Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: SPECIES TURNOVER IN PLANTS DOES NOT PREDICT TURNOVER IN FLOWER-VISITING INSECTS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The manuscript is well-structured and well written. However, I see a major problem with the hypotheses. Both hypotheses  include the question how plant diversity affects insect diversity. However, there is no statistical test on diversity patterns, but only on community composition.
Experimental design: The experimental design is clear, relevant and meaningful.
Validity of the findings: I do not think that the analyses support all conclusions. See "Basic reporting" and "comments for the author" for details.
Additional comments: I appreciate the effort of Simaika and colleagues to revise the manuscript. Yet, many aspects of the manuscript are still unclear and need further revision.

First of all, throughout the manuscript the usage of the terms species richness (or diversity) and community composition are not clearly separated. In several parts of the manuscript the authors draw conclusion about diversity patterns based on analyses of community composition (see comments below). It remains also unclear why it is important to compare species turnover of plants and insects as the introduction is mainly about diversity patterns and “turnover” is mentioned in the hypotheses for the first time.
In the discussion the authors write that based on their study the diversity of plants cannot predict the diversity of insects (L285-286). However, there is no statistical test showing whether plant diversity is a good predictor for insect diversity (again community composition changes are not the same as diversity changes). I agree with Reviewer 2 that the comparison of plant and insect diversity is the most interesting part of the study and therefore a statistical test is urgently needed to support this result. Based on the sampling design with different distances between the sampling sites the authors should account for this spatial dependency, e.g. by adding random effects or by including coordinates of the sites in the model.

Comments:

L48 I do not understand this sentence. Why is stability needed when plants and insects react similarly to climatic conditions as written in the previous sentence? Generally, I think that the impact of past climate is off topic and should be rather excluded. Instead the focus should be more on the concept of species turnover and why it is important for conserving affectively both, plant and insect species.

L88-89 In the analysis the authors do not compare the diversity at different distance classes, but the dissimilarity of community compositions. Diversity and community composition are totally different concepts.

L152 “data pooled per array and visit”?

L154-155 I assume you used the same estimator for plants and insects?

L174-177 After reading the cited reference I understand that 1 means that the samples that are closest to each other have the most similar communities while the most distant sites would have the least similar communities. I think this should be explained in the manuscript. Additionally, from the results I understand that you also compared plants and insects in this analysis. You should explain how this was done.

L184 This header is misleading as you do not relate plant and insect diversity, but their community compositions.

L219-220 “Trend” according to which hypothesis?

L228-229 There is no test showing the relationship between plant and insect species richness.

L231-242 I find this analysis not very interesting. It is not very surprising that the closest communities are generally more similar. I would omit this analysis or move it to the supplementary material.

L266 replace by “Effect of vegetation structure on insect community composition”

L285 See comment above, there was no test for species richness relationship.

L286-291: Unfortunately, the patterns found in Fig. 3 are not explained in the discussion. What could be the reasons for these patterns? I agree with Reviewer 2 that Figure 3 represents the 3 main spatial groups of sites as shown in Fig. 1 (A: rectangles, B: circles, triangles and diamonds, and C: star and crosses). The points within the first distance class are comparisons of sites within each of the 3 groups (A,B and C). The distance class of about 25-40km represents comparisons of sites of group B and C. In the last distance group (60-70km) the authors compare sites of group A with both B and C. Here the authors interpret the results that turnover of insects tends to increase across distance groups. However, the authors might have found these results simply because B is a little bit closer to A than C and it could be another environmental factor that influences the higher similarity of B to A than C to A (for example percentage agricultural land in the surrounding or crop grown in the vicinity). This possibility should be discussed.

L302-313 The authors should also acknowledge that there are many studies showing that plant species richness is very important in predicting pollinator species richness (e.g. Ebeling et al., 2008. How does plant richness affect pollinator richness and temporal stability of flower visits? Oikos 117, 1808–1815. or Papanikolauo et al 2017. Wild bee and floral diversity co-vary in response to the direct and indirect impacts of land use. Ecosphere 8(11):e02008)

L303-304 I do not understand this sentence.

L306 Specify what was analyzed: “herbivore community composition”?

L327 Again, there is no test to support any conclusions related to diversity patterns.

L344-346 This test also includes community composition and not diversity.

L358-361 I do not fully understand the last sentence, please simplify.

Conclusions: You found that flower cover had the highest impact on insect communities. Are there any management practices that can increase flower cover?


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: SHELL VARIABILITY IN THE STEM TURTLES PROTEROCHERSIS SPP.
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript is clearly written. The English is for the most part correct, and professional. Minor unidiomatic constructions and small grammatical mistakes are scattered over the text but do not compromise its comprehensibility. I have marked and suggested corrections of many instances of such problems in the PDF file. These are most frequently omissions of the definite article (i.e. "the").

I do not have deep knowledge of the literature on turtle developmental biology or detailed stem-Testudines anatomy. To the extent that I could appreciate it, the background information given by the authors was pertinent, sufficient, and provided with a wealth of references, among which were the papers that I would have expected to see cited.

The overall structure of the article is standard and logical. However, I found that the methods section is insufficient for following the presentation of the statistical results. The manuscript would be much improved by moving the text in p. 7 of S1 to the methods section. The figures are very good; clear and detailed. The manuscript makes reference to several measurements of length, width, &c, that are not given in raw form in the supplementary materials. The information is mostly given in the text itself, but if the authors have tabulated that data, it would be very desirable to make it available in a plain text format such as CSV. I appreciate that the authors do provide raw data of the gular region in the form of 3D objects embedded in a PDF file. However, I think it is better to give this data in PLY or STL format, as these formats are open standards and readily readable by most 3D software. 3D PDF was designed for visualisation only, and it makes it very hard if not impossible for other researchers to recover the geometry data of the models.

The manuscript contains results that are relevant to the issues raised in the introduction. Some of the hypotheses (e.g. sexual dimorphism) could have been stated more saliently.
Experimental design: The manuscript fits the aims and scope of PeerJ, as it contains original research in the Biological Sciences that consisted of the collection of very detailed data, and a sound discussion thereof.

The research questions are presented in the Introduction section. The authors explain how their study represents a systematic examination of phenotype variations that are known to be widespread in Recent turtles, but that has been explored only in a few early testudinatans (in good part due to limited fossil evidence, an issue in this study as well).

I found that the authors gave a very attentive and exemplarily detailed description of the shell variation of the concerned species, both in text and figure form. Some parts of the statistical analyses I could not understand. That might reflect problems in the writing of the manuscript, the use of methods unknown to me (in which case I'd appreciate a reference), or the application of the methods themselves. To the degree that I could evaluate it, I found no evidence of tampering with the data or the analyses. I see no reason to doubt that the authors proceeded in accordance to a high ethical standard.

As mentioned before, I think that the methods section could be much improved by adding the text that had been relegated to the supplementary material, and I think further clarifications would still be necessary. For instance, the regression models are not given out explicitly, and therefore they cannot be easily replicated and interpreted.
Validity of the findings: The authors clearly discuss the novelty and relevance of their data in relation to the evolution of developmental processes of the shell in Testudinata, sexual dimorphism, and (inconclusively) to palaeoecological environment. They also suggest avenues of further research in these topics, by means of palaeohistological studies.

The textual description and graphic representation of the data is of high quality, and I expect that the quantitative measurements were acquired with similar care. The practical sample sizes are very small, as it is too common in vertebrate palaeontology. This is of course no intrinsic failing from the authors, but the statistical conclusions that can be derived from the quantitative data should be regarded with extra caution.

The conclusions are clearly stated, responsive to the issues raised in the introduction, and follow from the observed data, although I think they should be tempered slightly in relation to the sexual dimorphism. I have certain doubts and critiques of the statistical methods used by the authors. I recommend major revisions solely because I could not understand all the methods and therefore cannot assess their validity. I have no expectation that the revisions should invalidate the conclusions of the authors.
Additional comments: This article is a valuable contribution to turtle palaeontology, providing data that is useful for the study of character evolution and the inference of the phylogeny of Testudines itself. I stress the latter, because failure to assess phenotypic variability and understand its nature can have grave effects on phylogenetic analyses.

The conclusions reached by the authors seem to me reasonable and consistent with the data. However, the degree of support that is afforded by the data is unclear to me in some cases. Maybe due to miscommunications or actual methodological problems. In either case, I think the manuscript be improved without much extra work.

Starting with the "Methods" section, as I mentioned before, I think it is insufficient for a self-contained reading the manuscript. Moving the "Principal Component Analyses" section in the supplementary materials to the "Methods" section of the main article would go a long way in making the article more comprehensible (by the way, the "Principal Component Analyses" section covers PCA only in its last paragraph, most of the text is actually about data acquisition and GPA superposition). Further, the version numbers of all the software used should be given, as this allows more faithful replication. Different versions can have different feature sets, algorithmic implementations, and bugs. In a more technical and admittedly pedantic note, MeshLab is distributed as "free software" under a GPL 3.0 Licence, which is different to what is commonly meant by "freeware". The concept of free software is based on the idea of freely sharing the source code, while freeware can be any software whose binaries are distributed at no cost, but the source code might remain undisclosed.

Moving on to the results, there are many references to "correlation indices" between linear measurements. I am not familiar with this term, the authors probably meant "correlation coefficient" (eg., p.21.l.462, p.25.l.601). The type of correlation coefficient (probably Pearson's) should also be reported, as well as the associated p-value. Those correlation coefficients were obtained from only 4 observations, so I think the authors should be more cautious about the strength of the evidence for the length correlations. Consider that n=3 is the bare minimum number of observations necessary for estimating the fit of the data to a linear model.

In p.30.l.735-44 a regression analysis is said to have been used to determine the presence of separate clusters in the shape of the ventral view of the gular region. I do not understand what regression model was used. What were the dependent and independent variables? What was the regression coefficient? More importantly, I do not understand how regression analysis was used to determine cluster separation. An explanation of the logic of this procedure and maybe a reference seem necessary.

In p.34.l.872-75 the authors claim that the PCA of the caudal region shows two shape clusters (and two singletons corresponding to juveniles). These clusters are not so apparent to me by the naked eye, certainly much less than the clusters of shapes of the vertical cross-section of the extragulars. For instance, in the PC1-PC2 plot SMNS 17561, which is assigned to "Group I", is practically equidistant to V39/69 in "Group I" and SMNS 12777 in "Group II". "Group II" could also be arguably divided into the shapes with PC2 > 0 and the shapes with PC < 0. The cannonical variates analysis that the authors perform does seem to validate the separation of the two clusters (with a rather large p-value, bearing in mind that the significance threshold of 0.05 is an arbitrary convention), so they might reflect some relevant biological phenomenon, but this still does not explain to me how the clusters were identified in the first place. An implicit and reasonable assumption seems to be that the number of clusters must be two in order to match the sexes, but no further criterion is apparent.

A way to validate "Group I" and "Group II" or to find alternative groupings is to use a partitional clustering algorithm such as k-medoids or k-means, among many others. These algorithms are not infallible, and might not yield optimal clusters for instance when the clusters have very different variances. Should the authors want to use them, they ought to check that the limitations of these algorithms and how they relate to their assumptions and the nature of their data. k-medoids and k-means are available in multiple R packages, and k-means is available in the software PAST. k-means is known to be more sensitive to outliers.

Alternatively, if the authors had an a-priori expectation of the shapes that would be clustering into "Group I" and "Group 2", that ought to be explained.

The CVA used to validate the clusters of the caudal region can also be used for the clusters of the vertical cross-section of the extragulars. It is not clear to me why the authors did not employ this method in the two cases.

Finally, in p.35.l.896-98 the authors mention a regression analysis, but again it is not clear on what variables the analysis was performed. Fig. 10C shows that the centroid size is the independent variable, but the dependent variable is given as a "regression score" of meaning unknown to me. Further, I do not know if a log-transformation was employed, as it is customary in allometric models. This analysis merits a more detailed explanation.

I provide the annotated review PDF so that the authors can check the language problems that I spotted.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: SHELL VARIABILITY IN THE STEM TURTLES PROTEROCHERSIS SPP.
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript is of very good quality and the findings are important to the understanding of the early evolution of turtles, showing that some of the common intraspecific variability seen in extant turtles were already present in the earliest representatives of the group. Although none of the authors is a native English speaker (but neither am I), the manuscript is well-written and the language used throughout the text is adequate. I made some specific corrections along the manuscript (please find all of those in the annotated PDF) and some suggestions on the usage of specific words, more specifically some anatomical orientational terms, that, in their current usage, make the manuscript sometimes difficult to follow.
The Background and Introduction sections show the relevant context for the development of this research and Literature is well referenced all along the manuscript. The structure of the manuscript conforms to PeerJ standards. I felt that the Results section, especially the descriptions of variability, is a bit too extensive and could be summarized to make the text more fluent and easier to read. It is difficult for me to tell what is more relevant and what could be may be sent to the supplementary files, but do consider revising that.
Figures (as well as supplementary figures) are relevant, high quality, well labeled and described. I suggested the inclusion of one additional figure (that could be added to the supplementary file without any problems) to more clearly refer to some specific variation on shell scutes.
The raw data in itself seems alright to me, but I consider it problematic that the authors didn't fully present some of them, e.g., complete descriptions (with reference to figures) of the sets of landmarks used for the shape analyses, and that the description of some analyses (especially the correlations/regressions) are only very briefly state in the supplementary files.
Please, find below more extensive details on these issues. In conclusion, I support the publication of this manuscript after revision of those points.
Experimental design: The research is original, with well-defined, relevant and meaningful questions presented and answered by the authors and the experimental design is adequate to this study.
The methods, although adequate, are not fully described in the manuscript, hampering replicability of their findings. Even though it appears to me that all analyses were conducted properly, the methods are described only partially in the supplementary files. I strongly feel that it is necessary to describe in more detail some of the analyses the authors conducted (especially correlation/regression analyses, and the landmarks used in each set of analyses) and I advise to move at least a brief description of the conducted quantitative methods to the main text (Methods section), instead of leaving everything in the supplementary files, since those are a very important piece of this research.
Also, I felt that the manuscript would benefit if the authors created a "Shape Analyses" section in the Results. Describing all morphological variation at first and then presenting the results of quantitative analyses to back some of the generated hypotheses seem to me a more straightforward and easy-to-follow way to present their results. Even if you do not agree to make a new section, the results of the quantitative analyses should be described in more detail. More specifically when the authors report and discuss the variations along the Principal Component and Canonical Variation axes, it is critical to report what do these variations mean in morphological terms, otherwise, it is just a graph. So, for example, when saying that Groups I and II are separated along the PC1 axis, what do the variation on positive and negative values of this axis mean for the morphology of the analyzed element?
If the descriptions and report of the methods, I cannot consider the methods description sufficient for replicate.
Validity of the findings: The manuscript presents important new data, with some novel interesting insights about the morphological evolution of early turtles. The results are described in detail, proper analyses are conducted (although I suggested they should be better described) and the discussion and conclusions, even though I made few suggestions on specific parts, are well stated and adequate to their findings.
Additional comments: I made several minor and some major comments along the annotated PDF of the main text and the supplementary file S1 as well, please, do consider those when revising the manuscript.
I consider it important to review the usage of some terms, such as cranial/caudal and anterior/posterior, and 'ontogenetic age' all along the manuscript. In the case of using cranial/caudal and anterior/posterior there is no agreement on which set of terms are more adequate and you can choose any of these, but, you should use those consistently through the text. When you use both cranial and anterior in the same text (sometimes in the same paragraph) the reader feels that you want to refer to distinct issues, i.e., that cranial means one thing in this context and anterior another. I do not think that was your goal, so I do advise you to choose and use just one kind of these terms. If that was your goal, you should more explicitly define what you meant by each of those. Other terms you used along the text, such as 'behind', 'higher', etc., I consider ambiguous terms for anatomical descriptions. Please, do consider also reviewing them and changing for more straightforward terms, e.g., posterior to, dorsal to, etc.
Using 'ontogenetic age' in the descriptions also bothered me because you cannot define an age for those materials without using their sizes as proxies. So, why not use size instead? Larger individuals, instead of older individuals, for example, are more appropriate in the description. You can (and should) approach the ontogenetic age in the Discussion section, when you will refer to larger or smaller individuals and discuss their inferred age relations.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: SHELL VARIABILITY IN THE STEM TURTLES PROTEROCHERSIS SPP.
Review round: 1
Reviewer: 3

Output:
Basic reporting: The English is fine (at least for me, I am not English speaker)
The references are fine
The article structure could be a bit improved (see remarks about cutting discussion/results differently)
Except potential circularity with statistical methods, the results and interpretation sound to me (see general comment).
Experimental design: The morphometric methods and statistical procedure should be better explained even in the appendix. As it stands, it would be difficult to reproduce easily the same study because there is not enough explanations about procedures.
Validity of the findings: The interpretations sound to me, the conclusion are well supported by the study.
Additional comments: main document:

This is an interesting, long, exhaustive, and complete study about shell variation in Proterochersis. There are few similar studies done on fossil or living turtles and I was very interested by the text.

I found the english understandable and correct (I am not english native); the ms is densely illustrated and the fossil material is remarkably well described.

I have a set of remarks, mostly related to statistics and to few other points that could be considered to improve the ms.

MAJOR REMARKS:

M1* the principal components are extrapolated from the shape of individual specimens, I recommend to display minimum and maximum of shape variation on each PCs since it may better show the meaning of axes in terms of "morphological" variation. The same applies for the CVA.

M2* since the idea is to discover a grouping structure, the canonical analysis may not be appropriate since it is circular reasoning (you based your group on the way they differentiate on PCs, and of course, as a result, they will differentiate morphologically). Rather you might prefer to use gaussian mixture models or kmeans or partition around medoids to identify whether you have several groups or not...I also cowrited a paper some years ago with a Bayesian approach (see geneland or things I wrote in the morphometric book).

M3*The long description of shell morphology and shell variation would gain to be accompagned by a table where you might note which character are overlapping in morphology accross both species, and whether some characters are really specific.

M4*From what I saw in the text and from the analysis, it seems that sex dimorphism encompass largely interspecific variation. Why therefore not being more conclusive and say that these two species differ by so few things (or nearly nothing); note that the characters that diagnose the two taxa are also the more variable and vary importantly during ontogenesis or can be related to sex dimorphism (shape of the carapace margin, anal notch...: see for instance what happens in giant galapagos tortoises, especially in saddleback forms). It is a bit confusing then to poo the two species and to analyse them jointly. Alternatively, you may drop from your analysis things related with specific variation and concentrate only on one species.

M5*There are many things in the discussion that could appear before with the section results (which could be renamed "Variation of shell features"). I would rather concentrate the discussion on sex dimorphism and ontogenetic variation, and possibly interspecific differences. The other sections (middorsal ridges and keels, growth marks, radial striation) within the previous chapter (it is more a description than a discussion here).

M6*shape analysis:
- L. 742. It is unclear on what is regressed shape ? is it regressed on size, and then after is it a pca on residual variation ? What is the p-value refering to ? to the significance of the regression on size ? If so it seems that shape variation is not related to ontogeny ?
How sex were a priori defined on this plot if it is not by the shape of the structure ?
What about the two groups on PC3 for the vertical section ? why PC1 is interpreted as sex related but not PC3? I think it would be necessary to be more precise here because conclusion of the morphometric analysis are a bit tautological.

- fig 10.C, it is unclear what the authors mean by regression score, the way to obtain this score should be explained in the text. The construction of groups look rather ad-hoc, for instance smns17561 could be in group I or II, and the same could apply to V39/70. Here also, using partitional clustering could have been informative (eg. gaussian mixture models, kmeans, or other related methods...). Think that PC axes are in no way biological axes, they just represent major component of variation and covariation. Although I think there is clearly an inflation of variable by comparison to the number of individuals, it would have been good to provide what were the shape characters related to group differentiation by reconstructing extreme shapes along CVA axes. As for the CVA, the manova run on the groups was expected: it is a circular result (if you define the group on the based on their shape variation, you should expect to find significant differences in shape). I am not sure that these analyses are necessary. The CVA could be interpreted, if you compute mathematically the shape diagnostic features among groups.

M7* The methods used for geometric morphometrics are not enough explained in supplementary material.
- The location of landmarks and semi landmarks should be described by the mean of a drawing, or by the mean of a list.
- since there are potentially few individuals but large number of variables, it is not very surprising to see clear differences in canonical analyses. Can you explain whether you reduced shape space dimensionality prior to run the canonical analysis (how many PCs axes were kept ?).

OTHER REMARKS:

o1*The chapter method starts a bit abruptly, can you first explain the purpose of taking photograph and how you made photograph for most specimens rather than only discussing about the small.

o2*l. 150 and everywhere in the ms. I am not sure that we speak about ontogenetic age, the meaning of that expression is unclear to me. Maybe rather, you want to say a large spectrum of shapes ? I am not really sure that we speak about ontogenetic stage after hatchling or it requires to be better defined.

o3*l.678-679: rephrase a bit, I was not understanding that sentence.

o4*l. 687. "an earlier stage of hyoplastron formation". should be rephrased, I do not understand it.

o5*l. 176-177. a bit unclear, I would rephrase it. I was thinking that carapace stoped growing, not that ankylosis was.

o6*Ankylosis remark: Your observation is interesting, and I believe that ankylosis is not necessarily related to stop of growth (it may be the case in Terrapene, but not necessarily in other turtles: eg. Batagur, and certainly the case in some fossil such as Meiolanids :  bone recomposition is likely to occur even if the suture disappear). Therefore I tend to agree with your conclusion, one should not necessarily conclude that sex maturity is related to ankylosis and that carapace stop growing once ankylosed. In this case, you cannot cross the information of size and ankylosis to determine easily the sex of the turtles, and you may rely on shape (and its covariation with size).

o7*l. 275 to l.300. when you speak about growth in some body part it would be probably more informative to speak about change in proportions; indeed everyone expect that by the simple process of growth, measurements will all increase. (or at least and if it is the case, just state that the growth is isometric).

o8*When you first mention a taxon in the text, please add author and year (you do not need to list authorship of taxa in the bibliography: eg. Keuperotesta limendorsa ).

o9*Fig 8. there is no fig 8F (correct 8D).

o10*l.858. "see the secion shape analysis below" -> as for thue gular part, this section is not clearly identified in the text, it seems to belong to the same chapter.

o11*Discussion:
As I mentioned during the turtle evolutionary congress in Tokyo, the fact that carapace variation is rather important in this group and could be related to the ecology of Proterochersis. Proterochersis was likely more terrestrial than Proganochelys, it would be therefore expected that the anal region would be more impacted (reproducing on land imposes more important constraints for reproduction). Although, authors speak about gular region and possible fight. If they are right in their interpretation, it further suggest that these turtle were terrestrial. Gular fight or strong differentiation was never reported for aquatic species. Maybe that should appear in the discussion.

o12*supplementary material
p7.l7. sup mat 1, veritcal -> vertical
interscutal -> not sure that this word is used for turtle anatomy. It seems more devoted to acaralogy
extragularium and gularium as well are not commonly used for turtle anatomy

I am julien CLAUDE.
Institut des Sciences de l'Evolution de Montpellier. feel welcome to contact me if you need more info concerning any of my remarks.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: SHELL VARIABILITY IN THE STEM TURTLES PROTEROCHERSIS SPP.
Review round: 2
Reviewer: 1

Output:
Basic reporting: The changes introduced by the authors significantly improved the readability of the manuscript. It is now easier to follow the relation between some of the methods used by the authors and the interpretations of their results. As before, I added a few suggestions to the text. The authors have now also included their data in a more accessible form,which is very appreciated.
Experimental design: The methods used by the authors are much more clear now. Otherwise, I have nothing to add that wasn't said in the first review.
Validity of the findings: In my opinion the main problem that remains in this second revision is the interpretation of the results of the analyses of the caudal region of the plastron. Although in many cases it is possible to identify clusters in PCAs plot by eye, figure 10 A & B are not one of such cases. I have removed the colour and group ellipses from Fig. 10 (see caudal_pca.gif) and see no clusters. Qualitative identification of clusters is of course subjective; my personal criterion would be that the clusters must be immediately apparent. Going a step further, I scraped the coordinates of PC1, PC2, and PC3 from the plots in Fig. 10 A & B and ran two simple analyses with the partitioning around medoids algorithm implemented in the R package "cluster" v. 2.0.7 (the scraped data and an R script with all the code necessary are provided). In the first analysis I included all the specimens and set the k parameter (number of clusters to find) to 4. In theory, this analysis could have found the same groupings shown in Fig. 10A: group I, group II, and two putative juvenile singletons. The algorithm did not find the clusters suggested by the authors (see clusters_all.png). As this failure to replicate might've been due to the influence of the juvenile specimens, I ran a second analysis omitting V.39/34 and V.39/66 with k set to 2. This other analysis failed to recover group I and group II again. Instead, it found a cluster with V.39/70, V.39.71, and V.39/49 (all with positive values in PC1 and PC2), and another cluster containing all the other specimens.

As I cannot replicate qualitatively or quantitatively the groupings claimed by the authors, I'm afraid that I find their interpretation of the PCA analysis unconvincing and their overall conclusion about sexual dimorphism poorly supported.
Additional comments: Should the you want to use the results of the clustering analysis in their paper, you're welcome to do so, but I must add a note of caution: Partitioning cluster algorithms will always identify the number of clusters required (k) in empirical data, regardless of whether the data contains "real" clusters or not. Several statistical methods exist to assess the support of clusterings; my perception is that there is no clear clustering structure in the caudal region data.

The paper provides valuable new data and insights, and I hope to see it published soon with revisions to the PCA analysis and its interpretation.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: SHELL VARIABILITY IN THE STEM TURTLES PROTEROCHERSIS SPP.
Review round: 2
Reviewer: 2

Output:
Basic reporting: The revised version of the manuscript completely and satisfactorily answered all my comments and see no need for further review. Hence, I now recommend the acceptance of the manuscript as it is.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: No additional comments


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: SHELL VARIABILITY IN THE STEM TURTLES PROTEROCHERSIS SPP.
Review round: 2
Reviewer: 3

Output:
Basic reporting: The authors have answered several of my questions, but the answered raised the problem of a possible circular reasoning in the shape and statistical analysis. This should be taken into account. see the review in section general comments.
Experimental design: ok but see section 1. see the review in section general comments.
Validity of the findings: ok but see section 1 and think that anatomy can also speak, there is no superiority of approach between an anatomical exploration and morphometric and statistical methods. see the review in section general comments.
Additional comments: This MS is still interesting (nice description/comparison of the material) and I am happy to have interacted with the authors during the review process.
The authors have done important changes in their text, they answered most of my questions and the manuscript is much better but I still find things that must be improved in the shape analysis section to avoid circular reasoning; they also asked me to provide a few how to, which is provided. there are a few minor things to correct also with the new changes operated. I consider that the changes I am asking for are minor by comparison to what as been done since the last version, and I thank the authors for taking my previous remarks into consideration.

#Shape analysis and remarks to my previous review: starting from l.1136. points M1,M2, M6/7 (the most important to my opinion), points to be adressed in more details.

M1. We still hardly understand mathematically the relationship between PC axes and shape. What we ideally need is an illustration of what is actually ongoing on PC1 and PC2 or CV1, CV2 (see for instance Claude et al., 2003, Claude et al. 2004...and many other references available for other organisms). basically to obtain that:
for a PCA
1.compute the mean shape
2.estimate max and min scores on PC1, PC2
3. compute change on PC1 by reconstructing hypothetical shape on it for min and max score:
mean shape + eigenvector 1 * max (score PC1)
mean shape + eigenvector 1 * min (score PC1)
the same can be done on PC2
mean shape + eigenvector 2 * max (score PC2)
mean shape + eigenvector 2 * min (score PC2)

Doing so, you may have a clearer idea of what is described by PC1.
for the CVA (something that is equivalent to linear discriminant analysis), the procedure is described with R code here:

http://www.italian-journal-of-mammalogy.it/Log-Shape-Ratios-Procrustes-Superimposition-Elliptic-Fourier-Analysis-Three-Worked,77247,0,2.html

or in my 2008 morphometric book

There is a need here to rescale the discriminant functions since they are expressed in the discriminant space with the mahalanobis distance (not the euclidean one)

M2. the absence or presence of clustering on a PC plot does not mean that the data are actually clustering or not (you see just one plan and data here are highly dimensional). In addition clustering by hand or by eye on the first plan is rather subjective. To demonstrate any clustering in terms of shape, you should use partition clustering methods or eventually superimpose a hierarchical clustering onto your acp (upgma for instance). I prefer partition clustering. In the rebuttal letter, you asked the step by step procedure. That's not really difficult if for instance you opt for multivariate gaussian mixture modelling.
1. consider the scores on your first PCs (for instance summarizing up to 90% of variance) to avoid an inflation of variable by comparison to the number of specimen. save that in a table
2. download R and install Mclust library
3. import the table in R, assign it to the data1 object (with read.table)
4. then run mclust: mod<-Mclust(data1)
5. mod, the output will let you know how many groups you have and which gaussian mixture model it conforms.
6. if you want to check the classification, you can extract the object mod$classification which will let you know to which group belongs each observation. do not forget to cite references to Mclust in your text if you use it.

...you might be disappointed by the result if you put too much variables because in that case, Mclust may conclude that you have only one group (multivariate gaussian models may require too much parameters); this is why I advise to reduce the data to their first principal components of variation. you can also force Mclust to build two groups (option G=2) to see what it returns to you at the end (I would exclude the supposed juvenile here since we expect them to be not differentiated ni terms of sex shape dimorphism).

if you do not like Mclust, just have a look in Claude 2008, I provide an how to for kmeans (which is a simpler method aiming at maximising intergroup variation and minimizing intragroup variation). and if it is still not exactly what you are looking for just check what we wrote for geneland in systematic biology with Guillot.

M6/M7. shape analysis and possible circularity in terms of reasoning.

- shape against log size regression analysis.
Thank you for clarifying this point:
Here also, since in the paper you describe ontogenetic trends, it would be good to reconstruct the shape using the regression parameters rather than to display individual shape.
for that your shape X = A log(size) +  B
X being your shape expressed as a vertical matrix, A and B  being vectors of regresion parameters.
to reconstruct shape variation due to size, you can reconstruct two shape: the one for the smallest and the one for the largest individual in your set. It will show you which shape parameters are described by the multivarite regression.

"- since there are potentially few individuals but large number of variables, it is not very surprising to see clear differences in canonical analyses. Can you explain whether you reduced shape space dimensionality prior to run the canonical analysis (how many PCs axes were kept ?)."

We do not know how to reduce the shape space dimensionality in MorphoJ. If the Reviewer considers that important and provides us with a step-by-step instruction of how to do that, we may include this.

Discrimination, sex determination, MANOVA and circular reasoning.
This is certainly the most important point to address to my opinion.
Thanks to your explanation concerning sex assignment, I know now that you are basing your grouping structure on shape (PC differentiation). Therefore, it is not surprising to find a linear combination of variable discriminating the groups (your answer to my remark about the sex determination is not equivocal since you say that "The sexes are marked based on PCA clusters"). Therefore and indeed, we expect to find a significant p-value for shape variation explained by size in the manova and we expect to find a nice differentiation on the LDA. Since this is tautological, I think you should drop the LDA and MANOVA.

If you opt for keeping the CVA, I think the problem of number of variable contra number of observation is an important point to consider: when you have plenty of variables and few individuals you can easily obtain a discrimination that is just dependent of the sampling and that do not reflect reality. To reduce shape dimensionality (but it may not apply anymore since the sex were obtained from morphometrics), you can concentrate only on the scores of the first X PCs describing your shape and discard the one contributing for a very small percentage. With your data, I would try to gather 90 of shape variation and drop the next PCs. Note that procrustes manova is also biased since the number of degrees of fredom increase with the the number of points.
To come back on the sampling artefact, you must check whether your specimens are well reclassified by performing a one leave out cross validation on your CVA or LDA (it is a jacknife) and it is explained in my 2013 paper in Hystrix (you have a tutorial in the supplementary material of the paper and everything is online).
-------------------------------------------------
#New minor things :
on1. since you explain now how you buid your 3D models, you should provide the reference for agisoft photoscan (not only for meshlab and visualSFM).

on2. reference to morphoJ should be restricted to the paper published in 2011 (the 2009 paper is not specific to that soft).

Julien CLAUDE, ISE-M
Université de Montpellier


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: NON-INVASIVE MONITORING OF GLUCOCORTICOID METABOLITE CONCENTRATIONS IN URINE AND FAECES OF THE SUNGAZER (SMAUG GIGANTEUS)
Review round: 1
Reviewer: 1

Output:
Basic reporting: The basic reporting of the manuscript by Scheun et al. is mostly clear and coherent. The structure of the manuscript is sound, and the contents are mostly easily absorbed. The raw data has been made available.
Experimental design: The experimental design is sound with respect to the aims of the study. The low number of subjects (3) mixing both sexes (2 + 1) undermines the study somewhat, but I know from personal experience how hard these studies can be to set up and justify for ethics committees. The research question is somewhat clear, but the precise hypothesis could be more explicit (what makes the ideal assay?). Moreover, the methods need a bit more detail for someone to be able to replicate them.
Validity of the findings: The findings are fairly clear, although some of the data analysis seems excessive (for lack of a better word). The use of arbitrary numberings for fecal/urinary samples, as opposed to providing timing is weird and leads to some odd analyses. Given that this is a study that will serve as a future guide for researchers studying stress in sungazers, I am also missing some clear recommendations in the conclusions.
Additional comments: Scheun and colleagues have made a thorough investigation/validation of how to non-invasively assess stress in sungazers. This experiment is key for future studies looking into factors affecting stress in the species. There is, as the authors state, much less work done on reptiles than there is for mammalian species, and with their somewhat cryptic and passive behavior, biomarker-based assessments are all the more important.

Reading the report you get the sense that the authors are somewhat impatient in getting these findings out the door; no doubt because they have other sungazer studies planned. Whereas the experiments seem solidly designed and well-conducted, the reporting could be better. The introduction needs work, the methods are missing some information, the purpose of some of the data treatment is unclear, some of the results are reported in odd opaque ways, and the paper would really benefit from some clear recommendations included in the conclusions.

Specific comments (ordered by section):

Abstract
Line 25: Based on one male and two females, no conclusions with respect to sex-specific effects can be drawn. Substitute “was observed for both sexes” with “was observed in all subjects.”

Introduction
Line 45: I realize that the frequency of studies in reptiles is lower than for most mammalian species but calling a 14 years old paper “recent” and an 18 year old one “new” is pushing it. Find newer references or rephrase the sentence.
Line 50: This sentence needs more context. We have trouble studying them because ... we cannot find them?
Line 64: To my knowledge, GCs do not affect cardiovascular activity (depending on what is meant by enhance, I suppose) and the references do not support this statement.
Line 70: “...monitoring GC concentrations in e.g. endangered species can therefore not only assist in defining the presence and effect of local stressors, but also provide an argument for appropriate conservation actions if necessary.” What does this sentence mean? Rephrase for a clearer message.
Line 82: What is meant by “respective” here?
Line 96: How does its burrowing preference “add to” its genetic distinctiveness?
Line 96: It is not number 19 in total; it is in place 19 among the threatened ones. (What an odd factoid...)
Line 98: Why “despite?” Are not endemic creatures more vulnerable to habitat destruction as a rule?
Line 100: I am assuming that pet and medicine trades are not indirectly affecting the animals, but that sungazers are sold as pets and used in traditional (?) medicine? This sentence needs work.
Line 106: What determines the suitability of an assay in this regard? What, exactly, did the authors set out to find? What are the hallmarks of an ideal assay in this context?

Materials & methods
Throughout: Units should be separated by number with a blank space (SI standard). For centrifuges, “g” is used as a unit and consequently the multiplication sign should be removed.
Line 117: Could the animals see one another?
Line 119: Substrate, both for the cage and with respect to the artificial burrow should be listed.
Line 120: What is listed in the parenthesis is not light intensity (which, if measured, should be listed in lux), but the light regimen.
Line120: The humidity data seem off. Average +/- 1 SD should for an ideal distribution encompass 68% of data. Yet, here it seems to encompass 100%. Either the range is listed incorrectly, or the SD is calculated in a truly weird way.
Line 134: Were samples collected hourly around the clock? The raw data sheet only lists sample collections in the time interval of 07:00 and 15:00. Do sungazers only poop during working hours?
Line 136: There is no mention of discarded samples in either results, nor in the raw data. This is important to list! Particularly with respect to the arbitrary ordering of samples.
Line 139: The listed ACTH dose is incorrect/makes no sense. Synacthen comes in ampoules of 250 µg, which means that the authors used about 500 ampoules per animal if the dose was 0.433 mg/g... 1-2 IU/kg is more reasonable, but it is highly inexact. What was the actual dose? Two of the listed references – Kindermann et al., Graham et al. – report the same bizarre dose (some weird math has been going on here) whereas Cartledge & Jones use a fixed dose (independent of body weight) of 25 µg (= 2.5 IU). Narayan et al. do not use ACTH in their study or even mention it!
Line 149: Sample treatment could be better explained. Moreover, the reference – Feiß et al. – does not explain the method, but in turn references Heistermann et al. (1993).
Line 166: What is meant by “sensitivity” in this context? LLOQ? The authors need to properly define this.
Line 166: Detection limits, Intra/inter-assay CVs, and parallellisms for the four assays are well suited for being reported in a table.
Line 184: Was 100% defined relative to (the absolute) zero or to the detection limit?

Results
Line 207: “The average defecation rate (number of defecations per time unit) for urine and faeces exceeded 37 hours per defecation event for the three study animals...” The authors start with a perfectly sensible way of expressing defecation – “number of defecations per time unit”, then promptly throw it out the window and report “37 hours per defecation event.” What does that even mean? Is that the average time between two defecations? If it is, does this account for “non-fresh” samples being thrown out? According to the data in Table 1 these variables are normally distributed. Defecation rate has been highly variable in the reptiles I have worked with – are the authors sure that data are well-described using means and standard deviations? (The raw data sheet also suggests sungazers are fairly irregular...)
Line 209 & 254: What can we learn from the subject-level tests? The authors have only three subjects and can thus not establish a good population (even if they had all been of the same sex). What would be the interpretation if there were significant differences? This feels like a hypothesis-less hypothesis test.
Line 213: What do we learn from the MAD values? Are we looking for a low or high value? If there is a circadian rhythm to uGCM or fGCM we would expect this to show as increased MAD. So is that a bad thing? The data are not presented in full either. It is as if the authors themselves do not know what to make of it.
Line 222: What are we looking for when comparing assays? Highest signal or lowest variability?
Line 230: “...both the 5α-pregnane-3β-11β-21-triol-20-one and tetrahydrocorticosterone showed the highest response...” No, one of them showed a higher signal than the other.
Line 251: What can we learn from these correlations? Which samples are correlated with one another? (And importantly: Why?!) The urine and fecal samples are not obtained at the same time. If urine sample 3 and fecal sample 3 are a matched x-y-pair, we are comparing samples that can be as much as three days apart in time. What is the point here?

Discussion
Line 259: “...the validity of two EIAs, for monitoring a physiological stress response in the faeces and urine of S. giganteus, have been confirmed...” Which ones? And based on what? This comment is getting ahead of itself.
Line 262: “The defecation rate of a species is a relevant estimate for the delay in hormone metabolite excretion in faeces...” Irrespective of intestinal passage time? Explain. Also, the reference – Palme et al. (1996) – specifically does not discuss defecation rate, but spends quite a lot of time discussing intestinal passage time.
Line 280: “...it may be advisable to interpret a likely ”cause-and-effect” relationships over a longer time period.” I do not understand what the authors are trying to say. Sentence should be elaborated on.
Line 284: “The MAD values for the four EIAs used in the fGCM analysis indicated low levels of variation from the predetermined baseline values and thus EIA stability.” What is a low MAD value? Is 5% low? 10%? What is a good MAD? And what is meant by “EIA stability.”

Conclusions
The conclusions should list clear recommendations to researchers looking to investigate stress in sungazers. What assay should be employed and why? Should they collect fecal samples, urine, or both; and why? How long after a stress-response should they expect to see an elevation in their chosen assay? What could possibly confound their analyses and interpretations of these analyses?
Figures 1 & 2: These figures are weird since the samples are along an arbitrary x-axis. For example: The fGCM data points at x-axis position “1” correspond to 24 hours after ACTH injection for subjects F1 and F2, but to 105 hours after injection for M1. Why are these three points grouped together? The x-axis should show the time and any discarded samples need to be acknowledged.
Tables 1 & 2: Are the values really so accurately obtained as to be usefully reported down to two decimal places?


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: NON-INVASIVE MONITORING OF GLUCOCORTICOID METABOLITE CONCENTRATIONS IN URINE AND FAECES OF THE SUNGAZER (SMAUG GIGANTEUS)
Review round: 1
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: Line 116: The date of study is future dated !!!
Line 129: Please provide a photo showing the study species and the excreta with distinction between urine and faeces shown.
Line 139: Did the authors consider sampling the lizards using control stressors such as manual restraint or saline only injection?
Validity of the findings: Line 139: It cannot be confirmed without control groups whether the responses observed were due to the ACTH or the needle or handling. Please clarify.
Additional comments: A very interesting and important study validating stress hormone evaluation in an endangered reptile species, the Sungazer.  I recommend acceptance with minor corrections.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: CHARACTERIZATION OF THE MITOCHONDRIAL GENOME OF ARGE BELLA WEI & DU SP. NOV. (HYMENOPTERA: ARGIDAE)
Review round: 1
Reviewer: 1

Output:
Basic reporting: Only few corrections/comments in the attached ms.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: No additional comments


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: CHARACTERIZATION OF THE MITOCHONDRIAL GENOME OF ARGE BELLA WEI & DU SP. NOV. (HYMENOPTERA: ARGIDAE)
Review round: 1
Reviewer: 2

Output:
Basic reporting: This manuscript determined one newly mitochondrial genome of the new species Arge bella, presented comparative analyses of this mitogenome with the other known symphytan mitogenomes and presented a phylogenetic analysis of Symphyta based on the mitogenome sequences. The manuscript is clearly written.
Experimental design: There seems to be no methodological problem.
Validity of the findings: There are important results for the field and the findings are well constructed by authors. The findings have been discussed and supported by relevant literature sufficiently.
Additional comments: Here, the manuscript presents the characterisation of the mitochondrial genome of A. bella for the first time. Then the authors aimed to comparison of various genomic features against other reported symphytan species. The most interesting evidence is the presence of rearrangements in tRNA genes. The manuscript presents a newly constructed phylogenetic tree using available symphytan mitochondrial genome to validate the phylogenetic position of the species (A. bella). Some minor changes or comments are listed below:
•	Line 60: The order of references should be updated. For example, Dowton et al. 2009a should be used at first referenced, not Dowton et al., 2009b. This problem should be checked throughout the manuscript.
•	Lines 62-63: I could not see the family name Heptameliidae in ECatSym database as well as the current literatures.
•	Line 164: The authors should use "unlinked" branch lengths in the analysis with PartitionFinder. When we prefer "linked" branch lengths, we're assuming that the relative rates of evolution among lineages in the tree are constant across partitions. However, with "unlinked" branch lengths, not only can the partitions have different overall rates of evolution, but also the relative rates of evolution among lineages can differ between partitions.
•	Lines 247-249: The authors should explain the likely reasons of this failure together with the relevant literature.
•	Line 263: When looking Table 2, Leu, Ile, Phe, Met, Ser seem to be most frequently used amino acids rather than indicated by the authors.
•	Line 304: When examining the related figure, it seems to have three domains. Was it wrongly denoted, or not, please give more explanation about this new domain. As taking into consideration the relevant literature, the predicted secondary structure of insect rrnS gene seems to have three domains.
The remaining minor corrections are shown on the manuscript.
In my opinion, the manuscript could be published in the journal PeerJ after minor revision.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: CHARACTERIZATION OF THE MITOCHONDRIAL GENOME OF ARGE BELLA WEI & DU SP. NOV. (HYMENOPTERA: ARGIDAE)
Review round: 1
Reviewer: 3

Output:
Basic reporting: Du et al. have sequenced the mitochondrial genome of Arge bella and compare with others.
Totally the paper has been analysed and written in good order. it is including new information of mitochondrial genome of Arge bella. The hypotheses of paper is unclear and it need to explain clearly in the last paragraph of INTRODUCTION, especially when the paper is a comparative study (Just the text needs to revise)
Experimental design: It is an Original primary research and the METHODS AND MATERIALS have been clearly explained and designed.
Validity of the findings: This paper give new information about mitochondrial genome of Arge bella.
Additional comments: There is a major scientific question that should be reconsider by authors. In the title, Arge bella was mentioned as new species (sp. nov.). It means this is the first time that this name used and author discussed about its taxonomical status for first time. But in page 4 line 179, this species was referred to "Arge bella Wei & Du sp. nov." if Wei & Du have described this species before this paper so "sp. nov."  should be removed from title otherwise line 179 should be revised.

in Fig. 7:  Generally values of Bayesian posterior probabilities were mentioned in the range of 0 to 1. I suggest authors follow in this way.

In Tab 3. I suggest the column of Anticodon replace with Codon
In Tab 3. I suggest J and M replace with H (Heavy) and L (Light)


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: OPTIMAL CONTROL OF IRRUPTING PEST POPULATIONS IN A CLIMATE-DRIVEN ECOSYSTEM
Review round: 1
Reviewer: 1

Output:
Basic reporting: In this manuscript, Holland and colleagues expand a previous model of consumer population dynamics with pulsed resources the authors investigated in 2015 (Holland et al. 2015) in order to study the optimal control of irrupting pest population (case study
being the broad-scale control of house mice outbreaks in New Zealand).

The authors convincingly show that the control level (*i.e.* the number of baits) impacts both the plague size (*i.e.* the "highest mouse density during the plague period") and the plague time (*i.e.* the "proportion of time during which the mouse density is above the plague level") whereas the timing of annual control only affects the plague size. Moreover, the authors demonstrate that alternative strategies with similar cost such
as a biannual-seedfall driven control can have similar or better results.

According to me, the manuscript is very clear, well-structured and scientifically
sound. I only have minor comments.
Experimental design: Overall the methods are very well explained, the authors did a great effort to
detail the model as well as its underlying assumptions. Below are a couple
of suggestions:

- Equation 1: I think B should be B(t) as it is time-dependent.
- l. 150: I would explicit the total mortality rate.
- l. 154: in 2015, the authors explored 4 functional responses, I suggest they
mention that based on their previous study they chose Holling II.
- regarding the bait, I found it hard to picture how the unit used relate to the unit
for mice
- l. 192:
  - I would mention that it is assume to follow a Normal distribution
  - why using a standard deviation of 1 instead of the standard deviation of the time series?
- l.194 I would write "Orongorongo Valley (hereafter OV)"
- l. 206: I would stress out that plague here does not have a specific biological
meaning (unless I'm wrong), it is rather a convenient reference point to compare scenarios.
Validity of the findings: To me, findings are valid and unambiguous. I have two comments:

- Table 2, caption "[...] the minimum expected plague time and plague years
across the different regimes are shown in bold text." Why not doing so for the plague size?
- Figure 1, bottom panel: tick labels are missing.
Additional comments: I would change a few sentences in the introduction and in the abstract to better introduce the example that inspires the model. If I am right, the model is inspired by the house mice dynamics in New Zealand but is thought as a general one. I think this is fair, I would however make this slightly more explicit as I far as I understand, the model has only been validated on this case study.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: OPTIMAL CONTROL OF IRRUPTING PEST POPULATIONS IN A CLIMATE-DRIVEN ECOSYSTEM
Review round: 1
Reviewer: 2

Output:
Basic reporting: This manuscript is tightly written and quite clear in outlining modifications to the underlying seasonal mast-driven mouse model first described in Holland et al (2015), with one exception: the double set of inequalities shown in eq 4 seem impossible to satisfy. Perhaps this reflects a typo? The extensive literature cited section is appropriate and well-linked to the text. Figures are clear and easy to follow, as are the tabular data. The results are well-linked to objectives stated in the introduction.
Experimental design: This ms reports on applied population control extension of a previously published model of stochastic seasonal mouse dynamics in New Zealand beech forests. Objectives were to identify the most effective combination of timing and minimal (yet effective) application of pesticide to prevent house mouse outbreaks and their consequent damage to beech forests. Rodent control is an applied ecological problem of considerable concern, but is rarely based on bottom-up driven models of convincing robustness, so the modeling work fills an important gap in the literature and will no doubt be widely cited. The modelling work is based on straightforward modification of a plausible and well-validated consumer-resource model published 3 years earlier. While code was unfortunately not included, my judgement is that it would be simple to replicate the model.
Validity of the findings: The conclusions seem to be well-justified, given the well-validated empirical model framework. My only editorial suggestion is that it would be helpful to clarify why any population density above the median of 2/100 trap nights is defined as a "plague" instead of simply being above the long-term average. It also wasn't clear why the authors restrict their attention to applying pesticide just once a year or once every 2 years in a single massive dose rather than in multiple smaller doses triggered by biomonitoring of either beech mast or mice. In other words: why just these control measures?
Additional comments: I congratulate the authors on a well-formulated and useful modelling paper. I'm sure it will be well-received.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: CLIMATIC NICHE SHIFT AND POSSIBLE FUTURE SPREAD OF THE INVASIVE SOUTH AFRICAN ORCHID DISA BRACTEATA IN AUSTRALIA AND ADJACENT AREAS
Review round: 1
Reviewer: 1

Output:
Basic reporting: There are several sections of the manuscript that could use judicious editing for clarity, including the Introduction and the Conclusions, which seem garbled in the first few lines.
And the authors seem to have an aversion the word "the." Many times while reading, I was halted in my tracks for it's lack. The judicious use of the article would greatly enhance clarity.

Specifically:

In both the abstract and the introduction you state that Disa bracteata is considered an environmental weed or a naturalized species. Weeds are generally considered to be noxious while naturalized species or not. This is an important distinction. Please clarify what you mean. Is it a matter of where it occurs? Perhaps it is weedy in some places but not in others…

In the first paragraph “invasive,” “naturalized” and “weedy” are not well delineated. This could be clarified in the manner provided below:

Line 38 “In Australasia introduced species are in essential problem and the number of introduced plants exceeds 28,000. The subset of them have become naturalized… A smaller subset have become invasive, and the expansion of exotic weeds incurs significant costs related to their eradication.“

Line 43 to 44 should read “control the spread of certain species and use various methods to undertake risk assessment“

Line 45 “trough” should be “through”

Line 47 should read “...to study the case of the invasive orchid species ...“

Line 50 through 53 the species is classified as an environmental weed or naturalized species based on what? Does it depend where the species is found? This needs to be better defined.

Line 66 through 67 please specify where you are conducting your research the title states Australia, which would be in the invasive range of the species.

Line 104 to 105 clarify that 20% of the data or set aside to be used as test points.

Line 122 please clarify the variables used for your principal components analysis

Line 130 to 132 should read “the final set of the most important and uncorrelated variables included eight of the original 49:”

Line 135 Should read “The calculated value of the area under the curve”

Line 142 should read “...uncorrelated variables and model in which climatic factors were exclusively analyzed...”

Line 143 should read “The only difference concerns the transitional zone ...“

Line 144 “between the western and eastern cape in Africa, and the Nullarbor Plain in Australia”

Line 145 should read “was not indicated as suitable in the model based on climatic factors, whereas the second one was shown as suitable…”

Line 161 change and invasive range to the invasive range

Lines 183 to 192 beginning with another interesting result… To the end of the paragraph. This section seems more suitable to the discussion then to the results section

Line 210 there are invasive or kids in both Fiji and Florida. The ones in Fiji are also terrestrial, though they occur in forested habitats.

Line 211 should read “The invasive success of D. bracteata has not been thoroughly investigated, and the mechanisms of this phenomenon remained unclear.“

Line 216 change fungi to fungal

Line 224 should read “Generally, this is not beneficial for genetic variability, however it is advantageous to produce a large number of seeds.”

Line 227 should read “seems to be a less important trait as many successful invaders are characterized by an efficient vegetative reproduction. This is frequently the only mode of reproduction for some invasive species. Ideally, even an invasive species will couple vegetative propagation with the occasional sexual reproduction to add the ability to respond to a suite of selective pressures.”

Line 234 delete "for example"

Line 244 capitalize south

Line 261 “In the case of Disa there seems to be a significant difference between the climate of occupied habitats in Africa and Australia. When Africa and Australia are compared, the latter split into two groups.”

Please clarify lines to 267 through 269. I think what you were trying to say is that when a new niche is occupied this is an active process and maybe linked to novel adaptations which may not be discovered during the study itself.

The conclusions need to be entirely reworked, particularly the first two lines. I'm not entirely sure I understand what you are trying to convey here.
Experimental design: I thought the methods used were appropriate, and well substantiated by the citations included.

I would like to have seen what variables were used in the Principal Components Analysis.

Also, the range maps are difficult to read, with the model and test points indistinguishable from the background. This makes it impossible to visually evaluate model fit.

Cartographically, they are inadequate. There is no compass rose or other directional indication. In the South African models, the geography is indistinct, with no attempt to clearly identify the geographic boundaries. There is no context for the reader to evaluate the models.
Validity of the findings: I think that the conclusions are valid - however, the way they are presented in the text is a bit confusing. Some of the text in the Methods section seem more appropriate to the Discussion, as noted above.

The range/habitat results should be clarified - as presented in the text they are a bit muddled - especially because no attempt is made to identify the regions they indicate on the models they present. In other words, there is no cartographic evidence available to evaluate their interpretation of the models.

Also, the inference of a niche shift in the invasive range seems intriguing, but the supporting evidence is not well established. In particular, a better explanation of the results of the Exact Test, and the bearing this has on the Koppen-Geiger shift, should be undertaken.
Additional comments: No additional comments


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: CLIMATIC NICHE SHIFT AND POSSIBLE FUTURE SPREAD OF THE INVASIVE SOUTH AFRICAN ORCHID DISA BRACTEATA IN AUSTRALIA AND ADJACENT AREAS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The English needs to be improved.
The aims and hypotheses need to be stated - the basis of the study was not clear.
I provide detailed comments below.
Experimental design: The research question was not well defined.
The methods were appropriate but their use was ambiguous.
I provide detailed comments below.
Validity of the findings: The data were robust, although their interpretation was unclear.
The conclusions were not well stated.
I provide detailed comments below.
Additional comments: This manuscript investigated the environmental niche of Disa bracteata, one of the few orchid species to become potentially invasive in Australia outside of its native range, South Africa. For this, the authors compiled a database of all known records for D. bracteata and used a Maxent framework to model its niche under present day conditions and under different climate change scenarios. The authors used a variety of environmental variables and constructed reliable niche models of the distribution of D. bracteata. Overall, I thought that the study was interesting in that D. bracteata is a “weedy” orchid and that climate change might influence where it could occur in future. However, this manuscript has a number of limitations, most importantly that it lacks a proper research question. Also the link with climate change is unclear i.e. why study the niche of this orchid under climate change scenarios? As a result the implications of the study are unclear. There are numerous lapses in the writing and presentation of this manuscript, which would need to be improved. The ENM approach needs a better justification – why were so many variables included prior to the Maxent variable selection process. Not all variables are equal a priori. This would affect what variables are selected to begin with. I recommend a hierarchical method of variable selection whereby highly correlated variables are removed (>0.7), then examine the relationships between the remaining variables and see if they are ecologically relevant. Many soil variables were included, but no geological substrate variables. Including many soil variables would not necessarily improve Maxent performance. Geological substrate is an excellent predictor of plant distributions and should be included in niche models of all plants. The future climate change scenarios are not well explained, and the methods the authors used to estimate the niche of D. bracteata under climate change is unclear. The authors state that they averaged the climate change models for each RCP. How many models were included for each RCP? These future scenarios often differ in their underlying code and ability to predict environmental change, even within a given RCP. This does not mean there will be bias from one particular model as the authors claim, it would depend on the justification of using a particular model (or models). Therefore, averaging them is not appropriate if you want to make predictions on future influence of climate change on species distributions. They would have to be examined individually. I provide some specific comments on the text below.

Abstract
The abstract needs to be re-written. Environmental niche modelling has been used widely over the past 20 years to investigate the suitable habitat for many invasive and potentially invasive taxa. Why study Disa braceata? What do you mean by “in an aspect of conservation”? How was future expansion quantified? How many climate change models were used? The concluding statement is overstated – D. bracteata occurs over a wide range of conditions in South Africa and can self-pollinate and reproduce clonally. That it encounters similar habitat in Australia and may expand in future is not so profound.

L35: A citation from 2001 is not recent.
L38: This needs to be re-written.
L44-46: They are not a “promising technique” - the use of ENMs has been extensive in invasion biology for the past 20 years.
L47: The link with D. bracteata is not clear. Just because it is a “weedy” orchid, does not mean that it merits thorough investigation.
L86-87: What other data are you referring to here?
L66-68: What is the research question?
L77-78: What do you mean by “precisely placed on the map”?
L93-94: What do you mean by “clipping using a rectangular mask”?
L96: Add ‘for’.
L98-100: It is not clear what these steps mean or do to the data.
L103: There are more general references for the reliability of Maxent in the literature.
L108: The jump to climate change scenarios is not clear.
L111-115: State exactly what models under CMIP5 you used. Did you use every model? While some future scenarios are similar (e.g. CSIRO and HAD), each model is different in its assumptions and underlying code. Therefore, aggregating them and averaging their influence on a species’ niche under each RCP may obscure this.
L115-116: What are “continuous grids”?
L117-125: More explanation is needed here. This is presumably to test for the differences between South Africa and Australia. Do you also use niche equivalency to test for differences between current scenarios and future climate change? What is a “bias metric”? Why was a PCA used here?
L176-205: You should explain better in the methods section what each of these statistics calculate. Then in this results section outline only the results. Some of the speculation here belongs in the discussion section.
L208: Orchids are often “weedy” in the sense that they often occur in ephemeral habitats. What you mean is that they are not normally classified as invasive.
L213-217: Many orchids automatically self-pollinate and mycorrhizas are generally ubiquitous in the soil. It depends on the species whether they have adapted to particular mycorrhizas.
L224:-232: This section needs to be re-written. There are a lot of different concepts introduced that are not well-epxlained.
L265: Can human introduction into Victoria be discounted?
L271-277: This conclusion needs to be re-written.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: CLIMATIC NICHE SHIFT AND POSSIBLE FUTURE SPREAD OF THE INVASIVE SOUTH AFRICAN ORCHID DISA BRACTEATA IN AUSTRALIA AND ADJACENT AREAS
Review round: 1
Reviewer: 3

Output:
Basic reporting: April 17th, 2018
Dear Prof. David Roberts
PeerJ Editor
The manuscript “Climatic niche shift and possible future spread of invasive South African orchid Disa bracteata in Australia” explores the potential expansion and habitat shift of an herbaceous weed. The authors have selected for this study an unusual orchid species that, unlike most species in the genus and the family, is of concern as an invasive alien plant in Australia and neighbouring islands. I trust this manuscript, if accepted for its publication in PeerJ, can contribute to a better understanding of how biological invasions evolve, providing to the readers of this journal a novel and more dynamic insight on plant invasions, by considering not only the current climatic scenario, but also edaphic parameters and some putative climatic scenarios to occur.

Despite of these positive aspects, I also have found some issues that should be clarified or improved.

Firstly, I suggest a modification of the title. This should reflect in a better extent which are the results here obtained. Contrary to the expectations, even when only Australia is mentioned in the current title, the manuscript explores the putative change in distribution of this plant in its native range, and in a broader invaded range (which includes Australia but also other neighbouring big islands). Indeed, this change could increase the interest of a wider public to read the paper because it covers a broader geographic scale.

Additionally, the English grammar along the manuscript is sometimes inaccurate, particularly the repeated omission of some articles, conjunctions and prepositions, which can hinder the understanding of the text. Other minor issues are reported in the list below.
In summary, I recommend this manuscript to be published in PeerJ, but only after the issues here mentioned are addressed by the authors, especially the two above mentioned. Besides, I am deeply interested in receiving the appropriate feedback on the authors’ criteria, and the actions derived from this and other reviews of the manuscript.
Experimental design: In this work, the authors assessed the potential ability of this particular plant to modify its habitat requirements in the invaded area, and they used this information to validate its potential distribution under different hypothetical climates to come. To this end, the authors performed a set of analyses that to my judgement are appropriated and sufficient to achieve their goals. In addition, they selected for this aim a very reliable source of information, including Chelsea, which resolution for this kind of analyses is more relevant that other alternatives (e.g. BioClim). In my criterion, there is not a clear justification for excluding the edaphic variables in the estimation of the potential distribution of this species under the assumed future climatic scenarios. I do not find a convincing explanation in the text about this. Curiously, the authors firstly included a group of edaphic variables, and in fact, later they found that three of these non-climatic variables are even crucial for the best-supported model. These variables were part of the set of most important and less-correlated variables to explain the distribution of this orchid weed. Nevertheless, the edaphic variables are simply omitted from the analyses that were based on the hypothetical future climatic scenarios. In this sense, I believe that there is not a clear explanation about why this procedure was followed. According to the authors when the figures 1 and 2 are explained, the suggested distributions following the model that includes and the one that excludes the edaphic variables are very similar (see the figures above mentioned). I assume this could be the explanation, but this is not obvious to me, and on the other hand this a not a solid justification for such procedure. In my opinion, that explanation is a very subjective statement, because in my criterion there is a certain area in each case for which the chance of occurrence of this species differs between the compared models (which occur for both the native and the invaded zones).
Validity of the findings: I consider the impact and novelty of the manuscript could be high due to the need to control this weed which expansion could have consequences not well understood for the local orchid floras in the invaded area. Data is robust, and its manage and analysis appropiate. The issue about the ignoring of the edaphic variables should solved, by including them or explaining in detail the reasons why they were not considered in the rest of the analyses (see comments). The discussion is in general appropiate but it could be improved by being a little less categorical in some points.
Additional comments: REVIEW OF THE MANUSCRIPT “Climatic niche shift and possible future spread of invasive South African orchid Disa bracteata in Australia”

General comments:

Please consider to include a broader geographic reference in your title. Note that your analyses are focused not only in Australia, but also in a broader range of the invaded region, and also in the native range of this plant. For me, maybe the aspect of higher concern is the next point. In my criterion, if the edaphic variables were found as being important in explaining the current distribution of this plant (which is explicitly mentioned in the manuscript, when you report the best fitted model, and all the variables that were analysed), then these edaphic variables should also be considered in the estimation of the potential distribution of this species under future climatic scenarios. I think it is biased to estimate changes in the species range for the next decades when the group of the edaphic variables is ignored. I assume that these variables will not change substantially in time, in the same time scale clearly. If this is not sure, please provide references supporting the exclusion of the edaphic parameters from the analyses.
In the Discussion you should explain that, considering this is one of the few orchid species completely pollinator-independent for seed production, there is no need to incorporate the potential distribution of any pollinator to get a more or less realistic potential distribution of the orchid. In contrast, the role of mycorrhizal fungi in this case is probably so determinant for this species as for most orchids. Nevertheless, you also mention that in the particular case of this species, the fungi are probably less limiting due to the use of a broad spectrum of fungi as mycorrhizal, or due to the exploitation of one particular or a few fungi species that are very abundant and well-distributed in its range. A short comment about how feasible or difficult is to obtain data about this kind of fungi to estimate the orchid distributions could also be mentioned (with the needed references). These two topics could enhance the relevance of your work by explaining why there is no need to consider the mutualistic partners of the orchid in the analyses you performed, and why the inclusion of data from the fungi should be considered in further studies.
I think the language, although good in general, should be improved to gain in clarity and propitiate an easier comprehension of the text by a broad spectrum of readers. Specific issues in this sense are indicated below (texts to be removed or included are always between quotation marks).

Specific comments:

Line 31: I think you could clarify in this point if those South African marginal habitats are also occupied by the species of interest.

Line 38-39: I suggest to replace “In Australia invasive species are essential problem and number of introduced plants in Australia exceeds 28.000” by ““In Australia, invasive species are an essential problem, and the number of plants reported as introduced in this continent exceeds 28.000 species”

Lines 40: Please replace “threat to rich, endemic flora” by “threat to the rich and highly endemic Australian flora”

Lines 47-50: I am afraid some information is missing here. Perhaps D. bracteata is the only species occurring out of the Sub-Saharan range of its genus. If that is the case, or even if not, please consider to rephrase this sentence. The different parts of it are not well connected.

Suggestion: “In the present research, we applied this approach to predict the future distribution of the invasive orchid Disa bracteata Sw., which is listed in the Global Compendium of Weeds (site address) despite of being part of a genus confined to only the Sub-Saharan portion of Africa (please include a reference supporting this)”.

Please be sure of rephrasing “the case of invasive species”. This has no sense to me if you do not include the particles “an” or “the”.

Lines 55-60: These two sentences are not well connected. Maybe you should introduce Australia as the region where this species was reported by the first time as a naturalized orchid weed. After that, mention the situation of the non-native flora in Australia (including the invasive species).
Line 76-78: The information provided in these two sentences is essentially the same. Please simplify the text by including the GBIF localities as a part of all the locations that we used. You could use this or a similar phrase: “including GBIF localities with a precision lower than 1000 m”.
Line 98: Please replace “applying following criteria:” by “applying the following criteria:”
Line 105: Please include a comma after the world option.
Lines 111-113: Redaction here could be improved.
Suggestion: “We only consider the models covering all four representative concentration pathways for the year 2070 (average for 2061-2080). These models were obtained from www.worldclim.org (Appendix 2)”.
Line 114: What in each case? Could you be more explicit? I think this information is quite relevant to understand the methodogy.
Line 114: Something is missing between “in” and “particular”. The sentence have no sense to me in its current version.
Line 116 (end): Please cite at least a reference at the end of this sentence. You should cite a study where this method was implemented by the first time or at least recently implemented.
Line 119: Readers should be interested in understanding the means of these two letters. Please include a brief explanation about it.
Line 124 Please note that the use of the conjunction “or” introduces uncertainty in this context. What did you use “in each case”?
Line 131: Please replace “eight from the originally included 49:” by “eight from the originally included 49 variables:”
Line 140: The distribution you are estimating is not the current one. It is the distribution estimated for the current conditions. Please, modify.
Line 140: Be sure the adjective “present” is modifying the noun “distribution”. Or it modifies “niche”?
Line 142: This has not sense to me. As I mention above, why do you use a model that ignores the edaphic variables, being those also important variables, as you demonstrate?  This also applies for estimating the distribution of the orchid species under future climatic scenarios. In my criterion this a crucial issue. In this sense, please include in "Material and Methods" an appropriate explanation about why the edaphic variable were neglected.
Line 142: Please check if “considered” is more appropriate than “analysed”.
Lines 143-144: This congruence is not so clear to me. The occupation of a considerable area boarding the SE coast is suggested as very probable in A but not in B (red patches in between 7 and 8 o’clock in the panel A, but absent in panel B).
Line 150: Please provide any reference sustaining this statement.
Line 160 (end of): Please provide the exact panels when this information can be checked.
Line 161. Why “an” invasive range? You are not talking about a random invasive range. The expression "the invasive range" is, I think, more correct. Or better yet: "the potential invasive range".
Line 161: “Will” could be interpret as too categorical. I think “could” is a better option here.
Line 163: “the loss” instead of “loss”
Line 164: “the Northern area of” or “the North of...”
Line 165: Please guide the reader to find the panels of interest in each moment. Keeping the correspondence between all the scenarios and the panels could be a little difficult and frustrating without the inclusion of this information.
Line 175 (end): Please read the previous comment.
Line 177: “the ecological requirements”... instead of “ecological requirements”
Line 177: Rephrase this sentence by including the article “the” where it is required in the expression “the invasive and the native populations...”
Line 177: “moderate” instead of “medium”
Line 181: “indicates” instead of “indicated”. I suggest to put the verb in present because this a result.
Line 183: The correct verbal form is “influences” because “it” is third person.
Line 183: Please consider “of niche identity.” or “of the niche identity test.” instead of “of niche identity test”.
Line 184: Replace “is” by “could be”. The results in this kind of studies are estimations and therefore are not necessarily categorical.
Line 196: “habitats” instead of “habitat”
Line 200: “also different” instead of “different”
Line 201: “these two…” instead of “the two…”
Line 209 Please check for an extra space between the words helleborine and Dactylorhiza
Line 209-210: Please consider to include some examples from the tropics, where the role of alien orchids is not so well known but the area affected is proportionally much larger. Certainly, some of these invasive species are not exactly weed. For example, Eulophia alta, Oeceoclades maculata and Spathoglottis plicata can reach high densities even in not so disturbed areas.
Line 212: “phenomenon has remained” instead “phenomenon remained”.
Line 214-217: Please provide some references regarding these ideas.
Line 227-229: Consider to explore if there is any previous study documenting that the existence of a pollinator independent breeding system can provide a higher number of generations just occurring in a particular habitat (i.e. without interchanging genes from other populations under different climatic conditions). Theoretically, this could allow a faster local adaptation to the particular conditions of each site.
Line 244: “South” instead of “south”
Line 261: Does this apply to the genus Disa or to the species of interest? (which I consider is the point in this phrase). Please clarify.
Fig. 1 (Figure capture): The expression “for the orchid Disa bracteata” or something similar should be included. Each figure needs to be self-explanatory.
Fig. 1 (Figure capture):  You need to distinguish more clearly between “current climate” and “future climate”. So, mentioning “climate” at the beginning for the panels A and B is not very accurate.
Fig. 1 (Figure capture): This is a question I made in many places along the manuscript. Why you did not consider the soil parameters in addition to the different future climate scenarios? Please provide this explanation in the section of Material and Methods of your manuscript.
Note: All comments above mentioned also apply for Fig. 2 as well. In addition, please note that dots in Fig. 2 representing the localities that were sampled should be green for simplicity, but they are in violet. Consequently, please modify the text or the images to keep the needed correspondence.
Fig. 3 (figure caption): Firstly, there is no reason to keep both sentences as separated paragraphs. Additionally, the text introducing this figure should not just describe what the reader can see by her/himself. The PCA shows much more information than the one provided in the text (e.g. 1. Degree of segregation in the abiotical niche of the native and invasive populations of Disa bracteata). Also, please provide more information about how you obtained the PCA.
Suggestion #2: “Enviromental niche of **** represented as a PCA resuming all environmental values recorded in natural and invasive populations of this orchid.”
Fig.4 (Figure Caption): Please check the comments for Figure Caption 3 and apply them to this one. What do these boxplots represent? I mean, what should be in the heading of your text? Both sentences should be joined in a single paragraph.
In addition: please also explain, as part of the caption text, the meaning of each climate variable code.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: CLIMATIC NICHE SHIFT AND POSSIBLE FUTURE SPREAD OF THE INVASIVE SOUTH AFRICAN ORCHID DISA BRACTEATA IN AUSTRALIA AND ADJACENT AREAS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The writing of this manuscript needs significant review. I have annotaed the document throughout with suggestions however at present there are some sentences and paragraphs which make understanding the main points difficult. Interestingly the written English in the rebuttel is significantly stronger than in the manuscript itself.
Whilst some of the important invasive literature is cited, I would have thought additional interpretive context with other invasive species studies could have been provided in the discussion
Experimental design: I do not profess to be an expert in modelling or in the methods employed for this study. Having read the rebuttel thoroughly and the earlier reviews by those who do seem to have more experience I do not think that the authors have responded to the comments adequately. Possibly the reason for this is that the data required to adequately understand drivers of distribution are simply not available in required detail.
I do not feel comfortable with the words 'ecological' or environmental' conditions being used to describe the bioclimatic variables used in this study.

I would prefer that the authors stick to 'bioclimatic' variables throughout as that is what is studies. I am also conscious of the word 'niche' which has quite braod connotiations. It should be prefaced with the word 'bioclimatic' because that was what was studied.
Validity of the findings: I think the findings are interesting and worth reporting however teh text needs considerable improvements beforehand
Additional comments: I am comfortable with the explanation provided by the authors not to consider the usual ecological drivers of orchid distribution - mycorrhizal and pollinator associations. I know the species well and these are certainly not variables easily modelled or likely to be of consequence. That said, I would have liked to see comparisons with similar studies on other non orchid invasive species.