversity statistics:
In the discussion, the authors claim a heterozygosity deficit of the markers because of a deviation of expected and observed heterozygosity. Table 1 shows locus-wise mean heterozygosity estimates. Because this analysis was not performed on the population-level (or it is not stated in the methods), it Is actually expected to find a heterozygosity deficit because of the Wahlund effect. These statistics, in my opinion, cannot be used to make statements about general heterozygosity levels of the species. Observed heterozygosity here is rather a characteristic of how polymorph a certain locus is. It would make more sense to show these statistics on a population level in table 2 or per locus with further information about population estimates (see e.g. Hoarau et al. 2002). The FIS estimates per population in table 2 indeed suggest that there is an incongruency between observed and expected heterozygosity but absolute numbers of heterozygosity should also be presented and are of interest.
Specific comments
Line 66: Do the authors mean increased drought frequency? Please specify.
Line 72: In this context Dauphin et al. 2021: “Genomic vulnerability to rapid climate warming in a tree species with a long generation time” could also be cited.
Line 120-121: I would suggest to delete the part about SNPs, they are particularly useful for many more approaches.
Line 143-144: Do the authors know anything about how the seed sources have been sampled for the provenance trials? Could this have an impact on levels of inbreeding or heterozygosity?
Line 151-154: Information about the Bulgarian populations should be deleted, as it is not very relevant for this study.
Line 179 & 189: Were FST-values tested for their significance? If not, this should be added.
Line 182-184: What do the authors want to test with a FIS calculated for K=3? Please specify.
Line 254-261: Please present the values of heterozygosity here.
Line 258-259: The abbreviations FST and FIS have been introduced before, no need to write it out. This is also true for the other abbreviations throughout the manuscript.
Line 259: It should rather be “..the mean FIS when considering the populations separately was..”.
Line 267-268: Which are the island populations? The levels of Ar are low compared to what, below the median, among the lowest 5 populations? Please specify.
Line 269: What is high in terms of numbers? Please specify.
Line 275: I think the authors should rather show FST-values of the neutral set, since there is an interested in neutral genetic structure.
Line 274-277: To which type of FST-values are you referring to here? Nei87 272 or WC84? Please specify.
Line 278-280: This belongs, if at all, to the discussion section. Otherwise, the authors should just mention the numbers. To which heterozygosity deficit are the authors referring to, FIS? I think population-wise heterozygosity estimates are not presented here.
Line 294-295: The interpretation about the type of selection should be moved to the discussion section.
Line 300-337: How do you define the term “admixture”? I am not sure if the authors should use the term “admixture” here or rather something like “showed mixed coancestry coefficients”. Admixture already implies genetic admixture between two groups which does not need to be the case if there is e.g. a third, different genetic cluster with K=3.
Line 311 & 329: “significant”: Did you test for significance? Otherwise remove.
Line 334-337: It is not clear to me why Corsica should be separated from the remainder. They individuals of the Corsica population cluster at least partly within the main cluster in the scatterplot.
How would you explain the outliers from the Sintra and Catalonia population in Figure 3?
Line 331: “13 loci PCA scatterplots” should be replaced with something like “The PCA using 13 loci…”
Line 335: “The CA” should be replaced with something like “The CA of the neutral data set shows…”
Line 344-354: This paragraph should be revised according to my comment on the diversity statistics. In addition, the Wahlund effect can also be responsible for a heterozygosity deficit.
Line 393-477: In my opinion, this section should be revised under the consideration of my comments related to diversity estimates and the inference of genetic clusters. I don’t think the authors can speak of the existence of three genetic clusters with the current evidence that is presented in this manuscript. Generally, I like the different aspects that are brought up in the discussion.
Line 395-400: I think this paragraph should be removed. Nowadays SNP genotyping can be achieved relatively cheap with a high number of samples and SNPs per populations. E.g. pooled sequencing is a cost-effective method to get genetic diversity estimates from a high number of SNPs. Furthermore, the first sentence does not make sense, SNPs can also be in low numbers.
Line 404: “SNP” instead of “SNPs”
Line 405: Which analyses, are you referring to the studies mentioned before? Please specify.
Line 462-466: Long and complicated sentence, please revise.
Line 474-477: The authors should also acknowledge that genetic diversity estimates based on microsatellite markers are not necessarily correlating with whole genome diversity (see e.g. Väli et al. 2008).
Legend Table 1 Line 2: Heterozygosity is missing a “t”, I would remove “overall gene diversity”.
Legend Table 1 Line 5: It should be mentioned that FIS are mean values calculated from the population estimates.
Legend Table 2: How many SSRs were analysed here? Please specify.
Legend Table 2 Line 3: To be consistent, you should also mention the method for calculating FIS.
Figure1: The distribution range of Q. suber indicated here would be very helpful.
Figure 2: I think the authors should use the abbreviations presented in Table 2 here.
In addition to the barplots, I would strongly recommend to plot genetic structure of one main result as pie charts on a map. The size of the pie charts could be scaled according to e.g. population-level heterozygosity. This Figure could then also replace Figure 1, which is not very informative on its own. Providing a spatial context would facilitate the interpretation of the results a lot.
Figure 3: How much variance is explained by each axis? What does the ellipse indicate? I think the ellipse could be removed.
Table S1: Which marker set was used for the calculation of FST? Please specify.
Figure S1: What does the black line indicate? This is not clear from the figure legend. Please specify.
I read with interest the manuscript by Sousa et al. "Population structure in Quercus suber L. revealed by nuclear microsatellite markers". The manuscript presents a report on population genetic structure of a Mediterranean evergreen oak, Quercus suber, that has been extensively studied along with other hybridizing Quercus species in the last decades. I must say that the manuscript is well-written and is easy to follow. The authors apply standard analytical approaches for these types of studies, discuss the potential issues of the specific microsatellites that may affect further inference, and interpret their results in regard of the population structure they find. The authors propose that nuclear SSR markers chosen in this study “proved to be an effective means for detecting population structure in Quercus suber, despite being in much lower number than SNP markers”. The findings may shed light on still unclear issues on the way cork oak populations are phylogeographically structured as a product of past climatic events (e.g. glacial cycles) and human induced expansions/fragmentations.
I have however some comments that should be considered before acceptance of the manuscript for publication in PeerJ.
(A) There is ample literature in this topic, part of which was not even cited in the manuscript. Actually, some of the findings of the authors were already proposed earlier in other studies. Therefore, I consider the inclusion of these references, along with some suitable discussion in regard to previous findings would improve the quality of the present manuscript. In particular, Q. suber genetic structure has been largely studied using different types of molecular markers with varied inheritance:
- A few relevant papers not cited in the manuscript and listed at the end of my report: plastidial RFLPs (Lumaret et al. 2005), PCR-RFLPs (López de Heredia et al. 2006, 2007) and sequence data (Costa et al. 2011), mtDNA (López de Heredia et al. 2018), isozymes (Elena-Rosselló y Cabrera, 1996; Jiménez et al. 1999; Toumi y Lumaret, 2001), nuclear ribosomal ITSs (López de Heredia et al. 2007) and AFLPs (Coelho et al. 2006; López de Heredia et al. 2007), nuclear microsatellites (Soto et al. 2003; Soto et al. 2007; López Aljorna et al. 2007; Burgarella et al. 2009; Lorenzo et al. 2009; Lumaret and Jabbour-Zahab 2009; Ramírez-Valiente et al. 2009), SNPs (López de Heredia et al. 2020).
- Cited in the manuscript: cpDNA microsatellites (Magri et al. 2007), nuclear microsatellites (Ramírez-Valiente et al. 2010), SNPs from nuclear loci (Modesto et al. 2014), SNPs from GBS (Pina-Martins et al. 2019; Vanhove et al. 2021)
The areas explored in the aforementioned articles is variable, sometimes covering the whole distribution range of the species and many other times restricting the sampling to specific regions. To my knowledge, a large proportion of the battery of nSSRs analysed in the present manuscript has been already used before in Quercus suber. Nine of these SSRs were early transferred to cork oak by Soto et al. (2003, 2007), and then extensively used to study introgression with sister species (Burgarella et al. 2009), local scale-spatial structure (Soto et al. 2007) regional population structure (Lorenzo et al. 2009 or to find correlation with functional traits using samples from provenance trials (Ramírez-Valiente et al. 2009-2010). Part of the information regarding the utility of these microsatellites included in these papers should be somehow included in the manuscript.
The interpretation for the population structure provided in the present manuscript should be also discussed in regard to the previous findings by Lumaret et al. (2005) using plastidial DNA and by López de Heredia et al. (20079 using plastidial DNA, nuclear ribosomal ITSs and AFLPs, not only to the more recent analysis with SNPs (Modesto et al. 2014, Pina-Martins et al. 2019, Vanhove et al. 2021), because both independent approaches already suggested three clusters for Q. suber in its whole distribution range (although not coincident with the clusters proposed here). While it is true that nuclear microsatellites here offer new insights on the genetic structure of cork oak populations (it is remarkable the behavior of the populations in Corsica, but see below), a more detailed discussion is required considering what other types of markers already showed.
REFERENCES
López-Aljorna A, Bueno MA, Aguinagalde I, Martín JP. (2007). Fingerprinting and genetic variability in cork oak (Quercus suber L.) elite tres using ISSR and SSR markers. Annals of Forest Science 64, 773–779. DOI: 10.1051/forest:2007057
López de Heredia U, Carrion JS, Jimenez P, Collada C, Gil L. (2007b) Molecular and palaeoecological evidence for multiple glacial refugia for evergreen oaks on the Iberian Peninsula. Journal of Biogeography 34(9):1505-1517 DOI: 10.1111/j.1365-2699.2007.01715.x
López de Heredia U, Jiménez P, Collada C, Simeone MC, Bellarosa R, Schirone B, Cervera MT, Gil L. (2007a). Multi-Marker Phylogeny of Three Evergreen Oaks Reveals Vicariant Patterns in the Western Mediterranean. Taxon 56(4):1209-1220 DOI: 10.2307/25065912
López de Heredia U, Vázquez F M, Soto Á. (2017). The role of hybridization on the adaptive potential of Mediterranean sclerophyllous oaks: the case of the Quercus ilex x Q. suber complex. En: Oaks Physiological Ecology. Exploring the Functional Diversity of Genus. Quercus, L. Eds. Gil-Pelegrín E, Peguero-Pina JJ, Sancho-Knapik D. Cham, Switzerland: Springer International Publishing, 239–260.
López de Heredia U, Mora-Márquez F, Goicoechea PG, Guillardín-Calvo L, Simeone MC, Soto Á. (2020). ddRAD Sequencing-Based Identification of Genomic Boundaries and Permeability in Quercus ilex and Q. suber Hybrids. Frontiers in Plant Science 11:564414. DOI: 10.3389/fpls.2020.564414
Lorenzo Z, Burgarella C, López de Heredia U, Lumaret R, Petit R J, Soto Á, Gil L. (2009). Relevance of genetics for conservation policies: the case of Minorcan cork oaks. Annals of Botany 104(6):1069-1076 DOI: 10.1093/aob/mcp200
Lumaret R, Tryphon-Dionnet M, Michaud H, Sanuy A, Ipotesi E, Born C, Mir C. (2005). Phylogeographical variation of chloroplast DNA in cork oak (Quercus suber). Annals of Botany 96(5):853-861. DOI: 10.1093/aob/mci237
Lumaret R, Jabbour-Zahab R. (2009). Ancient and current gene flow between two distantly related Mediterranean oak species, Quercus suber and Q. ilex. Annals of Botany 104(4):725-736. DOI: 10.1093/aob/mcp149
Ramírez-Valiente JA, Lorenzo Z, Soto A, Valladares F, Gil L, Aranda I. (2009). Elucidating the role of genetic drift and natural selection in cork oak differentiation regarding drought tolerance. Molecular Ecology 18:3803-3815. DOI: 10.1111/j.1365-294X.2009.04317.x
Ramírez-Valiente JA, Lorenzo Z, Soto A, Valladares F, Gil L, Aranda I. (2010). Natural selection on cork oak: allele frequency reveals divergent selection in cork oak populations along a temperature cline. Evolutionary Ecology 24:1031-1044. DOI: 10.1007/s10682-010-9365-6
Soto A, Lorenzo Z, Gil L. (2003). Nuclear microsatellite markers for the identification of Quercus ilex L. and Q. suber L. hybrids. Silvae Genetica 52:63-66.
Soto A, Lorenzo Z, Gil L. (2007). Differences in fine-scale genetic structure and dispersal in Quercus ilex L. and Q. suber L.: consequences for regeneration of mediterranean open woods. Heredity 99:601-607. DOI: 10.1038/sj.hdy.6801007
Toumi L, Lumaret R. (2001). Allozyme characterisation of four Mediterranean evergreen oak species. Biochemical Systematics and Ecology 29(8):799-817. DOI: 10.1016/S0305-1978(01)00024-2
(B) In relation to this latter point, the sampling scheme adopted in the manuscript gives me some doubts, both at global and local scales:
- Global sampling: I suggest including a layer with the distribution range for the species in Fig. 1 and then overlap the sampling sites. The authors can access the shapefile (or a jpg image) here: http://www.euforgen.org/species/quercus-suber/
According to this map, while there may be an over-representation of Portuguese populations (for obvious reasons), there is no representation of the populations from central Iberian Peninsula, the Landes nor from southeastern France.
This bias may be understandable providing the sampling was done in provenance trials rather in natural populations, but it must be considered in the discussion. For instance, the adscription of Corsican samples to a different cluster, which is new to this manuscript, could be more easily explained if some samples form southeastern France (Provence) were included here. This would require further confirmation, but I would expect some kind of relationship between cork oak populations from these regions.
The lack of Central Iberian samples is more difficult to explain, as they form part of the international provenance trials for the species and in any case, they could have been sampled in natural populations. Some of the papers I referred above have analysed some of these populations with 9 out of the 13 microsatellites employed here.
- Local sampling:
Another issue related to the sampling strategy is that 22-30 samples might not be sufficient for certain analyses. For SNPs Pina-Martins et al. (2021) and Vanhove et al. (2021) used 6-7 samples for SNPs, and using 22-30 is an improvement, as the authors suggest, but it may still be short to be free from bias inferring many genetic diversity parameters, and interpretations should be cautious.
(C) Despite my comments above, I consider that, overall, the methodology employed in the manuscript is correct. It applies the standard analyses one would expect for the particular question the authors aim to answer. Actually, this is the type of analyses population genetics studies based on nSSRs use to perform. The analytical methods to explore the validity of the 13 nuclear microsatellites to infer population structure at a global scale are appropriate for this type of research (linkage between markers, null allele estimation, neutrality tests, H-W equilibrium estimation), and I appreciate the github link that includes genepop data and R scripts to build Fst based dendrograms and to the plots of principal component analysis, which is in line with the open research commitment of PeerJ.
I have also some comments regarding the methodology employed here that may compromise the validity of the findings:
- Several Structure clustering approaches are adopted including and excluding markers from the analysis. While there is evidence of some degree of linkage between markers (for instance between QpZag36 and QpZAG46), I’m not sure if this was considered when running all the Structure simulations for K=2 and K=3 with 13 or 11 “putatively neutral” markers.
- Regarding the optimal K number from Structure, I consider there is not enough support for a third cluster including Corsican populations. Indeed, the authors support this finding with the PCAs. This is correct, as pointed out by the authors, the number of genetic pools inferred by Structure (K) frequently requires independent support. The problem is that here, if the data from Fig. 3 are correct, the clusters inferred by plotting PC1 vs PC2 are inferred from two principal components that explain only 6.85 % of overall variation, and this is non-significant. Being strict, these results should not be presented, as they may induce to incorrect interpretations of the results. A clarification is needed here before acceptance.
(D) Quercus suber is a species with undoubted commercial values in rural areas from the Western Mediterranean. I am convinced that uncontrolled acorn transfer between areas has not been the rule in the past, even less between distant regions, but I expected at least some comments in the Discussion referred to the impact of human intervention in cork oak distribution. Some expansion of Q. suber woodlands after the last Glacial cycle might be favored by human action, possibly enabling local expansion of between adjacent areas. We cannot interpret the current population structure of species that have been handled extensively in the past without considering that they form part of highly anthropized ecosystems (even more in the Mediterranean region than in other areas of the world).
(E) There are only marginal references (Lines 462-466) to introgression of cork oak with other evergreen Quercus species (Q. ilex in the west and Q. cerris in the east of the distribution range). Both ancient and contemporary introgression levels have been extensively studied (even with 9 out of the 13 markers employed here), and the impact of this introgression in the population structure of cork oak could be better discussed. Some estimations of contemporary introgression in mixed Q. suber-Q. ilex stands were < 2% (average) (Burgarella et al. 2007), but this introgression could have been underestimated and, in some areas, introgression could affect the number of private alleles inferred with this set of microsatellites. At leas a reference in the Discussion is required.
(F) Minor comments:
As said before, the manuscript is well-written, the Figures (except for my comments above), tables, supplemental information and files in the github link are correct. I only found a typo in Line 95: "drivers" instead of "driver"
All text and materials provided via this peer-review history page are made available under a Creative Commons Attribution License, which permits unrestricted use, distribution, and reproduction in any medium, provided the original author and source are credited.