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Thank you for your changes.
Both reviewers raise concerns regarding some of the generalised claims made in the study. There are some sensible suggestions how to tone these down to something that is appropriate to the results of this study. This must be made - especially in the abstract.
In addition to the reviewers comments, I have made some additional observations on the ms:
Lines 28-30. - reformulate problem statement to mention sibs.
Line 92 = panmictic
Line 96: Do you mean in amphibians or do you know that this hasn't been done in fish & insects?
Line 122: Using "amphibian*" as stated would exclude all instances of Amphibia - so if correct this would have to be redone.
Line 138: It would be useful if you gave target numbers that you had for each life history stage - did you achieve your own targets and is this relevant to the interpretation of how such studies are conducted? Note lack of larvae in some ponds.
Line 208: this is the same reference list you used in the introduction. Looks a little odd given that it's used as a result here.
Line 345: What?
Line 370: Would appear sensible to give a preference for embryos.
The paper adheres to basic reporting standards.
In terms of extent, the study does only focus on one species, in a spatially restricted cluster of ponds. Since ponds are within about 3.5 km of one another, it is possible (and in my opinion highly likely) that all of 'populations' belong to the same genetic cluster (especially given the extremely low FST values). This was not tested - there is no use of STRUCTURE or similar programs (BAPS, TESS, GeneLand) to determine population structure. We cannot assume that each locality is a population, and given the small extent, is is possible that all the sampling is from only a couple 'populations.' This presents a problem since the main findings were differences in population genetic differentiation measures between life stages. Results may be a case of the Wahlund Effect.
Beyond this, landscape genetic papers tend to sample across different habitat variables, which is essential since population genetic measures can be affected by local habitat conditions. In addition, studies tend to sample across a larger portion of the species' range which also ensures that different environmental factors exist within the sampled populations. Another large issue is that authors make strong suggestions against sampling mixed life stages in landscape genetics studies yet their sampling extent does not compare to most landscape genetic studies. It is also very misleading to have landscape genetics in the title yet not contain any landscape analyses. If the authors were to perform landscape analyses and find differences in supported landscape features based on life stage it would be justified.
There are strong claims based on very minimally significant results. FST/Dc was significantly higher for some population pairs based on the statistics used, but the differences were small in some cases. Take into account population parir '2_3' which had an adult FST of 0.005 and an embryo FST of 0.006. These are significantly different, but how does a difference of 0.001 affect a population genetic or landscape genetic analyses. My opinion is that it would not. Most changes is FST between populations are small here and I'm not convinced. This is an issue when the authors focus on how other studies don't account for life stages, yet do no discuss how their findings could change the outcome of another study. There are many negative results here, and I believe they are a results of such a small sampling extent (pointed out above).
It seems that you missed an opportunity to sample known full/half sibs in the embryo stage to have 'control' samples. For instance, if you take multiple eggs from the same small clutch then you have high confidence in those individuals being full or half-siblings. Sampling in this manner would have allowed you to partially test the effectiveness of COLONY. That is, determining if COLONY identifies your known half/full siblings.
What COLONY parameters were used? These can influence which individuals are considered full-siblings so they should be reported. In addition, it may be beneficial to use another kinship package to determine if full-siblings are consistent between programs.
It seems all of the ponds are man made ponds. There is not a lot of habitat description - do these ponds have the same habitat characteristics as wild ponds?
Ln 48: Weak opening statement
Ln 102: Should probably mention the system you studied here.
Ln 108: This hypothesis needs expansion. How and why should this affect estimates?
Ln 131: This might be a personal preference, but including the sample size in the methods I think makes the analyses a bit more clear?
Ln 140: Were these mesh funnel traps placed in or at the edge of the ponds?
Ln 141: If you were interested in how siblings affect population genetic metrics then why not purposely sample full/half siblings?
Ln 197 linkage disequilibrium method in Colony
Ln 170: Were all of these calculated using the Excel toolkit as well?
Ln 173: It would be useful to know sample size at this point
Ln 214: 8 ponds total? Make this clear. Perhaps give the total sample size
Ln 221: Does the .5% missing data include microsatellite loci that were no scored (i.e., due to ambiguity?) ?
Ln 360: Landscape genetics is most effective when sampling is done across habitats. Just a note if you are going to make landscape genetic inferences.
The manuscript is well-written and provides sufficient background on the issue, as well as relevant citations to the issue of genetic sampling of different life stages. The authors reference availability of raw data, although I did not see a way to review that raw data myself.
The manuscript addresses an important question in population genetics; namely how the sampling of different life stages might affect conclusions related to genetic diversity and genetic differentiation. While the authors accurately state that the issue is not generally addressed in studies, they build on a previous study that compared conclusions between subsamples of adults and larvae. The authors extend this previous study by including embryos, but by also investigating how the mixture of life history stages might influence population genetic conclusions.
The microsatellite genotyping methods are clear and appropriate and the authors use accepted analytical methods for estimating genetic diversity and differentiation. The one controversial method is the Mantel test for IBD analyses which the authors acknowledge. I agree with the authors that for the purposes of this study, the Mantel test is likely sufficient.
There are two aspects to the experimental design that could be added that I think would improve the overall study. First, and simplest, would be to do some subsampling of the microsatellite loci. In the discussion, when pointing out some of the discrepancies between this study and the previous Goldberg and Waits study, the authors comment on how they have more microsatellite loci and perhaps more power. It would seem to me to be relatively straightforward to test that hypothesis by subsampling loci at two or three levels to see if it makes any difference in the estimates of diversity or differentiation. A second addition would be more substantial and is a simulation component. I suspect the authors have already considered it and determined it was beyond the scope of their current study. And I certainly do not think it is essential for the paper to be accepted. But it could be very useful to help understand why the authors see some of the patterns that they do, particularly considering some of the differences between this study and Goldberg and Waits, which occurred in a similar pond-breeding amphibian system.
The main conclusions of this study are sound. It is pretty clear that genetic diversity is largely consistent no matter the life stage sampled and that the biggest differences occur with isolation by distance analyses. The other interesting result was that removing siblings did not make a big difference in any of the analyses.
My major criticism is that I don't necessarily agree with some of the conclusions in the discussion based on the results. For instance, the authors recommend against sampling larvae, largely on the rationale that sampling larva is inefficient because of having to remove so many siblings. This is despite the lack of a strong sibling effect in their dataset. I understand the authors are likely trying to be conservative in their recommendations, especially since Goldberg and Waits did find a bias when all siblings were included. My concern is that if the authors do not trust this aspect of the results, then it seems hard to trust other aspects (such as the IBD patterns) that the authors do place more emphasis on.
Related to this is my discomfort with the statement that the findings are broadly generalizable to other pond-breeding systems. However, without a more thorough investigation of the mechanism behind the pattern, which would require simulations (see comments in above section), I don't think the authors can make this statement. Most obviously, there were some clear differences between these findings and that of Goldberg and Waits, which was focused on the same type of breeding system. Furthermore, with respect to IBD, we have no idea the history of this landscape. I could imagine a hypothetical scenario in which there was recent landscape change that restricted gene flow, and so adult genetic structure represented the time before fragmentation, but the larva represented the result of recent land change. There are a number of other scenarios that could be in play as well. But because this is one species in one landscape, we can't really get at what is leading to the pattern.
I still think the results of the study are valuable and an important contribution to population and landscape genetics. I would just remove the text in the discussion regarding how general the study is. Instead, I would give a greater emphasis to the section of the discussion that suggests pilot studies. I think the value of this manuscript is that it supports the Goldberg and Waits study in that it demonstrates the potential for differing conclusions based on life history stage, but also that the differences may not be entirely predictable and is study-dependent.
Overall I think this study is valuable to the field of population genetics as an example of the importance of accounting for sampling of different life history stages. I think the manuscript can be easily improved by adding a subsampling component for number of loci, as well as reworking the discussion as described above. I consider these both minor revisions that would not require additional review by me. If the authors wanted to expand the generality of the study, then I would recommend adding a simulation component. I do not consider this essential, but if the authors chose this route, I would consider it a major revision and in that case would want tor review the revision.
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