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The new version only partially satisfies my criticisms, but I consider it now meets the minimal acceptance criteria.
[# PeerJ Staff Note - this decision was reviewed and approved by Patricia Gandini, a PeerJ Section Editor covering this Section #]
Despite the favorable opinion of the reviewer, I am not yet satisfied with the quality of the present version. Indeed, when addressing the crucial question of marker selection, you claim to «we identified a total of 37 dog microsatellite loci from earlier published literature (Holmes et al.; Ostrander, Sprague & Rine, 1993; Fredholm & Winterø, 1995; Ostrander et al., 1995; Francisco et al., 1996; Neff et al., 1999)».This literature listing is far from exhaustive and many essential publications are missing, such as - doi: 10.1016/j.fsigen.2018.08.005, doi: 10.1016/j.fsigen.2013.07.002, PMID:15480731, PMID: 15935941, PMID: 15168130; PMID:22139664, PMID: 20129463, PMID:20024924, PMID:19204943.
Please check and modify accordingly the sections Material & Methods and Discussion.
I'm now satisfied with the new version of the manuscript, which is now simpler and more limited in its scope, but also much clearer and more robust
no comment
no comment
no comment
I could not find satisfactory answers to the questions raised. Please address the reviewer comments.
[# PeerJ Staff Note: Please ensure that all review comments are addressed in an appropriate rebuttal letter, and please ensure that any edits or clarifications mentioned in the rebuttal letter are also inserted into the revised manuscript (where appropriate). Direction on how to prepare a rebuttal letter can be found at: https://peerj.com/benefits/academic-rebuttal-letters/ #]
The manuscript has further improved and most of the previous observations have been addressed, including language polishing and clarity
no comment
I still think that the presentation of the population structure analyses could be further improved by including some of the reasonings on possible weakpoints regarding discrepancies between the two methods, possibly unsampled populations, etc. reported in the cover letter also in discussion, especially regardin the PTR-TATR group.
Beside this, it is not clear to why "the low success rate might be one of the reasons behind the skewed sex ratio in this study."...if you expect to find a differential amplification success, please clearly state so with a specific reason/reference, or delete this sentence.
I also agree with the other reviewer on the opportunity to reorder Suppl. Figures as to improve their logical flow (TESS vs. DAPC all together)
No comments, see general comments
No comments, see general comments
No comments, see general comments
The manuscript of the second revision shows only minor changes compared to the preceding version although both reviewers and the editor raised a number of concerns. The authors provide extensive and mainly comprehensible explanations in their answer letter, however it would have been beneficial to include these in the manuscript.
In the following I want to focus on the points raised in my preceding review:
L313: There is still a discrepancy between text and Figure 1. TATR=4 instead of TATR=8
L314-317: This section was not edited and is still misleading although the authors state in their answer letter that no difference between PTR; UKWLS and TATR was found. Generally, the population genetic analyses show some pattern, but it would be better to shorten the interpretation section. The authors rightly point out that this paper should mainly present a genotyping method applicable to non-invasive samples from wild dogs. It would make the main message of this study more clear if the authors would give less details of the population genetics analyses. In this context this is not essential and even more confusing.
Supplementary Figure 2 was successfully revised
I cannot recommend this manuscript for publications as long as the authors do not revise the text according to the above mentioned points. Language editing is still needed.
I think the manuscript is still far from the acceptance level; besides the Reviewer’s’ criticisms, I keep some unanswered doubts I have formulated to the first version since the rebuttal letter was unsatisfactory. I detail below, but one major issue is that the nomenclature of the results must be defined, namely the classification of the ‘empty’ genotypes, specifying clearly if they are due to total lack of amplification or to ‘unreliable’(?) data. The collective assignment of a ‘0 value’ is not acceptable and this clarification would allow a sound analysis of the data.
To «false alleles» I would prefer to stick to ‘genotyping errors’, but I agree that previous authors in the field have introduced this misleading wording. In any case I do not how «slippage artifacts during PCR reactions, lead[ing] to both homozygous and heterozygous erroneous genotypes».
I still do not understand the ‘cumulative’ PID mentioned in the Table as it is denoted per locus (or primer pair). As it is, the table should be filled in with the values par locus with an end line containing the cumulative value. Moreover, how is it calculated? You state it «basically indicates the additive value of the PID(sibs) with addition of respective loci.» which would suggest the values are arithmetically added.
I have not checked the calculations (it depends on the solutions provided to the problem of missing data), but it is my experience that when the difference between He and Ho is as large as the ones you estimate, observed genotype distributions do not fit HWE. Please check.
On sex rate estimation, have you checked the accuracy of the test with sex-known samples?
The current version of the manuscript is much improved and the explainations given by the authors are mostly satisfying.
Nonetheless, the use of English still needs some polishing, especially in the newly added sections (e.g. matching the new section tens with the rest of the ms).
The caption for Suppl. Fig 2 is not clear enough.
All relevant information previously missing from the methods is now available to the reader.
The conclusions on genetic structure and connectivity are still counter-intuitive given the relative distance among the study areas and the possible reasons for this (e.g. geographical barriers? known patterns of deforestation?) need to be clarified to the reader. This section looks like the least robust of the paper
Specific comments:
(suggested changes are indicated in capitals)
L. 156: "roadS/trails"
L 160: "once a latrine WAS found"
L. 161: "One bolus from each fresh scat was collected, ASSUMING IT TO DERIVE from one individual"
L. 174: "once PER SITE"?
L. 184: please indicate how much blood was collected
L. 267: "bands" can be misleading (more commonly referred to gel testing of amplification success), maybe use "allelic peaks" instead?
L. 273-283: please adapt the tens to the rest of the paper (the past should be used)
L. 303: see above regarding "bands" (consider rephrasing)
L. 386: Is this value calculated based on the seven best-performing loci, the 7 worst-performing ones, or as an average of any combination of 7 loci among the total 12?
L. 411-412; "assigment OF each sample TO" ?
L. 529: you mean "fragmentation"?
L. 542: I would not use "great", maybe "valid" is more appropriate?
no comments, see general comments
no comments, see general comments
no comments, see general comments
The authors made great efforts to improve the manuscript according to the reviewer’s suggestions/comments. They added important details of the used methods and the lab work carried out. This improves the traceability of the results and is know more helpful for other researchers planning to perform similar analyses.
However, some potential for improvement remains. Therefore, I recommend this manuscript for publication if the following point are considered, which in my opinion could easily achieved at this stage:
L381-382: the numbers of unique individuals do not correspond to those given in Figure 2, please check.
L384-386: Figure S 1a shows clearly attributable genetic clusters for MTR and NNTR, but for PTR I cannot see obvious differences to UKWLS and TATR.
Figure S2: Please add sampling areas to each of the listed samples and insert column headings. The meaning of the colour coding is not explained.
Suggestion: as Figure S1b and Figure S2 both base on DAPC maybe change numbering (S2a and 2b)
Besides the comments and suggestions from the Reviewers, I further ask to consider the following:
- I could not find the criteria for classifying alleles as ‘false’
- definition/discussion of null alleles, dropout and genotyping errors are insufficient and seem incorrect; please clarify/distinguish misclassifications (if any), null alleles (resulting either from dropouts or primer binding problems) in fact I have not checked if null alleles estimation is correct, since no data per locus are presented.
- at least in some of the selected loci homozygous null genotypes (seemingly too many) are found
- the difference between observed and expected mean heterozygosities (0.40 and 0.62), respectively is too high
- sexing success rate (67%) is unacceptably low and may bias sex ratio estimation
- Table 1 legend is inadequate and should include ‘primer sequence’ and ‘diversity estimates’, and I do not understand ‘cumulative’ in the headings of some columns, and the number of displayed decimal places should be standardized per column.
• The language is appropriate and clear, but with several minor flaws noted below.
• The cited literature gives sufficient field background for the study, although some additional info that are relevant for the analyses carried out by the authors should be briefly included in the text
• Tables are clear and complete, the figure is appropriate but needs minor improvements, raw data in the form of multilocus genotypes have been shared.
• The body of the work is coherent and complete
• The research falls well within the aims and scope of the journal.
• The research aim is clear, relevant and meaningful. It is stated how research fills an identified knowledge gap.
• The investigations carried out look appropriate, but lack some relevant information on the results obtained
• Methods are mostly clearly described with sufficient details to be replicated – a few details indicated below are lacking
• The benefit to literature are clearly stated, although the actual improvements compared to previous research should be better motivated.
• Data appear robust and controlled, although a few unexpected features of the results (genotype recaptures and sex ratio) should be better motivated and supported by additional analyses
• Conclusion are well stated, linked to original research question & limited to supporting results.
The paper is mostly well written and clear, tries to fill the current limitation to better investigate an endangered canid species, taking advantage from the existing literature on domestic dog genetic features.
In my opinion, the two main issues that need to be improved or better justified in order to increase the robustness of the results are the following:
- The very low recapture rates (1/102 genotypes) look potentially suspicious to an external reader: I strongly suggest to either better explain how, given your sampling strategy, this result could be expected, and/or perform an easy mismatch analysis on the obtain genotype in order to evaluate how many of them differ for a small number of alleles that could be due to erroneous electropherogram interpretation (and also to better exclude the possibility of observing a ‘shadow effect’ that could occur when PIDsibs is low). Similarly, the observed sex ratio 4:1 should be better motivated in the light of the species biology or of the methods applied.
- The resulting PIDsib is good, but does not represent a strong improvement compared to previous literature. This should be better explained in the text, and its appropriateness explained taking into account the whole estimated population size (not only mature individuals)
Other points that could be improved:
L. 108-111: “Research permits and ethical considerations”: what about the 4 blood samples?
L. 133-135: please specify (if possible) how many km have been linearly investigated, or how many different latrines have been surveyed.
Figure 1: please include a section that represents the position of the study area within the Indian subcontinent. The Y-axis of the histogram should be labelled with ‘number’ only, since it also refers to scats and not only individuals. Please also indicate ‘genotypes’ instead of ‘individuals’ – which is formally less correct.
L. 161-161: ‘low PIDsibs value (3.3x10-4), indicating a potentially inefficient panel for unambiguous individual…’. This PIDsib value is in line with what obtained in your study. Please be consistent in the way you evaluate the efficacy of your results compared to theirs – and be objective in how you report your improvements compared to previous literature.
L. 173-174: just a reasoning: given the extensive application of those markers to wild canids as well, did you base your selection on the variability observed in wolves? Maybe they could be less biased by domestication and be more representative of the dhole variability…
Table1: please explicit which markers (if any) were included in the panel applied by Iyengar et al., 2005
L. 199: Please briefly summarize the methods described in Modi et al., 2018.
L. 205: Please briefly summarize the methods described Miquel et al., 2006 and explain what Q.I. threshold you applied per locus and per sample, and also the minimum number of loci per individual with a reliable consensus genotype (I think you mention this in line 271, but I think it should be reported here instead)
L. 212: Please briefly summarize the methods described in Modi et al., 2018.
L. 262: please indicate the results for False Alleles as well.
L. 280: please specify if it refers to M:F ratio (or viceversa). Possible reasons (biological, technical, etc) for this high skew should be explained in the discussion.
L. 283: please indicate as clearly as possible the correspondence (if any) between these six clusters (subclusters within areas?) and the 5 sampling areas.
L. 284. ‘The clusters indicate no genetic sharing between MTR and PTR’. Please explain the reasoning behind this statement (in the figure the correspondence of cluster with sampling areas is not indicated, please add labels if possible)
L. 286: please explicit the values for deciding that K=4 was the best clustering. Do you think that individuals with traces of ancestry from a different cluster could represent dispersers? This would be highly relevant for connectivity and future population dynamics (you can just raise the point here, then talk about this in the discussion)
L. 289: please explicit the formal results from Bottleneck for each model.
L. 292: are these results significant
L. 301: ‘with high statistical power’: please see the second main comment above
L. 323: see comment above on PIDsib vs. census size (not only mature individuals can be considered in order to reach a good resolution of the panel)
L. 332: I think the reasoning here is not powerful enough, unless you better motivate the reason why when sampling a given latrine for multiple scats you still don’t get resampling of the same individual (e.g.: maybe you selected only very fresh samples, therefore it is unlikely that you picked up two fresh faeces from the same individual? This would be important to know in order to exclude the possible doubts raised in the first main comment
L. 338: do you think that the limited amount of blue components in PTR individuals –if relevant - cannot be due to gene flow from MTR? Also, from Suppl fig 1b I see NNTR as a separate cluster, not intermediate between the two, except for a few individuals with blue component…what are you referring to? Please try to be much more rigorous and clear here
L. 355: please the consider the term ‘great’ in the light of the not-much-improved PIDsib compared to previous studies
Minor issues:
L. 29-30: not clear what ‘and landscape level’ means here
L. 76: ‘and included in Appendix II…’
L. 77-83: these two paragraphs could be improved in their fluidity
L. 88: ‘are ineffective’
L. 91-95: please avoid embedded parentheses
L. 96: ‘provides’
L. 103: ‘this this’ ?
L. 120: ‘consisting of’
L. 125: ‘present’
L. 130: ‘sample-containing’
L. 150: ‘respectively,’
L. 176: please explicit what genome build you used as a reference (canFam 3.1?)
L. 219: newline character to be removed
L. 264: ‘relatively high’ instead of ‘higher’?
Vertebrate animal usage checks:
• Please provide additional info on the blood sampling procedure
Basically, the article is written in professional English but an additional overhaul is recommended to improve the readability.
The structure of the article conforms.
Figure 1 should by revised. An overview map of India should be included to show the location of the sampling area within the country. Additionally, I suggest to show the inserted bar graph independently (maybe as Figure 2). This would improve clarity and gives better visibility of the results.
The legend to Supplementary Figure 1a does not explain the correlation between the cluster numbers and the Sampling sites. This makes the corresponding section of the manuscript (lines 281 to 285) not verifiable. Text and/or Figure 1a should be revised.
An additional Supplementary Table showing the genotypes of all samples should be included to make raw data available.
The authors state that “in this study, we address key methodological issues…” (Line 99). Taken this self-chosen key area into account more methodological details should be given. The authors should consider the following questions and objections:
As reference samples only 4 dhole individuals were used. This small number should be explained. Are these individuals unrelated? Was the genetic diversity sufficient?
All markers were originally developed for the domestic dog. During the validation of the genetic tests samples from domestic dogs and other canids should have been included. Can the authors exclude that DNA from other species affect the genotyping results. Is a mix up with domestic dogs possible?
Are the primer sequences shown in Table 1 taken from the corresponding references listed in the Table or are they newly designed/modified?
Table 1 does not show which markers are combined to the 4 multiplexes. This reduces the reproducibility of the method by other laboratories.
Line 186: 50 cycles is very high; please comment; was contamination an issue?
Line 194: specify the CE model used
Line 279-280: Molecular sexing is not described in Methods
The genotype data were processed with different statistical methods to draw conclusions. This was done in an appropriate manner. But the following issues should be considered:
The authors refer PID values based on 12 loci. As a minimum of 7 loci was considered as sufficient for individualization PID values for this reduced number of loci should be given and evaluated.
The conclusions drawn from Supplemental Figure 1b (lines 285-287) are not comprehensible. Please describe in more detail and/or improve the Figure.
In the Discussion I miss a consideration of possible relatedness of the sampled individuals. From the social behavior of dholes sampling of scats from related individuals is probable. Have you found individuals most probable closely related? And can closely related animals compromise the accuracy of individualization?
The authors present an appealing contribution for non-invasive DNA analysis of wildlife animals. This publication should be revised to improve the usability for other scientists working in the field by adding more methodological details and by expanding the validation approach (i.e. by including other species like the domestic dog)
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