An ancient age of open-canopy landscapes in northern Madagascar? Evidence from the population genetic structure of a forest tree

Dear Jordi Salmona, Guillaume Besnard and coauthors,

Thank you for the thorough revision of your manuscript. You have satisfactorily addressed the concerns raised by the reviewers.

However, in the evaluation of your reply it has come to my attention an important problem that was overlooked in the previous round of review. At different parts of the manuscript you refer to “genetic diversity”, “heterozygosity”, “Ho”, “He”, and “% of polymorphic sites” regarding nuclear RADseq data. After carefully reading all the relevant text and supplementary materials I conclude that in all of these instances you are referring to the same measurement: the individual heterozygosity per base pair, that is, for each individual the number of heterozygous sites over the total of sequenced data (after application of relevant filters). First, the text needs to state this more clearly and use a consistent name for that measurement throughout the entire work. Second, individual heterozygosity is a poor measure of genetic diversity. For instance, it can be affected by the reproductive system (i.e. clonal or selfing reproduction). Expected heterozygosity (per bp, i.e. π) calculated among individuals of the same forest patch (for comparisons among populations) or over all individuals (for comparisons with other species) is a more appropriate measure and what most readers expect as a measure for genetic diversity, please add this or an equivalent measure to your work. Since the levels of genetic diversity are one of the main results from the work this problem needs to be addressed before the work can be recommended.

In addition to this main point there are some other minors points that I would like you to consider:

In the discussion you suggest that current landscape structure must have been in place “at least 40 generations” corresponding to “at least ~800 years”. I think there is little justification for those numbers even in the light of the results by Landguth et al., (2010) and Mona et al. (2014). The dynamics of how pattern change through time in non-equilibrium models depends on many unknown parameters (effective population sizes, migration rate…), giving such precise numbers seems misleading. While I agree with the general message and I understand that this sentence was intended to address a point Yurena Arjona raised in her review, I think it would be more appropriate to discuss that the number of generations for the period with data on forest cover (1953-present) represent less that 5 generations, which seems too low to erase the signal of previous population structure (or lack of).

Please verify that the description of header for Table S1 is complete and accurate.

In line 617, I suggest to write “geographical distance” instead of “Euclidean distance”.

Last, I would like also to suggest you considering an alternative wording for fragmentation/forest fragments throughout the text. Since one of the conclusion of the work is that the landscape structure with open areas is a relatively old feature, it is unclear to me whether there was ever an ancient continuous forest in the region subsequently fragmented (presumably by humans). Thus forest patches might be just that, “patches” and not “fragments”.

Dear Jordi Salmona, Guillaume Besnard and coauthors, I have now received the reviews for your manuscript. While they are in general positive, both point out few concerns regarding the methods, conclusions and writing that require further work on the manuscript. Please consider all their comments carefully before submitting a revised version for evaluation. I believe most of these points can be addressed by working on the text and no further analysis will be necessary. However, pay special attention to properly justify the absence of new analysis regarding the concerns on the methodology. Both reviewers highlight the lack of explanation for the reduction of samples from sampling to genotyping. Please revise your text so it is completely clear for the reader why there are such differences. In addition, clarify how the survey of Noronhia was conducted and if N. spinifolia was identified in the field. Were all Noronhia spp. sampled? In the main text it is unclear if the 220 samples are from Noronhia spp. or from N. spinifolia only (in the supplementary text it is clearly stated, but I think the reader should not need to go there for this basic information). Another question that seems to require a more clear explanation is the discussion of the age of forest fragmentation in the area. I believe that some of the confusion stems from the better fit of the genetic distances with data on recent vegetation cover (2000’s) but a conclusion that forest fragmentation structuring the genetic diversity of N. spinifolia must be ancient. It might not be clear for the reader why data on older vegetation cover does not explain better the genetic structure of N. spinifolia. I also have some points I would like you to address: 1) Regarding the discussion on the role forest cover for seed dispersal (lines 497-509), it is not obvious to me why patterns of mtDNA and cpDNA haplotype networks would be incompatible with the signal found by IBR analysis on organelle data. I would appreciate if you could develop this point. 2) Supplementary data availability: In addition to making available the missing Table S1, please consider making supplementary tables S6, S7 and S8 available through reputed repositories (such as institutional repositories, Zenodo, DataDryad, supplementary material in bioRxiv...) that can assure long term accessibility to those files (instead of Google Drive/Docs service). Also, I could not find reference PRJNA632767 in the Sequence Read Archive (SRA) NCBI database, make sure the reference is correct and it is accessible. 3) line 59: "tropical biodiversity hotspots" instead of "tropical hotspots" 4) line 72: Specify what 40-50% are referring to (area?) 5) lines 324-5: It is unclear what the values “m=4, M=5, N=8” are. Please clarify: a brief description/definition (such as in figure S5) should be included in the main text when and in the supplementary materials (Method S6) when they are first mentioned. 6) line 466: instead of “prehistoric”, which strictly refers to the time period before the invention of writing, use “non recent” or some other wording. 7) Table S2: What is the difference between columns “Allele number” and “Number of alleles”? Best regards, Miguel Navascués   **Additional requirements of the managing board**: We would like to receive your revision within 2 months. If you need more time, just tell us. As indicated in the 'How does it work?’ section and in the code of conduct, please make sure that: -Data are available to readers, either in the text or through an open data repository such as Zenodo (free), Dryad or some other institutional repository. Data must be reusable, thus metadata or accompanying text must carefully describe the data. -Details on quantitative analyses (e.g., data treatment and statistical scripts in R, bioinformatic pipeline scripts, etc.) and details concerning simulations (scripts, codes) are available to readers in the text, as appendices, or through an open data repository, such as Zenodo, Dryad or some other institutional repository. The scripts or codes must be carefully described so that they can be reused. -Details on experimental procedures are available to readers in the text or as appendices. -Authors have no financial conflict of interest relating to the article. The article must contain a "Conflict of interest disclosure" paragraph before the reference section containing this sentence: "The authors of this preprint declare that they have no financial conflict of interest with the content of this article." If appropriate, this disclosure may be completed by a sentence indicating that some of the authors are PCI recommenders: “XXX is one of the PCI XXX recommenders.”