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: SLIMENRICH: COMPUTATIONAL ASSESSMENT OF PROTEIN–PROTEIN INTERACTION DATA AS A SOURCE OF DOMAIN-MOTIF INTERACTIONS
Review round: 1
Reviewer: 1

Output:
Basic reporting: Minor Comments:
1) There are a number of important reference missing from the paper, in particular, Neduva V, Russell RB (2006) and Gavin et al. (2006) (see the "validity of findings" section). Also, important are Pepsite (Petsalaki et al. (2009)), ADAN database (Encinar JA et al. (2009)), iELM (Weatheritt et al. (2012)), MiniMotif miner (Mi et al. (2012), and PIPER-FlexPepDock (Alam et al. (2017).) Plus review of Bilkstad and Ivarsson (2015).
2) The scripts used to create SLiMEnrich should be freely available.
Experimental design: No comment
Validity of the findings: Major Comments
1a) The authors they map “predicted SLiMs” to “any protein in the first PPI data column”. The authors have previously published programs such as SliMPrints and SLiMSearch that demonstrated the need to use conservation when predicting SLiMs. Based on the text, the authors are using only regular expression matches and a disorder filter. This is likely to lead to significant false positive rate.  The authors need to demonstrate this does not impact their results (see point 1c).
1b) The authors identify SLiM-binding domains by identifying known interaction domains from the ELM-curated list in “any protein from the second PPI column”. However, many SLiMs have a strong preference for sub-groups of the Pfam domain families, as demonstrated by phage display and discussed in multiple papers from members of the ELM database A few prominent examples of this are SLiMs binding to the SH2, SH3, PDZ, and WD40 domain families.  The authors need to demonstrate this does not impact their results (see point 1c).
1c) If the authors wish to use a weak stringency filter for SLiMEnrich, they need to demonstrate that the results are not affected by the stringency of filtering they use.

2) The authors describe a case study demonstrating the power of SLiMEnrich of Y2H data. The authors need to contrasts these results with Neduva and Russell in 2006, as well as in Gavin et al. (2006), that found “only about 1% of interaction in Y2H data rely on motif-mediated interaction”. The authors should also extend this analysis to compare multiple high-throughput PPI studies (e.g. from Y2H, tandem mass-spec, LUMIER, and MAPPIT), as well as older Y2H studies to the most recent iterations.
Additional comments: The authors introduce a computational pipeline called SliMEnrich to assess how well a given PPI dataset captures SLiM-mediated interactions. This is a useful approach to assess the enrichment of motifs within protein-protein interaction datasets. To the reviewer’s knowledge, the resource is unique and the website works nicely producing graphics that are useful and easy to interpret. However, the usefulness of the resource depends strongly on its accuracy, which is in not sufficiently assessed or demonstrated. Furthermore, Russell and colleagues did a similar analysis over 10 years ago, which the authors do not reference. Prior to publication, the authors need to address the handful of major comments below.

The website should provide the location of the motif and the domain in the output, as well as an assessment of accuracy.


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: SLIMENRICH: COMPUTATIONAL ASSESSMENT OF PROTEIN–PROTEIN INTERACTION DATA AS A SOURCE OF DOMAIN-MOTIF INTERACTIONS
Review round: 1
Reviewer: 2

Output:
Basic reporting: - While the introduction explains the importance of SLiM and DMI prediction and
the motivation for developing SLiMEnrich, the authors fail to acknowledge a lot
of relevant work that has furthered our understanding of how SLiMs bind to
distinct recognition domains. Some of these papers exploit PPI data to predict
DMIs, so I disagree with the authors' statement that "the nature and complexity
of PPI data used for SLiM and DMI predictions has not been the focus of rigorous
study". Some of the papers I refer to are:
   - https://doi.org/10.1186/1471-2105-12-225
   - https://doi.org/10.1371/journal.pone.0025376
   - https://doi.org/10.1093/bioinformatics/btu350
   - https://doi.org/10.1371/journal.pcbi.1003881
   - https://doi.org/10.1093/bioinformatics/btw045
   - https://doi.org/10.1073/pnas.1518469113

- The authors must explain where SLiMEnrich stands compared to some of the
above-listed methods for DMI prediction, why it is better and list its
limitations.
Experimental design: - The authors claim that SLiMEnrich "assesses how well PPI data is capturing
DMIs and thus, by inference, how useful that data should be for SLiM discovery".
While it is clear how the former is achieved by comparison with a random
distribution of predicted DMIs, it is not clear how the pipeline can help with
SLiM discovery. The authors must explain this.

- I suggest that the authors label each step of the SLiMEnrich pipeline in
Fig. 1 (e.g. with letters or labels like "STEP 1") and refer to these sections
of the figure in the text. This will make it much easier to understand the
pipeline.

- One of the files required by SLiMEnrich is the SLiM predictions, which
associate proteins in the first column of the PPI file with short linear motifs.
The authors suggest the SLiMProb tool, developed by themselves, to generate this
mandatory file. What other tools are available for this task? Are their outputs
compatible with SLiMEnrich? What is the minimum set of columns required in a
SLiM-prediction file to be compatible with SLiMEnrich?
Validity of the findings: - The authors present a Case Study in which the well-known HI-II human protein
network is enriched with DMI data. In the Discussion, the authors argue that
this high-throughput PPI dataset is "indeed capturing real SLiM-mediated
interactions and [is] therefore suitable for de novo SLiM prediction". The
authors must clarify why the over-representation of DMIs in HI-II is unexpected.
Is it due to the low-affinity of SLiM-mediated interactions? If so, this could
be a good part to remind the reader of this fact.

- The authors conclude that "SLiMEnrich [...] is useful for identifying
suitable PPI data for de novo SLiM prediction". However, this is not supported
by the presented results. Even though the authors start the Discussion saying
that this is outside the scope of the paper, they must backup this conclusion
by applying their pipeline to different PPI data sources (e.g. a meta-database
like HIPPIE https://doi.org/10.1093/nar/gkw985, a Y2H dataset like HI-II and an
AP/MS dataset like the BioPlex https://www.nature.com/articles/nature22366) and
show that the cases in which DMI enrichments were poor lead to bad SLiM
predictions and vice versa.
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: SLIMENRICH: COMPUTATIONAL ASSESSMENT OF PROTEIN–PROTEIN INTERACTION DATA AS A SOURCE OF DOMAIN-MOTIF INTERACTIONS
Review round: 1
Reviewer: 3

Output:
Basic reporting: The article is well written and makes good use of the literature to provide sufficient context and background. The raw example data are downloadable at https://github.com/slimsuite/SLiMEnrich/tree/master/example, as referenced in the paper.

Self-contained: I would have liked to see the approach applied to other datasets to really address the challenge outlined in the abstract and introduction (comparing PPI detection methods). I think it would have been very easy to include one or two other protein-protein interaction datasets, and I don’t quite understand why the authors decided to stop where they did. A followup study is mentioned, however.

Figures:
- Figure 1 has some formatting issues and would greatly benefit from a simpler layout and use of colours. Some of the text is too small to be legible, the acronyms are not explained or obvious, and most of all the flow is not clear to me. Some arrows are missing heads. This figure does not currently benefit the paper as much as it could since it is unintelligible at first glance. What, conceptually, is the difference between “Tool/Application” and “Feature/Module”? It should be made clearer that SLiMProb is an external tool that provides input. What is an “ELMOcc”, an “EBD” and an “mProtein” to a reader trying to quickly grasp the workflow? An improved version would clearly show the input data sources and the outputs at a glance, without making use of acronyms. This would greatly improve the clarity of the paper.
- Figure 4 would greatly benefit from having intelligible protein names (e.g. gene symbols) and Pfam domain names rather than numeric identifiers — otherwise its usefulness is extremely limited. The same goes for the example data used in Figure 2 and on the website. I realise that no identifier mapping is done by the application, but it would be very helpful to have readable identifiers. A simple export from UniProt should provide this.

Finally, it would be useful if the Conclusions section spelled out the acronyms (lines 184-185).

Some minor points:
- Abstract, line 14 (“Despite of their significance”) -> “Despite their significance”
- Abstract, line 14 (“challenging to identify”): I think an explanation of such a statement is necessary, e.g. “due to their low affinity”
- Abstract, line 16 (“DMI are generally underrepresented”) should read “DMIs”
Experimental design: The application and analysis are very useful and admirably implemented for reproducibility. The approach is clear and straightforward and uses established methods. The analysis is open, well-documented, downloadable and additionally available as an interactive web implementation using Shiny.

The research question is extremely interesting. However, I am a bit surprised the authors decided to stop where they did, just short of actually comparing multiple PPI datasets, or using an ELM dataset containing only experimentally validated instances. However, a followup study is mentioned, which is great.
Validity of the findings: Using the example data on the website, the Histogram tab reports “False Discrovery Rate (FDR) is: 1.21”. It should not be above 1. This is not an actual “FDR” implementation and should be renamed (line 113). The definition is closer to a BLAST E-value. The text should also be amended where an “FDR” of 0.85 is reported (lines 174-175).

The conceptual issue here is that the mean 5,213 random DMIs are not necessarily all false, as the authors state in the introduction (the motivation being discovery of new domain-motif interactions, many of which do not show up in PPI datasets). I also find the very simplistic quantification of "true positives" in line 180 problematic. I am not sure the approach can support it.

A much better, and I would think more obvious measure would be to count how many of the ~14,000 Y2H interactions involve one of the 1,716 experimentally validated, true-positive human ELMs (http://elm.eu.org/instances/?q=&instance_logic=true+positive&taxon=Homo+sapiens&submit=submit&reset_form=Reset) and an appropriate ELM binding domain (http://elm.eu.org/interactiondomains).

Overall the analysis is clear and straightforward and I do find the findings believable, namely that Y2H is an appropriate method for domain-motif interaction detection, despite a high degree of noise.
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: SLIMENRICH: COMPUTATIONAL ASSESSMENT OF PROTEIN–PROTEIN INTERACTION DATA AS A SOURCE OF DOMAIN-MOTIF INTERACTIONS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The discussion section should be limited to providing context to the results presented in the paper. At present, the discussion reads more like a review. I'd recommend making the discussion more succinct and saving discussion points for the author's future paper on PPI networks.
Experimental design: I am content with experimental design of the study
Validity of the findings: I am content the findings are valid
Additional comments: I am content with the authors' responses to my concerns. It is disappointing that they didn't include further analysis in the paper but I understand the logic.


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: SLIMENRICH: COMPUTATIONAL ASSESSMENT OF PROTEIN–PROTEIN INTERACTION DATA AS A SOURCE OF DOMAIN-MOTIF INTERACTIONS
Review round: 2
Reviewer: 2

Output:
Basic reporting: The revised version of the article is well-written and easy to follow. The introduction explains the importance of SLiM and DMI prediction, includes the references suggested by me and the other reviewers and more clearly states the goal of SLiMEnrich.
Experimental design: The authors have made a much better version of Fig. 1 that makes it much easier to understand the proposed pipeline. In addition, they included a default set of SLiM predictions so that users can apply SLiMEnrich to their data out-of-the-box.
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: SLIMENRICH: COMPUTATIONAL ASSESSMENT OF PROTEIN–PROTEIN INTERACTION DATA AS A SOURCE OF DOMAIN-MOTIF INTERACTIONS
Review round: 2
Reviewer: 3

Output:
Basic reporting: I still think the many acronyms used make the manuscript and tool unnecessarily cryptic. Terms such as "ELMc" really need to be explained, particularly in Table 1. I had to guess that this refers to ELM classes. Please define these in the text. "Motif-containing proteins" would not be unnecessarily long in place of "mProteins" either, I think.
Experimental design: I am very pleased that curated ELM instances were used now, and the low FDR estimate for these is reassuring to see.
Validity of the findings: This is still a bit difficult to assess when only looking at one PPI dataset, and I still believe that it would be very easy to test at least one or two additional ones. I do agree with the authors that the question of which experimental method and which specific PPI datasets best capture domain-motif interactions warrants an in-depth follow-up study, however, and I look forward to seeing it.
Additional comments: Thank you for the impressive amount of work involved in the improvements to the manuscript, the excellent new figures 1 and 2, and the improvements to SLiMEnrich itself. I very much look forward to reading your follow-up 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: UNCOVERING HIDDEN SPECIFIC DIVERSITY OF ANDEAN GLASSFROGS OF THE CENTROLENE BUCKLEYI SPECIES COMPLEX (ANURA: CENTROLENIDAE)
Review round: 1
Reviewer: 1

Output:
Basic reporting: I think the manuscript is written in proper English. The references are adequate, but there are some minor errors in the citations and references (one missing). The structure, figures and tables seem good to me. However, I have my concerns about the relevance of the results (detailed in the comments to the authors).
Experimental design: The work is within the aims and scope of the journal, but I think that it fails to fill a gap of knowledge (see comments to the authors).
Validity of the findings: See comments to the authors.
Additional comments: This study aimed to evaluate the species diversity of populations allocated to Centrolene buckleyi and the taxonomic status of C. venezuelense, for which a series of standard unilocus species delimitation methods were applied. As a result, three candidate species were identified and the distinction of C. venezuelense was ratified. The methodological approach and the interpretation of the analyses are relatively simple so there should not be ambiguities in the taxonomic decisions derived from the results. However, I have several serious disagreements with this study.

1. The authors first highlight the advantages of using delimitation methods based on coalescence (lines 40-46), but finally recognize that these methods actually diagnose genetic structure, not species (lines 278-279). Consequently, the authors consider their results as "a first assessment of species boundaries of the C. buckleyi species complex" and recognize that their single-locus data provide "a preliminary view of species boundaries" (lines 275-278). So, what is the contribution of this research to the taxonomy of the C. buckleyi complex? One of the arguments that suggest that C. buckleyi is a complex is "its lack of monophyly", which can be inferred from some of the articles cited (e.g. Guayasamin 2008, Twomey et al. 2014). Therefore, the only novelty of this study is that C. buckleyi would be composed of at least four lineages that could correspond to different species. I agree "that in this era of biodiversity crisis, it is urgent to increase the rate in which the biodiversity is characterized" (lines 292-293), but it is not clear to me why the authors did not formalize any of their findings. I suppose that the authors are working on the description of one or more of the candidate species, but by not including this final step, there is practically no progress in solving the problem: C. buckleyi is still a species complex (something that could already be inferred from previous analyses) and C. venezuelense would be a good species (something that other authors had said).

2. The distribution of C. buckleyi complex covers more than 1000 km and the authors only included specimens from five localities. Is this enough to evaluate the diversity in a taxon that apparently includes several species whose distributions are obviously not known? Why were not more populations assigned to C. buckleyi included? From Ecuador, for example? (Cisneros-Heredia & McDiarmid 2007) I think that sampling is insufficient, in number of localities and specimens, to solve a taxonomic problem of that magnitude.

3. My third main point is about the interpretation of the results of the delimitation and distances analyses. Usually, the idea behind using various methods of delimitation is to seek instances of congruence between them (i.e. candidate species supported by all of them) and to resolve cases of inconsistency by going to information from other sources, unless the authors favor one method over another. Here I do not see clearly what strategy the authors applied. First, the methods of delimitation recognized between 21 and 25 species, but where is explained what criteria were used to choose between the methods? In the discussion, apparently, the authors favor the delimitation obtained with bGMYC because of its greater sensitivity and because it has been used successfully in other studies of amphibians (and you will always find examples where any method works well!). However, the fact is that there are many examples in the literature where this method fails in the delimitation of species, mainly due to overesplitting (e.g. Miralles & Vences 2013, Hamilton et al. 2014, Pentinsaari et al. 2016), and the same could be applied to other methods. Conversely, the results of PTP analyses are discarded because they group C. sabini and C. buckleyi 2 as a single evolutionary unit. But why is the conspecifity of C. sabini and C. buckleyi 2 an equivocal delimitation? (line 254) Can not there be a species of amphibian that is distributed along 1300 km? In this case, the short branch lengths that separate these taxa are striking (Fig. 2), so intermediate samples are required to elucidate this issue. Second, the two methods try to accommodate intra- and interspecific processes along the branches of a phylogeny so the question is, how does the present sampling influence the performance of the methods, when most of the data are one specimen per species? Of course the proponents of the method say that it works very well under a wide spectrum of conditions (e.g. Fujisawa & Barraclough 2013), but the present data set do not allow to evaluate if the method is really distinguishing intra/interspecific patterns of molecular variation. And third, regarding the genetic distances, what is the point of calculating the distances only between the focal populations? This does not add additional information to what one can observe in the phylogeny, but it does provide a clue that the authors neglect. Are the genetic distances that were obtained between the candidate species low or high compared to the other species in the group? Although the authors do not provide all the distances between species, it seems that the values between C. buckleyi 3 with C. aff. buckleyi and C. venezuelense are the lowest of all the species of the genus included. I am aware that genetic distances are not an unequivocal indication of species status, but those values are well below the values that have been proposed as a thumb rule for the limit of intra/interspecific divergence (3-5%) for the 16S in amphibians (e.g. Vences et al. 2005, Fouquet et al. 2007, Matsui et al. 2016, Walker et al. 2018). According to this yardstick, even the other candidate species (and surely other species included in the phylogenetic analysis) do not reach enough divergence to be considered as full species (I think that the pair C. sabini-C. buckleyi 3 fall in this category). I reiterate, there is no fixed value to define the boundary between the intra/interspecific divergence, but the genetic distances between some populations of C. buckleyi and other closely related species are quite low enough to consider the possibility that they are conspecific.

4. My last main point is about the other types of evidence that the authors provide as additional support for the distinction between candidate species. In the discussion they point out that glassfrog species in general are altitudinally segregated, giving the example of C. buckleyi 1 and C. buckleyi 3. However, the data of C. buckleyi 3 are only from the Yanayacu Biological Station and of C. buckleyi 1 only from two localities (Table 1). What about all the other populations of C. buckleyi from Ecuador? (Cisneros-Heredia & McDiarmid 2007) Is there enough geographic data to claim that both species segregate altitudinally? On the other hand, the authors cite differences in calls between both species, but the data are from one specimen per population. Similarly, is there enough data to establish if there are significant differences in this trait? My opinion is that the knowledge of the phylogeny, biogeography and bioacoustics of this group of anurans is still too incomplete to support those taxonomic suggestions with such fragmentary data.

In short, I believe that this work does not represent a significant advance in the taxonomy of the C. buckleyi complex because its main result is only to confirm that this taxon is a complex, formed by at least four species. I think that sampling is insufficient to solve such a complex problem and that the authors do not adequately argue their methodological choices. Moreover, It is not clear to me why authors provide only partial information to support the specific status of some of the candidate species (and why they refrain of describing them formally), and in turn ignore their own genetic distance data, which suggest that some of the populations may be conspecific.

I have a few minor comments, but I did them in the corresponding text in the pdf. Also, I detected several minor errors, including spelling, and other formatting errors that I also indicated in the pdf.


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: UNCOVERING HIDDEN SPECIFIC DIVERSITY OF ANDEAN GLASSFROGS OF THE CENTROLENE BUCKLEYI SPECIES COMPLEX (ANURA: CENTROLENIDAE)
Review round: 1
Reviewer: 2

Output:
Basic reporting: The article is well written and the conclusions supported by the analyses they performed. The authors proposed some taxonomic changes for a group of glass frogs and they are aware of the limitations of their data set regarding sampling numbers. However, the authors do not mention the weaknesses of working with mtDNA only, and that their results might be biased because of this. More about this in the section 'Validity of the findings'

I have some comments for specific points in the manuscript:

L143 change model to models
L150 higher? how much is higher?

Please use a constant term throughout the manuscript : "a single molecular entity" or "a single evolutionary unit"

L200 C. aff. buckeyi  in italics

L255 What do you mean by "intrinsic factors of the 12S and 16S genes"

L261 (0,6% y 0,8% respectively : be consistent in the decimal separator, use period instead of comma, same with thousand separator, use comma instead of period

L277 In my opinion, there is a more fundamental problem than the analytical outcome of the coalescent methods when using one locus. The main problem is the incomplete history resulting from analysing only mtDNA loci.

L300 Finantial change to Financial

Figure 1 It would be useful to know where the samples of the closely related species were taken.

Figure 2 Bayesian and ML totally concordant? Why did you pick this tree? Please also explain in the text.

Figure, please be consistent on how C. buckleyi 1 is labeled in the figures, you refer to those sample at least in 3 different ways

Table 1 there is no column for the Genbank accession numbers

What is the difference between Fig 2 and Figure S2? Is Figure S2 really needed?
Experimental design: Please provide more details about how the BEAST analysis was performed. I assumed that you calculated relative divergence rates only, but this is not explained in the manuscript.

Table S2. how were these distances calculated?
Validity of the findings: One interesting outcome is the paraphyly of the study species Centrolene buckleyi, a result previously found by other studies and confirmed with the newly analysed samples in this manuscript. The authors describe this pattern but do not provide possible explanations for it. For example, is this the result of past introgression and mtDNA sequence capture? This phenomenon has been observed in other frogs e.g. Bryson et al 2010). Although the authors lack nuclear data to test for this hypothesis, at least this possibility should be mentioned and considered as several studies suggest this might be a widespread phenomenon. Additionally, unless I missed it, the authors mentioned that to improve the species delimitation it would be necessary to add more geographical samples, how about adding more markers, specifically nuclear markers?
The authors did not mention anything about differences in morphology among the samples studied, nor possible differences between the C. buckleyi groups and the species they resulted related to. It would be useful to provide information about this. How the specimens were identified? Is there a possibility that they have been misidentified?

How about geographic distribution changes? The authors mentioned that some of the taxa that now have similar mtDN sequences are rather far away. What is known about distribution changes in this species or in other species in the area?

The discussion will benefit from considering plausible biological explanations for the results in addition to the methodological aspects that the authors discussed.
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: UNCOVERING HIDDEN SPECIFIC DIVERSITY OF ANDEAN GLASSFROGS OF THE CENTROLENE BUCKLEYI SPECIES COMPLEX (ANURA: CENTROLENIDAE)
Review round: 1
Reviewer: 3

Output:
Basic reporting: The manuscript is well-written and clear, with good coverage of relevant literature. I think the introduction could have a bit more context. It is basically paragraph 1 about species delimitation, and paragraph 2 is already the specifics of the taxonomy of the buckleyi group. I think a paragraph to bridge these two paragraphs could be a good addition. Specifically, it would be good to convey the importance of finding candidate species. Most people would not argue against the significance of actually describing species, but here no species are described so I think you need to "defend" why identifying candidate species but not describing them is still important. It could also be worth mentioning drawbacks, if any, with using coalescent-based delimitation methods.
Experimental design: The methods are described in detail, however, as I mentioned in an email to the associate editor, I do not have expertise in coalescent-based species delimitation, so I cannot adequately review the technical aspects of those analyses.
Validity of the findings: The interpretation of the results is generally sound, although in some cases relies on some subjective acceptance of one delimitation method vs. another. I expand on this in point 2 of the general comments section.
Additional comments: 1. Overall the main goal of the paper isn't entirely clear. It seems to me that applying these coalescence methods should be a tool towards some greater objective, like describing a species or maybe using the identified taxa to evaluate some biogeographical scenarios. But in this case the application of the method seems like the endgame. The most obvious way this could be rectified would be to actually describe the species here. That would of course entail a lot more work on the manuscript but it would make crystal clear why the authors would use these delimitation methods. I understand the authors want to get more data before doing this so formal descriptions might be unfeasible. Otherwise, this aspect of the manuscript could be improved by better emphasizing in the introduction why this study is important. I touch on this a bit in the basic reporting section.

2. I think that using a battery of methods kind of undermines the idea that these methods are an improvement over traditional taxonomy in that they reduce subjective interpretations. For example, which of the 5 methods is 'correct' with respect to Ce. sabini and Ce. buckleyi 2? The authors argue that because of biogeography it is extremely unlikely these two are conspecific, but in my opinion it is completely possible (glassfrogs have some crazy distributions, for example we found Cochranella erminea something like 900 km north from the type locality, and some of the Amazonian Hyalinobatrachium have similar stories.). On one hand it's good to see how different methods treat the same dataset, but using all these methods comes at the cost of increased subjectivity during interpretation. I don't think there's a good way around this but this could be touched on in the discussion.

3. Figure 3 could be improved by including all the terminals on the tree. For example, it seems like only a single buckleyi 2 and buckleyi 3 is included in that figure, but from the results section it sounds like all the terminals were included in the analysis. I think showing everything is important for that figure because it allows the reader to see whether the methods are oversplitting (ie. splitting what are definitely single species, like two sequences originating from the same locality). Related to this, including multiple terminals from species where multiple sequences are available (e.g. Ce. charapita, Ce. sabini, possibly others) could help evaluate over/under-splitting, which could broaden the scope of the discussion a bit. For example if GMYCs also splits charapita into two species, you'd have an indication that this method seems too liberal in delimiting species.

Specific comments:

Introduction
lines 29-30: "urgent challenge in biodiversity hotspots". Wording is unclear -- do you mean it's an urgent challenge in identifying biodiversity hotspots?

line 31: "...due to theoretical and practical issues." I don't really understand what you mean here. You don't actually say why it's important, you just say that it is because of issues, which is vague.

line 33: hypenate 'species-level'

line 35: delete 'mostly'

line 58: change to "...differences with respect to..."

lines 62-68: based on this, in particular the polyphyly of buckleyi, it seems obvious it is a species complex. The different populations of this "species" are not even very closely related. It seems to me that what is needed is not another study saying that there are multiple species here. They ought to be described and this manuscript seems like a good place for it, assuming the relevant data is available.

Methods
line 75: Wording is a bit awkward, change to "Nymphargus, a genus closely related to Centrolene."

lines 96-97: All positions containing gaps or only gap-only positions? If it is the former, why would you do this? An indel shared between two taxa could be evidence of homology. Same with missing data -- if all taxa but one had data for a given site, why would you delete that?

line 165: On the trees, buckleyi 1 is called "buckleyi sensu stricto". Maybe change it to "buckleyi 1 (sensu stricto)" so you know exactly what buckleyi 1 in the text is referring to.

Discussion
lines 205-206: The distinction is only corroborated if you disregard the results of the PTP analysis.

line 227: change to "regards"

line 265: change to "here we show" or "here we have shown"

Sincerely,
Evan Twomey


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: UNCOVERING HIDDEN SPECIFIC DIVERSITY OF ANDEAN GLASSFROGS OF THE CENTROLENE BUCKLEYI SPECIES COMPLEX (ANURA: CENTROLENIDAE)
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: The article has improved after the first round of revision, the added detail in methods and justification of the study is welcomed. I have a couple of minor comments:

- I still think that the BEAST methodology is incomplete, specifically regarding the calibration/no calibration of the nodes. This is essential to reproduce any analysis.

- I would have liked to see the accession numbers of all the sequences included in the analyses. As it is currently presented, the reader would have to dig in the Genbank to find the specific sequences used.

Please address the following spelling mistakes:
L.63, The later was synonymized under C. buckleyi by Ruiz-Carranza & Lynch (1991).  - Change to 'latter'
L73 C. aff. Buckleyi  - change to lower case


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: UNCOVERING HIDDEN SPECIFIC DIVERSITY OF ANDEAN GLASSFROGS OF THE CENTROLENE BUCKLEYI SPECIES COMPLEX (ANURA: CENTROLENIDAE)
Review round: 2
Reviewer: 2

Output:
Basic reporting: As this is a re-review I've consolidated all my comments to a single section (General comments for author)
Experimental design: As this is a re-review I've consolidated all my comments to a single section (General comments for author)
Validity of the findings: As this is a re-review I've consolidated all my comments to a single section (General comments for author)
Additional comments: As this is a re-review, I mainly focused on whether my suggestions were addressed appropriately, however, I couldn't help but notice that many of my concerns echoed those of reviewer 1, just that reviewer 1 used a bit stronger wording than me. My main comments were:

1. Clarify the goal of the paper. A paragraph was added to the introduction to address this. However, I mentioned that it would be good to also discuss drawbacks or limitations of these methods, but it doesn't look like that was added. Basically, the authors argue that proposing candidate species can be useful for guiding taxonomic research and conservation actions. While this is true, it doesn't change the fact that formally describing these species is actually a better and more direct way of doing the same thing.

2. "Reduce subjectivity" in terms of selecting some methods over others. It appears the authors dealt with this appropriately, supporting candidate species inferred by most or all methods.

3. Include multiple terminals from species where multiple sequences are available. The authors dealt with this, adding some extra terminals to the analysis that allows them to address whether putative conspecific lineages are being "oversplit" by the analyses (it appears they are not). Although, one method (GMYCm) gives some results that are really absurd (e.g. lumping C. charapita and C. geckoideum). This latter result does not appear to be mentioned anywhere in the manuscript. In my view this is kind of an important point because it shows that these methods are necessarily evaluated in light of an existing taxonomy, which in my view calls into serious question their use for establishing new taxonomic proposals "from scratch".

New comments:
-- on re-read, the Conclusions section seems a bit preachy. On one hand the authors are stressing how important it is to characterize biodiversity but at the same time do not describe the species here, despite there seeming to be plenty of evidence for doing so (lack on monophyly, call differences). Thus, this seems sort of ironic.

-- The references should be checked in detail. There are many inconsistencies (e.g. using title case occassionally for titles, sometimes including the volume number and sometimes not, inconsistent italics on journal names)

- the GPS coordinates on the genbank table messed up, I guess a formatting error with decimals

Overall, the authors did mostly address my comments, in particular including additional terminals in the analysis, which I feel definitely strengthens the paper. Still, I'm not totally sure why the analyses presented in this manuscript would not simply be included in the formal taxonomic description. In other words, assuming the descriptions will eventually be done, I don't see the reason to publish these data in a separate manuscript rather than just including it in the formal descriptions. These analyses would simply be used to support the taxonomic proposal. In the rebuttal letter the authors argue that identifying candidate species using methods like this is an important first step for (eventual) taxonomic changes, but I disagree, as there has been plenty of excellent taxonomy done prior to the advent of coalescent delimitation methods. To some extent these comments echo the comments of reviewer 1.

If indeed these populations of C. buckleyi have crashed and are in urgent need of conservation, this only underscores the need to formally describe these species. I doubt the Colombian and Ecuadorian governments will be designing conservation strategies based on candidate species (I could be wrong). To me this is a better argument for why these species should be described than why the delimitation methods should be used. There is clearly call data available for some of these lineages (as mentioned in the discussion), when combined with the new samples, compelling phylogenetic results (i.e. lack of monophyly, delimitation results), the description of these species should be straightforward.

In any case, these comments mainly focus on "degree of advance", which is something PeerJ is not interested in. As far as scientific validity I have no issues with the manuscript in its current state. I have made some changes to the tracked-changes manuscript, mainly minor grammatical issues. The sheer volume of tracked changes made it difficult to see exactly what was supposed to be written, so I would suggest that someone (either one of the reviewers or the editor) carefully check any final version for minor errors.

Sincerely,
Evan Twomey


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: BIOINSTALLER: A COMPREHENSIVE R PACKAGE TO CONSTRUCT INTERACTIVE AND REPRODUCIBLE BIOLOGICAL DATA ANALYSIS APPLICATIONS BASED ON THE R PLATFORM
Review round: 1
Reviewer: 1

Output:
Basic reporting: This manuscript needs a lot of improvement in English writing. Grammar errors examples are:
1. line 142, 'what more' should be 'what's more'.
2. line 144, 'and so on' should be 'et. al'.
3. line 145, 'combined' should be 'combine'.
4. line 167, 'download' should be 'downloaded'

Improvement is also needed for wording, for example, in line 123, it's not appropriate to use 'non-professionals' to define users, maybe 'non-programming' is better. For 'Use case # xx' , it's better to change as 'Example # xx'.
Experimental design: The methods are well-explained and illustrated. However, the research question is not clearly specified in materials and methods. The authors should explain why it is necessary to develop such a tool to integrate download, install and share of bioinformatics tools/databases. What kind of issues are not solved by existing tools?

In line 74-75, 'integration of bioinformatics software/script and database' is confusing. It sounds like a pipeline providing bioinformatics analysis by combining software and database. Authors better explain the goal of this tool before introducing the design.
Validity of the findings: The authors didn't provide examples for uploading/sharing tools/data, and didn't report the time/speed of downloading/uploading a large dataset.
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: BIOINSTALLER: A COMPREHENSIVE R PACKAGE TO CONSTRUCT INTERACTIVE AND REPRODUCIBLE BIOLOGICAL DATA ANALYSIS APPLICATIONS BASED ON THE R PLATFORM
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript is well written with enough details and reference.
Experimental design: The technical design of the R package is comprehensive and novel.
Validity of the findings: The four cases well demonstrate the usage of the package.
Additional comments: The authors make great efforts to create a comprehensive R package, BioInstaller, with both Shiny application, and the HTTP representational state transfer (REST) APIs. The manuscript and the package are well written.

I only have one comment. Though enough technical details have been presented in the manuscript, Could the authors comment how the BioInstaller could be used for biological scientific finding?


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: BIOINSTALLER: A COMPREHENSIVE R PACKAGE TO CONSTRUCT INTERACTIVE AND REPRODUCIBLE BIOLOGICAL DATA ANALYSIS APPLICATIONS BASED ON THE R PLATFORM
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: No comment


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: BIOINSTALLER: A COMPREHENSIVE R PACKAGE TO CONSTRUCT INTERACTIVE AND REPRODUCIBLE BIOLOGICAL DATA ANALYSIS APPLICATIONS BASED ON THE R PLATFORM
Review round: 2
Reviewer: 2

Output:
Basic reporting: The English writing is good.
Experimental design: The experimental design is comprehensive and reasonable.
Validity of the findings: The findings are validated.
Additional comments: The author addressed my 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: DO SUBTERRANEAN MAMMALS USE THE EARTH’S MAGNETIC FIELD AS A HEADING INDICATOR TO DIG STRAIGHT TUNNELS?
Review round: 1
Reviewer: 1

Output:
Basic reporting: This manuscript contains concise, straightforward results and a new analysis method that is a marked improvement from its predecessor. By reworking how the background and technical challenges are presented, these contents will be much more accessible to a broader scientific audience.

1)	The authors do a good job in the introduction arguing for why circular statistics is a better choice than prior statistical approaches. They should also provide rationale for their decision to develop a new method for analysis, since it is a major contribution of this work. The ‘long tunnel method’ has an advantage when analyzing circular burrow systems (and conversely the ‘polygon method’ struggles with this), and I think this should be introduced earlier in the manuscript. This will provide the readers with expectations that are satisfied when interpreting the directional orientation plots.
2)	The introduction discusses positive magnetoreception findings from laboratory experiments with species that, at first glance (see point #5), are not sampled in the manuscript. Providing some phylogenetic context either in the text or in a figure would greatly benefit a reader that is not a Rodentia expert in understanding why these referenced findings may be applicable to the sampled species.
3)	Both points (1) and (2) can be addressed in figure form by providing a phylogenetic tree annotated with species/genus names average circularity scores and then representative burrow system images from a more linear species and more circular species (like in the current Figure 2).
4)	What is the rationale behind which species were chosen for analysis? If it is simply availability of data, that is fine, but then I would like some more context regarding this sampled set. Do they represent unrelated taxa? Are their burrow systems representative of the range of fossorial rodents? (size, circularity, etc.)
5)	Please clarify which specie(s) is used in the Eloff and early Burda experiments. In the referenced review Begall et al. 2014, an early Burda paper (Burda 1987) is cited with the following comment: “…Ansell’s mole rats (Fukomys anselli, in earlier papers denoted as Cryptomus hottentotus).” This comment is not repeated in this manuscript, such that the referenced paper by Burda appears to be studying species that is not sampled in the paper. However, this review suggests that there HAS been a history of magnetoreception laboratory experiments with F. anselli, which is sampled in the paper. If so, please explicitly state this, as it would strengthen the rationale for sampling Fukomys immensely. Also, the cited article in this manuscript (Burda 1989) and one cited in the review have the same title and journal name, but the review has the article’s publication year as 1987. If this is indeed the same referenced article, please reconcile.
6)	The raw data is supplied and clearly organized. It appears the number of significant figures differs between methods. If this is not due to greater accuracy in one technique, please make this consistent across data.
7)	Please provide scale bars for Figure 2. There are some small markings and annotations on the burrows in Figure 2A and Figure S1A-B. These markings should either be addressed in the figure legends or removed.
8)	The manuscript is clearly written in professional language. A few phrasing and clarification suggestions are listed below.

27 – Replace “in” with “over.” Please specify “long time.” Hours to weeks?  Comma between “and” and “in social species.”
28 – Replace “has already been” with “was.”
59 – Replace “during” with “while.”
63 – Replace “neither” with “none.” Remove “seems to be able.”
68 – Replace “also” with “then.”
70 – Remove “e. g.”
73 – Clarify “biological meaning.” Function? Underlying mechanism?
231 – Since Fukomys were pooled, “genus or species.”
246 – Replace “way” with “hand.”
248 – Remove comma.
252 – Replace “what” with “that”
258 – Remove “e. g.”
265 – Remove “e. g.”
275 – Italicize “in statu nascendi.”
295 – Are parentheses necessary?
345 – Typo.
Experimental design: 1) For the ‘long tunnel method’, was there a minimum cutoff for the length of tunnel to be included as a “straight tunnel”? Was this a relative or absolute cutoff and how was it determined? Assuming that only tunnels marked with a red line were included in the analysis, it appears many small tunnels in Figure S1E that meet the direction change criterion were not marked. This is necessary information for replication.
2) There should be some justification for pooling the two Fukomys species because congeners can be very different in their burrowing behavior. Do the F. anselli data alone show non-random orientation?
Validity of the findings: Data sets and analysis appear sound, provided that decisions made in experimental design were well justified. The interpretation of the results is fair and the the conclusion and outlook are well stated.
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: DO SUBTERRANEAN MAMMALS USE THE EARTH’S MAGNETIC FIELD AS A HEADING INDICATOR TO DIG STRAIGHT TUNNELS?
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript by Sandra Malewski provides interesting and original data that significantly contribute to long-lasting debate as to whether subterranean mammals prefer some direction while digging their tunnel systems and what sensory modality guides this behavior. As far I can judge, the authors have used all available published (and also some unpublished) data describing excavated tunnel systems. Another strength of the study that allows certain degree of generalization is inclusion of five species representing distantly related subterranean rodents as well as solitary and social species.
The paper is generally well written; the introduction provides an adequate context; references are adequate and are properly cited.

One think I miss in the Introduction is information that subterranean rodents likely use landmark independent navigation, path integration in their burrow systems. It is dependent exclusively on self-generated, idiothetic cues it is prone to rapid accumulation of errors. That is why subterranean rodents need external directional reference, i.e., a compass sense (for review see Moritz et al 2007).

While it is generally known within community zoologists studying subterranean mammals, it may be useful for a general reader to mention explicitly that light propagation is very limited in burrows and that sense of vision is of little use in underground ecotope.
Experimental design: Methodology, design of the experiment and statistical analyses are adequate. Utilization of circular statistics and “the long tunnel method” constitute important improvements when compared to Chi2 test and the polygon method has been employed in previous studies.

“The long tunnel method” need to be described in greater detail to be reproducible by another investigator. Specifically, exact information of how vector addition was done is needed. What software was utilized?
Validity of the findings: Results are convincing and substantiate majority of the conclusions the authors have drawn. However, there are few statements in the Discussion that are poorly justified or unclear to me:

1) Lines 219–222: “Although the statistics of the examination by means of the ‘polygon method’ points to a significant deviation from a random distribution for the Talas tuco-tuco’s burrow systems, this method is more prone to ecological effects than the ‘long tunnel method’, and thus less suitable to reveal any directional preference.“

The meaning of this statement is unclear and somewhat illogical. Both the long tunnel method and the polygon method yielded very similar directional preference in case of the Talas tuco-tuco’s. In fact, application of the polygon technique resulted in a smaller scatter of data points. This suggest that the polygon method is well applicable and reliable for analysis of mean direction of simple, linear burrow systems of (at least some) solitary species. Why the authors suggest exact opposite?

2) Lines 234–237: “Since the studied burrow systems have been uncovered in different regions (even continents) and areas (e.g. grassland, woodland, mountainous areas), and thus accompanying different habitats, as well as in different years (1998-2012; Table 1), the Earth's magnetic field seems to be the only globally common and stable potential heading indicator.”

This argument is not tenable. The preferred directions differed between studied species and the silvery mole-rats from only one put of three localities exhibited significant directional preference. Therefore, the authors should refrain from argumentation just mentioned. Nevertheless, I agree that magnetic compass sense most likely serve as external directional reference simply because it has been repeatedly shown that they use magnetic compass under laboratory conditions.

3) Line 232: The directional preference of Fukomys mole-rats (47°/227°) should not be described as roughly north-south as it actually is loser to west-east axis.

4) Lines 287-289: ” A preference for the North-South axis could be interpreted as a response in accordance with a magnetic polarity compass, where northward and southward can be distinguished (Thalau et al., 2006), what might be easier than calculating an angle to the poles.”

I do not understand the logic of this argument. Moreover, it is a pure speculation. I strongly recommend its omission.

5) Lines 292-294: “ …… it is not unlikely that the use of the Earth’s magnetic field by subterranean rodents as common heading indicator during digging straight tunnels is genetically determined, too, possibly explaining similar results in different species found here.”

This argument is not convincing. First, the directional preferences of the studied species are not that much similar. Actually, directional preference of Fukomys mole-rats might be significantly different from that of Tuco-tuco.  Second, and more importantly, the preferred directions reported here do differ from those reported in laboratory experiments (the silvery mole-rats: field directional preference -north/south, laboratory directional preference – east; Fukomys anselli: field directional preference -north-east/south-west, laboratory directional preference – south-east), the fact that seems to be inconsistent with hard-wired, genetically determined behavior.
Additional comments: Minor comments:
1) Lines 133-134: “..values were re-blinded…”; Line 143: “ After re-blinding the data”
Are you sure about correctness of these expressions?

2) Lines 177-179: “The ‘polygon method’ revealed that the alignment of the burrow systems of the Talas tuco-tuco deviated significantly from random orientation, while a similar strong tendency was observable for the silvery mole-rat’s systems.”

Consider reformulation of this sentence.

3) Line 258: (e.g.) (Nevo et al., 1995, Reyes et al., 2003, Savić, 1973, Yağci et al., 2010) should read (e.g., Nevo et al., 1995, Reyes et al., 2003, Savić, 1973, Yağci et al., 2010)

4) Lines 309-310:” Furthermore, we did not find statistical sex-dependent differences in mean orientation for any of the solitary species.

This information shall be moved to Results.


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: DO SUBTERRANEAN MAMMALS USE THE EARTH’S MAGNETIC FIELD AS A HEADING INDICATOR TO DIG STRAIGHT TUNNELS?
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors have sufficiently addressed my earlier questions and concerns.

Two final remarks:

If possible, increase the image quality of Figure 2B. The file version I see is quite pixelated and there are grayed areas. A file quality more similar to the complex burrow in the supplemental file would be preferred.

In the raw data, the C. talarum data has some 'long tunnel method' values that include commas. Please check if these are typos. Also, the 'long tunnel method' for Fukomys has less significant figures than the rest. Could this also be a data entry/Excel issue?
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: DO SUBTERRANEAN MAMMALS USE THE EARTH’S MAGNETIC FIELD AS A HEADING INDICATOR TO DIG STRAIGHT TUNNELS?
Review round: 2
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The revised version of the manuscript is significantly improved. I have only few comments:
1.	Lines 54 – 56: “Especially light propagation is highly limited in subterranean burrow systems, so that vision is of little use for subterranean rodents here (Kott et al., 2010).” It would be more pertinent co cite Kott et al. 2014 (Journal of Zoology 294:68–76) in this context. Also exchange “here” by “there” in this sentence.
2.	Lines 196 –197: “Furthermore, we did not find statistical sex-dependent differences in mean orientation for any of the solitary species.” Add statistics or explicit statement – statistics not shown.
3.	Lines 197 – 199: “The ‘polygon method’ revealed that the alignment of the burrow systems of the Talas tuco-tuco deviated significantly from random orientation. A similar strong tendency was observable for the silvery mole-rat’s systems.” Refer to the Figure 1 here.
4.	Lines 268 – 270: “However, the preferred mean axial directions of the burrow systems at the three localities did not differ statistically for both methods (Watson-Williams F-test applied), wherefore we pooled these data here (Figure 1).” I do recommend leaving out this argument. Because orientation was random at two out of three localities, mean directions of the burrow systems simply cannot differ statistically.
5.	Lines 292–293: “….representing a highly interesting research question of heuristic potential.” Leave out “of heuristic potential”.
6.	I did not go through the references systematically, but there seem to be a lot of inaccuracies in the reference list. For instance, ID numbers of articles are missing in some references (e.g., Hart et al. 2012; Lövy et al. 2015; Malkemper et al 2015); pages are not indicated in some references of book chapters (e.g. Hickman 1990; Lacey 2000; Moritz et al 2007).


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: CANCELLOUS BONE AND THEROPOD DINOSAUR LOCOMOTION. PART I—AN EXAMINATION OF CANCELLOUS BONE ARCHITECTURE IN THE HINDLIMB BONES OF THEROPODS
Review round: 1
Reviewer: 1

Output:
Basic reporting: I would like to commend the authors on this substantive contribution to our understanding of avian locomotion biomechanics. The basic reporting of the article is fine. The manuscript is self-contained and rational behind the study is well justified.

In terms of the structure, particularly results and discussion, I would like to see a clearer distinction between data and interpretation pertaining to the 'quantitative' fabric analysis vs. the 'qualitative' geometric modelling or scoring system. Ideally I'd like to see the quantitative data first, including the stereoplots and regressions, then followed by a qualitative section with the more verbose description. Simply, I should be able to eyeball the first few tables and graphs, and quickly get an idea of what the broad patterns are. At the moment, the interesting findings are somewhat buried in the lengthy text.

In relation to the raw data, there is no mention of making the CT data available as far as I can tell. I leave that to the Editor to decide if that is acceptable. It would be nice to also include a data table of the orientation of primary fabric orientations for specimens when collected.

The literature review is extensive and relatively comprehensive. The authors do, however, fail to mention the many studies that have found distinctly equivocal results when attempting to correlate trabecular architecture with locomotor behaviour interspecifically. Farardo et al. (2007), Ryan and Walker (2010), Shaw and Ryan (2012) have all failed to distinguish between locomotor regimes on the basis on long bone trabecular architecture (although admittedly the authors don’t tend to calculate fabric direction).
Experimental design: Whilst the authors have been ambitious in scope, this has resulted in the inclusion of several different CT protocols and data analysis techniques that are not quite fit for purpose.

I am somewhat concerned that the authors have not quantified intraspecific variation in trabecular fabric orientation. The authors recognise this limitation, but suggest this was necessary in order to achieve their broad intraspecific sample. However, in light of the subsequent Part II and Part III, it is not clear to me how they have put this big interspecific sample to good use. Only 3 species (chicken and 2 dinosaurs) are analysed in any great detail. Furthermore, the authors have actually collected some intraspecific data on modern birds, as they recognise in the legend of Figure 22 by stating that 'significant intraspecific variation' exists.

In the primate literature, several studies have found quite a high degree of intraspecific variability in trabecular architecture (Tsegai et al. 2013; Ryan and Shaw, 2012). This isn’t necessarily a problem per se, as long as the interspecific variation relating to the differences in locomotor behaviour you’re interested in is greater. But given that the authors seem to have the modern replicates, it would be nice if this were given some consideration.

Linked to this, I would like to see more consideration given the potential taphonomic effects on fossil trabecular structure. The authors suggest fabric direction is more reliably assessed in fossils than trabecular thickness or spacing.  However given that fabric orientation is obviously only useful relative to the anatomical axes, I wonder how one controls for potential deformation of the fossil, twisting, curvature etc. Again, having an idea of modern intraspecific variability is essential, in order that we can then understand the degree to which fossil taxa fall with this range. Larger intraspecific variation in fossils might be suggestive of some taphonomic artefacts.

There are also issues with the scanning methodology. Specimens were digitized in a range of scanners depending on their size and bulk density. Ultimately, larger specimens were scanned at a coarser voxel size. This might not be a problem if we can assume that larger dinosaur have absolutely larger trabeculae. But to what extent is this the case? Were the specimens at least scanned at a comparable 'relative' voxel size? How many voxels, say, comprised the average trabecular thickness, and is this consistent across the sample?

Obviously the authors have also been constrained by the scanning of 'whole' bones. I agree that it is a step forward compared to studying small cubes of excised bone, but it does limit scanning options and specimen availability. This would all be worthwhile IF the authors used a data analysis technique that could cope with the whole bone data. But they don't. Hence why lots of the small bird bones cannot be quantitatively analysed, and the authors rely on scoring metrics for midshaft trabeculae. It feels like the authors have embarked on a data collection exercise without having a sensible way of analyzing the resulting data. Ultimately, that means that only medium-sized birds and non-avian theropods are actually analyzed using the preferred methodology. The trabecular architecture of small birds and large dinosaurs cannot be quantified with the present methodology. I think this is a shame, and potentially obscures interesting scaling patterns and limits meaningful comparisons.
Validity of the findings: I think the endeavour of documenting and describing trabecular architecture across birds and non-avian theropods is worthwhile. However, I find the attempt to link fabric orientation and limb posture in the discussion to be weak.

Specifically, in the broader context of Parts II and III, it feels like the authors have missed an important stage:

Part I - Measure trabecular fabric in birds and dinos
Part II - Assuming fabric direction correlates to midstance posture, what is the mechanistic link?
Part III - Apply mechanistic model to dino fabric direction to predict midstance posture

But between Part I and Part II, I was expecting an analysis similar to those in the primate literature, in which trabecular variables are actually shown to be correlated to locomotor behaviour. In the Supplementary Materials, the authors have attached an accepted manuscript on modern bird kinematics, in which they have midstance posture for 12 species of bird, for which they also have fabric orientation. Why is there no attempt to correlate the two, since Part III relies upon there being a discernable postural signal in dinosaur trabecular architecture?
Additional comments: Specific comments:

Ln 754, 756, 758 - "Most", "A small proportion". Be specific about the number of specimens that could be quantitatively analyzed.

Ln 843-844 - The construction of 'geometric representations'. This proceedure is obviously not ideal, but is seemingly the only way to visualise the trabecular patterns in the larger theropods. If this were purely an exercise in visualization, this would be fine. But the authors then use this 'data' from the model in the stereoplot of Fig 22. We therefore need to check how well the orientation data extracted from the models agrees with those calculated automatically. The modelling proceedure should be repeated on 1-2 modern birds for which fabric orientation was also quantified, just to check the two metrics agree.

Ln 988 - How was pneumatisation determined?

Ln 998 - It would be nice if the authors included some orthoslice images of the original CT data for the larger theropod dinosaurs. So that readers can judge the quality of the underlying scan data

Ln 1128-1129 - There needs to be a better justification than, they were different so we excluded them

Ln 1250 - Mention regressions statistics here?

Ln 1276 - Logistical constraints such as....?

Ln 1487 - Of the 4 ICC scores calculated, two were 0.46 and 0.69. These cannot be considered 'high'. They are poor-average. I would go so far as to say that an ICC of 0.46 for 5 people is so bad that we shouldn't be interpretting that data at all.


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: CANCELLOUS BONE AND THEROPOD DINOSAUR LOCOMOTION. PART I—AN EXAMINATION OF CANCELLOUS BONE ARCHITECTURE IN THE HINDLIMB BONES OF THEROPODS
Review round: 1
Reviewer: 2

Output:
Basic reporting: This is one of the best-written manuscripts I have reviewed. Two adjustments will slightly raise clarity and phylogenetic compliance. Be more specific with "this" and "the nature of". The latter could mean anything, and therefore conveys little. When you say "reptiles" clarify that you mean extant, non-avian and/or sprawling reptiles, varanids and crocodilians, or "other reptiles" (when also referring to birds and other theropods). There are a few suggestions for conciseness ("Because.." rather than "owing to" clauses), but the original wording is clear.

Also, be careful about "plesiomorphic" taxa; it's too blanket a characterization. Make sure the reader knows you're referring to the pelvic locomotor system relative to the condition in birds. Birds are just Allosaurus-line theropods in other ways.

Cite Tsai's work a little more for hip morphology, including his PhD thesis. You're correct that it's "worthy of .. study", and his soft tissue reconstructions are relevant to the results here (and vice versa).

The study is self-contained, and sets the stage for further installments of the research. The paper could start on line 493, but the (dissertation-derived?) background is made for online journals.
Experimental design: "Check" for all of the PeerJ criteria.

Fabric tensors are the best! It's wonderful to see them introduced to paleo so lucidly. Maybe (occasionally) refer to u1-3 as principal orientations in the results, to remind the reader.

The reconstruction protocols are actually replicable as described! The methods here and elsewhere are often a model of clarity and completeness.
Validity of the findings: Intriguing results from comprehensive methods.
Additional comments: Comments expanding on those above (including praise for the methods) are embedded in the reviewed manuscript. I found the trabecular architecture figures more informative than the volume-of-interest figures, although I recognize the latter's value. Splendid work, and I look forward to the rest of the opus.


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: CANCELLOUS BONE AND THEROPOD DINOSAUR LOCOMOTION. PART I—AN EXAMINATION OF CANCELLOUS BONE ARCHITECTURE IN THE HINDLIMB BONES OF THEROPODS
Review round: 1
Reviewer: 3

Output:
Basic reporting: This article presents the preliminary results of CT scanning and 3D model construction from the CT data that surveys the cancellous bone structure in the hind limb bones of a range of living and extinct "reptiles" (crocodilians, lizards, birds, dinosaurs) and one human. It interprets the variety of forms of cancellous bone structure observed in the specimens in terms of the types of loading that the animals experienced when they were alive.

The paper is clearly and well written, if a bit verbose.

There is a MOUNTAIN of references that more than demonstrate the authors' familiarity with pre-existing work and ideas in the field.

The large number of figures support the findings reported in the text, but some more work is needed with the figures (see General Comments below).

The truly epic Table 1 thoroughly documents what specimens were examined and how they were scanned. The details provided should enable anyone to repeat the observations presented in the text.

The results are self-contained. Occasionally the authors do refer to the other two articles that are associated with this theropod  CT scanning, but this is not a hindrance to understanding the current work.
Experimental design: The current paper satisfies all four of the stated criteria.
Validity of the findings: Again the current paper satisfies the four criteria. The authors make it very clear that very small bones caused them problems with both scanning and processing to build up a 3D model.
Additional comments: For the most part I enjoyed reading this paper. My only real complaint is that it reads like a thesis. I think a lot of the text could be reduced. This is especially so with the exhaustive reporting of the orientations of the trabeculae for ALL the bones and ALL their regions (proximal, mesial, distal) and sub-regions. My brain quickly overflowed with the blizzard of observations. I just couldn't take it in. I was relieved to find paragraphs summarizing the main trends and patterns in the Discussion.

Some specific comments follow:

Section I.3.4 Statistics

Starting at Line 925 the authors refer to ‘body size’. What do they mean exactly - linear body dimensions or mass? There are several studies that make use of femoral dimensions to estimate body mass. The recent, statistically rigorous work of Campione et al. would be a good place to get regression and scaling relationships to estimate the masses of the various animals that gave up their bones for analysis.

The first of only two word usage/typo mistakes seen: Line 1149 needs a ‘the’ after 'Throughout'.

Section I.5.1

This summary (big picture) section REALLY needs some graphics to help the reader visualize the trends and patterns reported for each of the regions of the bones (proximal, mesial, distal). The messages from the long, verbose interpretations could be much more effectively done by replacing them with some schematic figures. Figure 44 is a nice example of a summary figure. I think several more like it would greatly help in the presenting their findings and interpretations to readers.

Lines 1650-1661 is where the authors report the ranges of ‘sweep’, and bemoan the fact that the local variability of orientations makes the reporting of mean orientations somewhat “mean-ingless”. What if they compute and report the standard deviations about these means?

Section I.5.3
The authors go to the trouble of deriving an expression (equation 6) for the critical torque to initiate buckling, but then don’t do much with it except give a one sentence interpretation of the equation. They have all the geometric data, and with body mass estimates from regression analyses, they could actually compare ciritical torques for the specimens they scanned.

The second sentence structure complaint: Line 1849 doesn’t need the parentheses.

Figure comments and suggestions:

For all the figure captions the scientific names of animals ought to be italicized. Also, I think the common names for extant forms ought to be included as well.

Figure 12 – a 3D, oblique view of a femur with the three, mutually orthogonal axes displayed in proper perspective would be better than the current effort. I think the directions of +x and +y in the current illustration could be interpreted in more than one way.

Figure 15 and onwards – I would like to see at least one cut-away view for each bone that reveals the original trabecular orientations that were used to derive the u1, u2 and u3 vector fields. This has been done in selected figures, but it should be a consistent feature in all the figures.

Figure 19 – for the Allosaurus and Tyrannosaurus results we don’t get the usual red, blue and green vector fields. Instead we are presented with a new style of intersecting surfaces. These surfaces certainly show the trabecular trends, but for consistency and to allow comparison with the other scans, I think the vector fields should be shown as well. I know that the identification of what the colours of the surface represent is mentioned in the main text, but repeating it in the caption would be a great help. Placing a graphical colour legend right in the figure would be even better.

 Figures 25 and 26 – the jumping up and down of the figure labels – ‘A’ on top, then dropping down to ‘B’, then back up to ‘C’ is disconcerting, and not seen in previous figures. This needs to be fixed.

Figure 33 sequence ‘D’ through ‘J’. I found it difficult to see the separate surfaces and perceive their orientations, no matter what view was shown. Also, the colours are rather muted as if they are being partially masked by the grey, semi-transparent surface of the bone.

Figure 36, 39 – the red overlays of parts ‘F’ and ‘G’ , and ‘C’ of figure 39, thoroughly obscure the trabecular details of the CT images. I think it would be best to shift the red overlays to lie immediately below the original images.


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: CANCELLOUS BONE AND THEROPOD DINOSAUR LOCOMOTION. PART I—AN EXAMINATION OF CANCELLOUS BONE ARCHITECTURE IN THE HINDLIMB BONES OF THEROPODS
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: Author Response to Reviewer 1: As outlined in the Methods, the qualitative models produced (e.g., Figs 19, 26) were derived directly from the CT scans for those fossil specimens that were imaged using medical-grade machines. They simply convey the observed 3-D patterns in an alternative graphical format (since the fabric vector analysis was not possible), with no ‘higher level’ interpretations added on. Hence they portray just as much data as the fabric vector field plots.

Similarly, the verbal description of fabric vector fields (in an anatomical context) is a necessary item of data, because the cancellous bone architecture of theropod limb bones has never been described before; so the first thing to be done is to lay down the anatomical framework, which is a key objective of this exploratory study. Given the comparative theme to this study, it is important to present the data in as much a structured order as possible, in terms of both bony element and phylogeny.

Now that we have established a general anatomical and comparative background to work from, it is envisaged that future, more focused investigations will be able to report their findings in a manner more like what the Reviewer describes.

Reviewer 1 Response: Please try to provide a more concise summary of the broad trends. Both Reviewer 1 and Reviewer 3 have requested this change, but the authors have chosen not to do so. I appreciate this paper is derived from a thesis, and that summarising the main trends will be more work, but we are trying to help. I think your research is more likely to be cited if you do the reader a favour and spell out the main messages for them. I do not find the argument that a summary might only further confuse the reader convincing. If the authors have chosen to use such a mix of methodologies, across a diverse interspecific sample, and in such a verbose manner, then the burden of responsibility is with the authors to take on summarising the results for the reader. The authors themselves refer to the manuscript as a ‘comparative study’. How is this the case if it is not possible to make some broad comparisons and summarise trends across the sample?

Author Response to Reviewer 1:The data used in this set of studies collectively occupy about 3 TB (and some of the individual files are massive, too), which makes uploading the data to an online repository both impractical and prohibitively expensive. Nevertheless, all the data and code used are permanently accessioned into the Geosciences Collection of the Queensland Museum; the data and code are stored in a databank within a fire-proof safe on-site at the Museum. Anybody is able to freely access this permanent repository upon contacting the Collections Manager. (In future, this data will be made available online, but there are not available avenues for this now.) We originally had stated this solely in the Acknowledgements section, but now have made a statement in the Methods section as well (page 20, lines 613-616). Similar statements concerning data availability have now also been made in the Methods sections of Parts II and III.

Reviewer 1 Response: Again, this is shame for the authors. The work is more likely to be cited if you make your scans available for download from an online repository. Could you consider at least making the isosurface models you generate available?

Author Response to Reviewer 1: See overview comments above (re intraspecific scaling)

Reviewer 1 Response: I don’t agree with the authors’ assertions in-text that ‘It was…not possible to quantify potential intraspecific variation in bone architecture’. The data in Figure 22B clearly give an idea of fabric variation in the larger modern bird species. And more importantly, the variation does appear considerable. When discussing the difficulties associated with intraspecific variation in-text, please explicitly draw the reader’s attention to these figures and acknowledge that within-species variation does appear to be considerable in modern species.


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: CANCELLOUS BONE AND THEROPOD DINOSAUR LOCOMOTION. PART I—AN EXAMINATION OF CANCELLOUS BONE ARCHITECTURE IN THE HINDLIMB BONES OF THEROPODS
Review round: 2
Reviewer: 2

Output:
Basic reporting: The writing is cogent, and needs no further modification. The authors thoughtfully incorporate broader and specific suggestions (e.g. line 405), and additional literature (such as in line 1804).

Reviewer 1 asks about availability of the raw and reconstructed CT data. I applaud the authors' literal safe-keeping of the data at the Queensland Museum (lines 613-616 and response-to-comments file).
Experimental design: As with the first submission, the research question and experimental design are insightfully and thoroughly described. The exhaustive methods are replicable, and Reviewer 3 is correct about their useful summary in the discussion.
Validity of the findings: Valid results and applicable findings, as the subsequent manuscripts show.
Additional comments: The revised manuscript is acceptable as-is.


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: CANCELLOUS BONE AND THEROPOD DINOSAUR LOCOMOTION. PART I—AN EXAMINATION OF CANCELLOUS BONE ARCHITECTURE IN THE HINDLIMB BONES OF THEROPODS
Review round: 2
Reviewer: 3

Output:
Basic reporting: The manuscript meets all four criteria.
Experimental design: The manuscript meets all four criteria.
Validity of the findings: The data are derived from a limited set of specimens, hence the true nature of the variation between the sampled bones is not that well known. However, the authors recognize this and comment on it.

The authors do draw attention to their finding of the oblique trabeculae in the diaphyses of bird femora and tibiae. I don't know if this conflicts with the first point in points for reviewers at right.
Additional comments: This paper is an improvement on the previous version. It was a much less onerous read, although I still find the long series of descriptions of the u1, u2, u3 trajectories a bit heavy going.

My only quibble is with the interpretation of equation (6), with diameter 'd' in the numerator, and length 'l' in the denominator. Is it not the case that propensity for buckling is proportional to the square of 'd' and inversely proportional to the square of 'l'? This is not what is stated in the text.


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: CANCELLOUS BONE AND THEROPOD DINOSAUR LOCOMOTION. PART II—A NEW APPROACH TO INFERRING POSTURE AND LOCOMOTOR BIOMECHANICS IN EXTINCT TETRAPOD VERTEBRATES
Review round: 1
Reviewer: 1

Output:
Basic reporting: I have no concerns about the basic reporting of the manuscript.
Experimental design: It is not clear to me why the preferred workflow for determining posture should require knowledge of bone architecture PLUS centre of mass PLUS segment masses PLUS muscle geometry PLUS muscle activations  PLUS material properties etc….all of which will introduce errors when applied to fossil material. Why have the authors not at least attempted to correlate trabecular architecture directly to midstance posture or whatever behavioural parameters they wish to predict in extinct taxa? As on lines 182-184, the authors are supposedly aiming for “fewer assumptions (i.e. model simplicity)”. Whilst they are undoubtedly an impressive undertaking, these models are far from simple, such that we have ended up in situation where we’ve validated the protocol on a n=1 chicken (which is suboptimal itself, see below) and then applied it to only two fossils in Part III.

Ln 191. The choice of a chicken to validate the protocol seems unjustified. Firstly, this is not the same chicken as from Part I, so we actually have no idea what this particular individual’s trabecular fabric is. Secondly, the Part II chicken wasn’t able to be dissected, so the muscle-specific maximum forces had to be scaled from the literature from a different strain. Thirdly, the fabric orientation of the Part I chicken was not able to be quantified because they were so small that the continuum assumption is invalidated, so we can’t quantitatively compare chicken against chicken.

Ultimately, this means the authors cannot test whether this technique successfully predicts the midstance posture of a chicken. Instead, max. principal stress orientation is compared to the mean for all birds in Part I. So effectively we’ve shown that this protocol can predict a bird-like posture for a chicken. But what I want to know is: can the method predict a chicken-like posture for a chicken? Especially because the supplementary manuscript attached on bird kinematics shows (Bishop et al. PLoS ONE, Fig 1D) that there is a distinct scaling relationship in modern bird posture with leg length.

In order for this technique to be truly ‘validated’, we need to know whether it can successfully distinguish between the mid-stance posture of, say, an ostrich and chicken on the basis of trabecular fabric. If the technique cannot distinguish between two modern taxa with different postures or locomotor repertoires (with all the luxury of associated soft tissue data), does it stand a chance with fossil species?

A further advantage with an ostrich or suchlike is that the authors could then directly compare max. principal stress results from the FEA to the Quant3D within the VOI spheres. And then have a more detailed understanding of where the stress and fabric orientation are agreeing/disagreeing, which would get around the problem highlighted by the authors in Lns 732-734.

Lns 731 – This needs further justification, at least some references. Presumably this is why the authors chose model 8 as their preferred model, over 7? This decision also needs further discussion. It seems like there is very little difference in angular deviation within the femoral head between postures 7 and 8, yet 8 is considerably worse within the distal condyles.  Why favour 8, rather than trying to minimise the sum of deviation across the two regions?

Ln 812 – “worst to best”.  Are the actual joint angles associated with models 1-8 documented anywhere? Why were these 8 chosen out of all the potential options? Why only 8? And when did the authors decide that convergence had been reached? On the basis of what criteria?

838-840 – Do you have any a priori hypotheses about why you would expect sigma1 to match the fabric orientation in this region, whereas correspondence to sigma3 is only discussed in relation to the femur.

Why is no stereoplot for the tibiotarsal results included?

Ln 1042-1043. I disagree. Part I clearly shows that the methodology fir quantifying fabric orientation breaks down both at small and large scales.

Ln 1075 – This is only the case because the authors have selected model 8 as their ‘optimal’. Model 7 seems equally feasible, and would negate this statement.
Validity of the findings: Ln 923 – “the validity of the approach”. I disagree, I do not think the authors have adequately examined the validity of the approach on a modern theropod, because we don’t know what the trabecular architecture of the modern theropod actually is. What if the chicken fabric orientation could be plotted in the stereoplot space, and it sat at the extremities of space occupied by modern birds? Suddenly the correspondence between fabric orientation and stress direction would not be convincing. I do not think comparing stress orientation to a mean fabric orientation for birds is valid.

Lns 738-739 summarise my concerns about the endeavour in its current form. The authors state “it has been shown that birds as a whole appear to demonstrate a largely consistent pattern of cancellous bone architecture in the femur, tibiotarsus and fibula”. Yet the attached Bishop et al. PLoS manuscript shows that the same birds adopt different levels of crouch at midstance. So, in modern ground-dwelling theropods, posture changes but trabecular bone stays the same. I therefore fail to understand how the present attempt to predict posture from trabecular bone can be justified.
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: CANCELLOUS BONE AND THEROPOD DINOSAUR LOCOMOTION. PART II—A NEW APPROACH TO INFERRING POSTURE AND LOCOMOTOR BIOMECHANICS IN EXTINCT TETRAPOD VERTEBRATES
Review round: 1
Reviewer: 2

Output:
Basic reporting: The first three criteria are all met. However, there are several places in the methods, results, discussion, and figure captions where the reader is directed to parts I and III of the series of papers on this project. I would prefer to have this information immediately available, especially the observed bone trajectories to compare with the computed compressional stress trajectories.
Experimental design: The paper meets all four criteria here.
Validity of the findings: All four criteria are met here.
Additional comments: The present text was a much more manageable read compared to Part I and its 44 figures. It is for the most part well written, but I do have some comments and suggestions.

At many places in the text, especially the introduction, there are what appear to be excessively long lists of citations of papers supporting the authors’ claims. These ought to be pared back.

Line 113: I was amused the specific phrase “normal DAILY activity”. Does this mean the results of the study are not relevant to nocturnal animals?

Lines 164-166: another epic citation list. Do you really need ALL of them?

Line 587: Equation (3): at first glance I was rather mystified by this cryptic expression with a square root within a square root. I spent a few minutes deriving it for myself, and then it seemed very obvious. I think for less mathematically inclined readers the authors might want to include a brief derivation of this expression.

Line 731: the authors state “... since hip angles are presumed to be more important for determining overall posture in bipeds”. This sounds like it might be true, but I think a demonstration or justification of this statement ought to be made. I think a graphical one would be good to see. This could show the large angular displacement of the foot for a small angular displacement of the femur.

Lines 905-910: I think more than a qualitative assessment of the degree of correspondence between stress trajectories is needed. Some sort of statistical measure is needed.

Paragraph I in II.5.2: both the abstract, introduction and the title of this section refer to the applicability of the method and results of the present study to extinct taxa. However, the only mention of this topic after the introductory remarks is one sentence in this first paragraph, and nowhere else. I was looking forward to what the authors would say on this matter, but was disappointed. I suspect I have to wait until I read Part III for the gripping conclusion.

Figure 4: Part A: It was nice to see the decreasing angular deviations between Ϭ1 and u1 with iterations of the modelling process, but I would like more explanation for the sudden increase in deviation for the medial femoral condyle at stage 8. Part B: A sequence of full lateral views of the 8 steps of the skeletal model from the initial neutral pose to the solution pose would be much more informative than the few obscured stick views currently shown.

Figure 5: I would really like to see illustrations of the original (CT derived) bone trajectories side-by-side with the computed stress trajectories. I don’t think all the views are necessary here, just a select view to show the typical results. For parts I and J some spherical statistics would be very useful to quantify the degree of alignment of the various vectors. Also, there is no explanation of the what the different colours indicate in the caption.

Figure 6: I don’t think ALL these examples are needed. Reduce the number and include the original bone trajectories for readers to make direct comparisons.

Figure 7: Include the original bone trajectories for readers to make direct comparisons.


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: CANCELLOUS BONE AND THEROPOD DINOSAUR LOCOMOTION. PART II—A NEW APPROACH TO INFERRING POSTURE AND LOCOMOTOR BIOMECHANICS IN EXTINCT TETRAPOD VERTEBRATES
Review round: 1
Reviewer: 3

Output:
Basic reporting: The writing is clear, although less coherent in places than in the first contribution.  The manuscript is technically sound. It works as a self-contained study but is well-integrated with the companion manuscripts.  Cite a convergence paper by Tseng (2011) to justify the number of nodes and elements you settled on (p. 24).
Experimental design: Wonderful application of inertia relief, and good mathematical approach to trabecular and principal stress correspondences. NOT a necessary revision, but a suggestion for the future: You can improve the leg segment reconstructions with more interpolation or surface smoothing proximally. Currently they're a bit choppy. You're approximating the inertial properties just fine and the error is certainly small, but smoother anatomy is more evidently authentic.
Validity of the findings: Fascinating correlations between tertiary principal stresses and trabeculae, and the deviations are instructive (as with the distal tibiotarsus).
Additional comments: Most comments about the previous manuscript in the series apply to the current one. The attached edited copy has suggestions pertinent to this particular manuscript. Definitely expand Figures 6 and 7to include at least one comparative sub-figure from the first manuscript. The accretion is good to highlight how you're building an integrated case, although it may seem unnecessary when the first manuscript is a few clicks away.