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: A BIOINFORMATICS APPROACH TO IDENTIFYING WOLBACHIA INFECTIONS IN ARTHROPODS
Review round: 1
Reviewer: 1

Output:
Basic reporting: Thank you for the opportunity to review the manuscript submission “A bioinformatics approach to identifying Wolbachia infections in arthropods”. Pascar and Chandler present a method by which to screen SRA libraries from arthropod sequencing projects for evidence of Wolbachia infection. Wolbachia is the most common symbiotic bacterium across insects, and has sculpted the evolutionary trajectories of many lineages, allowing for niche expansion and creating reproductive barriers through various mechanisms. This is a fun study that is a good match for PeerJ, and takes advantage of the vastly growing amount of short read data with the intent of picking up previously undescribed associations with Wolbachia. The manuscript is nicely written and extensively referenced. I was happy to see the scripts and lots of intermediate data in the supplemental. While there are some interesting findings (ex., newly described Wolbachia associations, and supergroup assignments for previously un-assigned strains), some of the methods are problematic and should be re-visited.
Experimental design: Major Comments:

These are ones that would affect the phylogenetic reconstructions, and prevalence estimations.

1) The choice of reference loci (ie., wsp, ftsZ, groE) should be fine for detecting Wolbachia reads, but the use of wsp in phylogenetic reconstruction is problematic due to extensive recombination. The authors touch on this with the now retired Supergroup G, and reference Baldo and Werren (2007) (line 62), which is a great example of the problematic nature of wsp.

2) It looks like there are mate-pair libraries included in the samples. Are different mapping/assembly parameters used for MP vs PE read pairs to account for different directionalities? Along those lines, were different fragment sizes controlled for? You may be missing some hits if the pairs are not handled correctly.

3) Most of the host species have multiple SRA libraries that originated from the same BioProject/DNA extraction. Wolbachia sequences were assembled separately for each of these positive libraries, and then these “multiple strains” of Wolbachia were used in phylogenetic reconstruction. However, these data represent the same Wolbachia strain, just a different library preparation. This is misleading, as it looks like the authors have recovered multiple strains from the same species.

4) I would imagine that the size of the host genome would be an important consideration for the number of reads used for Wolbachia detection, as the ratio of host:Wolbachia DNA will be different and have an effect on detection.

Secondary Comments:

There are a few things that, while they should not have an effect on the major findings of the paper, could benefit from some smoothing out.

5) The authors choose to search arthropod SRA libraries, but blast them against reference loci from supergroups A-D (with C and D infecting nematodes). An explanation of why they included C and D loci would be beneficial, as we would not expect to recover these supergroups from arthropod samples.

6) How/why reference gene alleles were chosen could benefit from some discussion. For example, there are multiple wsp alleles from Nasonia vitripennis, unequal numbers of alleles chosen per reference gene, some of the groE operon alleles are not complete, etc. I really like the way Table 2 is laid out and the choice of “positive controls” in the analysis. Why not use these positive phylogenetic controls as the reference loci?

7) I’m having difficulty matching what is in the scripts with what is in the methods. In the scripts it looks like first the libraries were pre-screened for wsp hits, and then positives were reanalyzed to pull down the other loci?

8) Is the non-coding region of the groE operon used in phylogenetic reconstruction?

9) Line 144: What length of matching basepairs was considered “sufficient”?

10) Line 145: What parameters were used for Gblocks?
Validity of the findings: 11) The bootstrap values seem very very low (0’s, for example) for some clades. I would re-visit these.

12) It would be nice to see some statistics on read coverage that the authors obtained for their reference loci.

13) I like the discussion of the factors that can contribute to false negatives/positives and skewed Wolbachia prevalence using the presented method. While it would take significant additional work, the authors could include host loci to see if Wolbachia and host have equivalent or drastically different read coverage (to get at HGT vs infection). Similarly, the authors could look at their libraries and see if those with positive hits were more likely to be “wild-caught” (addressing hypothesis #2 in the discussion).
Additional comments: Minor Comments:

14) The last sentence of the abstract is unclear: what is meant by “similar methods can be replicated”?

15) The introduction is generally well written though I might suggest reordering such that lines 51-56 go along with the first paragraph in which the authors discuss Wolbachia prevalence.

16) Line 92: Insecta is a class, not an order.

17) Throughout the methods “samples” is used a lot, which I think is confusing given my earlier comment (#3). I would suggest using, “species”, “samples”, and “libraries”, or something similar to help differentiate between these levels of organization.

18) Line 130: s/Velveth/Velvet/

19) Table 1 would benefit from some reformatting. The definition lines (taken from NCBI) are not descriptive – ex., the first 5 ftsZ alleles have no host species listed. My preference would be to show host species, supergroup (if known), length of the sequence, and citation, similar to what you have done for table 2, which I like very much.

20) The phylogenetics methods should be re-located from the figure captions to the methods section.

21) Table 3: what is the difference between “?“ and “-”?

22) The literature search in the supplemental can be included in the main manuscript text.

Summary:

There are some kinks that need to be worked out in regards to the methods, but I think the take away of this manuscript is a nice contribution and I hope to see an improved version.


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: A BIOINFORMATICS APPROACH TO IDENTIFYING WOLBACHIA INFECTIONS IN ARTHROPODS
Review round: 1
Reviewer: 2

Output:
Basic reporting: See below
Experimental design: See below
Validity of the findings: See below
Additional comments: This manuscript by Pascar & Chandler presents the results of a Wolbachia screen within short read samples stored in the SRA public database of the NCBI. The screen was performed by (partly) downloading 2,545 short read libraries generated from 288 species and mapping these to three Wolbachia genes. The matching reads were assembled and their phylogeny analysed together with reference sequences to determine supergroup affiliation of the detected strains. This way, 8 novel Wolbachia – host associations could be determined.
I think the idea of this study is very cool and the analyses seem to be well planned and performed. Short read libraries are indeed a valuable source for symbiont data that is often neglected, and this can’t be stressed enough – this paper is a welcome contribution in this respect.

I have however two major reservations that I feel should be addressed before this should be published, one regarding analytical approach, and one regarding the form:

1) The data seem to be of mostly preliminary nature, i.e., it appears that the authors have stopped at a point where things become most interesting. The approach, while not totally new, is certainly well suited to detect bacterial symbionts in arthropods, so why not check for more (all?) endosymbionts known from arthropods? As opposed to PCR screens, this requires little effort and would hardly take more time than checking for Wolbachia only. Furthermore, 288 species does seem like a low number for all arthropod species in the SRA database (maybe I am wrong there). I fear that the authors’ rather restrictive filtering has led to the exclusion of a number of potentially interesting samples. I think there is a really good chance of some cool findings with such a screen. There have been countless PCR based screens and meta-analyses investigating the incidence of various endosymbionts. Here, you present an alternative, more or less unbiased dataset, potentially providing independent evidence for these previous analyses.
As an alternative a more in-depth screen, why not try to extract whole Wolbachia genomes from at least some of the detected associations? This would demonstrate it actually is possible to ‘assemble complete Wolbachia genomes’ as the authors mention in the conclusions section, and I know that the Wolbachia community would welcome such an effort.
I have other comments about the methodology (listed below), but I think this is my biggest issue with the manuscript.

2) Related to point 1), I think the authors should clarify the narrative of the manuscript. In its current form, the reporting switches between a ‘proof of concept’ kind of paper and a Wolbachia screen with a new approach. I feel that the latter is the better option given that the concept is not entirely new. However, as mentioned in point 1), this screen should be extended to potentially yield more meaningful insights.

Please find more details on these points and other, minor comments below. I hope you will find these constructive:

Introduction
The introductory paragraphs are mostly about the biology of Wolbachia. There’s nothing wrong there, but I think this could be condensed and the readers referred to one of the excellent Wolbachia reviews around. Instead, the authors should expand more on the motivation behind their study and background of their methodology. They should also mention other studies with a similar scope (they do this later in the discussion section) and how their study differs from these previous studies. A number of bioinformatic tools exist that enable the extraction of microbial reads from eukaryotic short reads (e.g., Blobtools or Anvi’o), maybe these should also be mentioned. You may also want to have a look at the recently published study on honey bee symbionts that essentially uses the same approach as your study (https://peerj.com/articles/3529/).

L34
Change ‘α-proteobacteria’ to ‘α-Proteobacterium’

L36
Suggest to change ‘distribution’ to ‘incidence’ or ‘frequency’

L72–73
ftsZ and groEL don’t exactly qualify as fast evolving.

L77–79
wsp is highly recombinant and therefore inherently unsuited as phylogenetic marker or to ‘identify groups and strains’ of Wolbachia

L106ff
As mentioned above, it is unclear why you excluded other sequencing technologies or single library layouts. You may be missing quite a few interesting samples.

L122
What was the rationale behind choosing these particular loci? When using multiple loci, it would make sense to use the MLST genes, this would enable comparison with many other strains. Much more important than multiple different genes (why should one not be sufficient?) however, is the inclusion of more divergent Wolbachia lineages. You mention many Wolbachia supergroups in the introduction, and for all of these, there is some genetic data somewhere that can be used for screening. Of the four supergroups you do employ, two (C & D) were never found in arthropods, so you basically only searched with A and B groups. I suspect that may also be a reason why these were the only hits that were recovered. Further, as mentioned above, I think it would be worthwhile to check for other common symbionts (Rickettsia, Spiroplasma, Arsenophonus, Cardinium, Sodalis, etc).

L123
Does this mean 98bp when summing the length of all reads? Otherwise you may have excluded short reads from earlier Illumina platforms (50bp or 75bp reads were not uncommon).

L127
Were these randomly chosen? It may be better to assemble all the samples and then chose the best contigs. Assembling these tiny regions shouldn’t be computationally prohibitive. Also, it might lead to the detection of multiple different strains in a single host species.

L144
What did you consider of ‘sufficient length’?

Results section
It would be nice to have a graphical overview of the taxonomy of the samples, i.e, how many samples were from each of the investigated taxonomic groups. Also, was there any evidence for geographic clustering? Did you check for tissues from which the samples have originated? I think that looking at the metadata might reveal some interesting patterns.

L153
For the positive samples, were always all of the genes recovered?

L167
I think that four tree figures are not really needed, as they all show similar information. Also, differences between the trees are not really discussed anywhere. I suggest to keep the concatenated tree in the main manuscript and move the rest into the supplement.

L193
I would disagree that the threshold used (three matching reads) is to strict. The low number of infected species might be due to the reference sequences used.

L218
One of the most interesting findings of this paper is hidden here: the detection of supergroup B Wolbachia in Anopheles gambiae. Wolbachia seems to be mostly absent in Anopheles, and it has been shown that there an incompatibility between its native microbiome and Wolbachia may be the reason for this (http://www.pnas.org/content/111/34/12498.short). The only study (I know of) claiming to have found infections in natural populations is the one you cite (Baldini et al 2014). Frankly, this paper is not very convincing – they sequenced two complete Illumina lanes and only got a handful of Wolbachia reads which they claim belongs to a distinct phylogenetic lineage (based on questionable methods in my opinion).
If you can demonstrate that this is indeed a supergroup B Wolbachia strain, this would be very neat and interesting to many people, both working on Anopheles and Wolbachia. Even better, if you can assemble the genome of this Wolbachia strain (which should be feasible), and show that this is not only a chromosomal insertion of the host, this might make for another very interesting paper!

L239
HGT could be assessed by checking read pairs after mapping. If only a single read of a pair has mapped to the Wolbachia target, it can be tested if the other read matches to a host chromosome.

Final comment
This may seem like a lot of nagging, and I apologize for this. However, this is because I really feel that with a little effort, this paper has the potential to become an exciting contribution.


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: A BIOINFORMATICS APPROACH TO IDENTIFYING WOLBACHIA INFECTIONS IN ARTHROPODS
Review round: 1
Reviewer: 3

Output:
Basic reporting: This is a very well put together paper. The structure, language and context provided are more than appropriate for publication. I would also like to commend the authors for the completeness of the submission, for not only including raw data, but the code and literature search methodology to reproduce the work.
Experimental design: I believe the experimental design element meets the criteria for publication. Methods are clear, rigorous and clearly address the stated research goals and I only have one minor comment here.

Minor comment:
Diagnosing Wolbachia infection [lines 119-125]. My reading of this suggests that +ve infection was declared even if only one of the reference genes met the matching reads criteria - is this correct? If so, how robust do you think this criteria is - did you do any benchmarking with known infected samples? Also, how do your infection rates change when you set the threshold to be that i) at least 2 and ii) all reference genes must meet the matching criteria?
Validity of the findings: I feel the data is sound and the conclusions 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: A BIOINFORMATICS APPROACH TO IDENTIFYING WOLBACHIA INFECTIONS IN ARTHROPODS
Review round: 2
Reviewer: 1

Output:
Basic reporting: I am so pleased to see such a thorough set of revisions on the manuscript submitted by Pascar and Chandler. Please find attached my suggestions for some last smoothing over. I have also included some additional experimental suggestions. I do not find them necessary for publication of your results, but they might be nice quick additions, especially if you are familiar with the bioinformatics. There are a few references that could benefit from updates (please see general comments). I think this paper will be a nice addition to the literature.
Experimental design: - I maintain that wsp should not be used for phylogenetic reconstruction. I think at minimum there should be a discussion of its utility (or lack there of). The references in lines 65-67 came before the discovery of wsp recombination. I think it is fine to use wsp for detection, but why not just use ftsZ and the GroEL operon for phylogenetics?

- It isn’t clear what constitutes “unrealistic” sizes of genomes for determining HGT. Insect genomes vary in size by orders of magnitude (from <100Mbp to >6Gbs). Additionally, I do not think the coverage statistics are calculated or reported in a clear way: "Host genome size if same cov. as Wo" is not intuitive, especially when you are comparing that value in Mbp to host genome size as a C-value. The authors mention the difficulties of obtaining whole genome coverage, but maybe coverage of a single copy gene, or the arthropod BUSCO set would be helpful. Many genome sizes are missing from Table 4, but are listed on NCBI for the host genome assemblies that came from these reads (ex., Gerris buenoi = 994Mbp, Diabrotica virgifera = 2.4 Gbp, Diachasma alloeum = 388 Mbp, D. citri = 485 Mpb, and many others).

- It appears that BisSeq libraries were used in screening. These probably are not useful, as they are not the true genomic sequence, but will contain converted nucleotides from the bisulfite processing.
Validity of the findings: No issues here. Please see my more general comments below.
Additional comments: - Line 150: For the readers' convenience, please include the strain names of these genomes in the text (ex., wPip_Pel, wMel, wNo, etc).

- I think in figures 1 and 2, there are many species that should have the squares indicating supergroup was previously known (ex., For D. simulans there are many papers; many works by Stouthamer show Trichogramma pretiosum has supergroup B, including Lindsey et al 2016 Genes|Genomes|Genetics for that exact genome + placement of others like wDi from D. citri; O. brumata and D. coccus have also been previously assigned a group I believe). Many of these appear labeled in Table 3, so it isn’t clear why they are not all labeled on the figure.

- The reference for the Trichogramma pretiosum wTpre Wolbachia genome (Table 3) should be Lindsey et al 2016 Genes|Genomes|Genetics. (Currently the only reference in the citations is for the Systematic and Applied Micro paper, which talks about taxonomy and is referenced at line 48.)

- Several of your assembled Wolbachia genomes already have published assemblies from these reads/biosamples (ex., wDacA, wDacB, wTpre, etc). The wTpre genome, as well as the wDacA and wDacB genomes, were computationally separated from their respective hosts and used many of the same methods as you (ex., sequencing coverage), so may be worth referencing at lines 86 and 370. Additionally, you could align your versions with the published versions to see how well your iterative assembly method worked (Ex., use nucmer/mummer to get an estimate of the similarity).

- I like that the authors attempted to look for Wolbachia co-infections. Some of these have been published (ex., D. coccus: Ramírez-Puebla et al 2016 Genes|Genomes|Genetics), which the authors reference (line 280). It gets a little complicated, because the phylogenetics place just the B strain in D. coccus, but the Wolbachia assembly appears to be a chimera of the A and B, which is what I would expect given what we know about this dataset and the assembly method. Addressing this in the discussion would be appreciated.

- I like that the authors have urged others to include better metadata in their biosample submissions. I am not sure what the appropriate amount of filtering to suggest would be. While clearly the symbiont reads are useful, someone who is not looking for those could be lead astray by their presence. Definitely the information on filtering should be included in the metadata, and perhaps there should be options to submit both raw and filtered reads.

-What is the difference between the white and grey rows in table 4?

- Line 73-74: Stouthamer 1990 PNAS is one of the first references for this.

- Lastly, I am happy that the authors have provided the draft assemblies. I would like to state for the record, that I think they are premature for NCBI, and as such I agree with the authors’ decision to only provide them in supplement. There are other examples of Wolbachia genomes on NCBI that are chimeras and/or HGTs (ex., wAna). Unfortunately these genomes are often used in analyses and it confuses the literature. Hopefully you or others can follow up on the drafts you generated to verify their true infection status and assembly quality.


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: A BIOINFORMATICS APPROACH TO IDENTIFYING WOLBACHIA INFECTIONS IN ARTHROPODS
Review round: 2
Reviewer: 2

Output:
Basic reporting: see below
Experimental design: see below
Validity of the findings: see below
Additional comments: I am very happy to see the revised work by Pascar & Chandler much improved, most importantly by the assembly of the Wolbachia genomes. This was a big effort, but I think it was worth it. Also, the narrative has been tightened and the text is much better to follow than the original version. I want to congratulate the authors for this contribution. I have in general no objections against this being published, but found one important issue that needs fixing.

From the scripts you submitted as Supplementary material (which I find very commendable!) it appears that the Wolbachia coverage was taken from the Spades contig file names. It is important to notice that the coverage there does not correspond to whole genome coverage, but rather to kmer coverage of the largest kmer used for assembly (51 in your case). This can be considerably lower than the actual genome coverage.

I suggest for a more exact estimate of Wolbachia genome coverage to map all Wolbachia reads used for assembly back to the Wolbachia assembly, and then use samtools to estimate coverage. If you don’t want to do that (which I’d understand), you could just calculate (number of reads used for assembly)*(read length) / (Wolbachia genome size).

Also, is the Wolbachia coverage normalised to library size? In your calculation for A. gambiae for example, you use all reads to calculate the coverage of the host genome, but it appears that only the dowloaded reads (5x10^7) were used to calculate Wolbachia coverage. If so, this needs to be corrected.

Minor comment: there are two very recent preprint articles that report on Wolbachia in Anopheles that could be cited (https://doi.org/10.1101/338434 ; https://doi.org/10.1101/343715 )


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: A BIOINFORMATICS APPROACH TO IDENTIFYING WOLBACHIA INFECTIONS IN ARTHROPODS
Review round: 2
Reviewer: 3

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: This is a fun paper and the authors have done a great job in revising the manuscript. I believe they have addressed all of the reviewers concerns and will be pleased to see it published.

The section in the discussion providing best practice advice, while important, is largely already covered in other publications (see weblink and references below). Im not suggesting removing it, as I believe it is valuable to the community - particularly regards pre-filtering of 'contaminants'. It would be nice to see references to relevant literature for interested readers however.

e.g.

http://fged.org/projects/best-practices-for-omics-data-sharing/
https://www.nature.com/articles/sdata201618
https://f1000research.com/articles/6-1618/v2


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: A NEW SPECIES OF LEPTOBRACHIUM (ANURA, MEGOPHRYIDAE) FROM WESTERN THAILAND
Review round: 1
Reviewer: 1

Output:
Basic reporting: Some minor comments
Line 47. ‘asian’ should be Asian
Line 64-67 and other places. Please minimize the use of brackets.
Line 67. ‘letter’ should be ‘latter”
Line 168-171. This description is unconventional. Bootstrap values below 50 may indicate that these nodes are not-well-supported; however, most of these nodes are clearly resolved.
Line 205-209. The most meaningful comparison is comparing the distance between L. sp. Vs L. smithi to 1) pairwise distances between recognized sister groups, and 2) the highest intraspecific divergence.
Line 332. “polydominant” should be predominant.
Line 404. Please move this and the following paragraphs to the beginning of the section “comparisons”, because they are the most important.
Lines 434-439. Please remove any sentences that discuss the phylogenetic relationships of the genus. MtDNA may be sufficient to distinguish species, but far from sufficient to build phylogenies.
Line 447-452. Long sentence. Break it.

Table 1 could be an appendix. It is not essential.
Experimental design: No comment
Validity of the findings: Conclusion is well supported
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: A NEW SPECIES OF LEPTOBRACHIUM (ANURA, MEGOPHRYIDAE) FROM WESTERN THAILAND
Review round: 1
Reviewer: 2

Output:
Basic reporting: Article is generally well-written, although there are still some minor errors in language. The literature references are sufficient, but the introduction needs more details, particularly on the recognition of subgeneric classification and the “Leptobrachium smithi complex”. Like, the author mentioned “L. smithi complex” in the text a few time, but without any brief background about this species complex. This aspect may be presented in the introduction to make the issue understandable.
The article structure conforms to the acceptable formations.
Experimental design: Materials and methods are correct and sufficient for the scope of the paper. Methods are described with sufficient details are reproducible by other researchers. But the currently presented data is not an integrated taxonomic approach that the author claim in the introduction.
Validity of the findings: The presented data are basically sufficient for supporting the validity of the new species being described, although adding more supporting data on acoustics is highly recommended. Some mistakes in the comparison section, and figure can be noted.
Additional comments: See attached file for more comments/corrections.


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

Input:
Title: PLANT DATA VISUALISATION USING NETWORK GRAPHS
Review round: 1
Reviewer: 1

Output:
Basic reporting: well-written.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The manuscript entitled “Plant data visualization using network graph” by Mohamad-Matrol proposes a web-based visualization system, called PlantViz, using a graph model representation of plant data. The system can convert ontological dataset as graph model, query from the model data, transform lengthy text data form into graphical form, and display the results based on GUI. The authors assessed the PlantViz by two different types of user evaluations, the usability heuristics- and query and visualization evaluations. The results suggested that the PlantViz can contribute to data retrieval and sharing to infer and gain new insights from the vast amount of plant data. Given that biological data integration using Semantic Web technologies like RDF and SPARQL is one of promising approaches, I think that this work is timely and effective. Although the development of the methodology and evaluation seems to be reasonable, I have a few comments below.

(1)	Where is a demo site?
As a whole, the manuscript is well-written. The figures and tables are nicely organized. However, I was not able to find the URL link to the demo site on the WWW, although the source code for the PlantViz development can be accessed in GitHub. I am not sure that the system works well.

(2) Detailed manual ‘how-to’
The authors should prepare the detailed tutorial section to include actual "How-to's" on the website and Supplementary materials on the journal site. I also think that multiple example datasets are very useful for potential users and readers in the journal.


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: PLANT DATA VISUALISATION USING NETWORK GRAPHS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Although the paper is on the whole well written, it seems to me that there is a lot of redundant material, and it takes the authors a long time to get to the point (i.e. that they are described a web-based database graphical querying service for a relatively small dataset).

L14 There are some basic errors of grammar (e.g. ‘graph’ should be ‘graphs’ in the title), but there are also some phrases that are ambiguous to the reader, e.g. L14 in the abstract, what type of “botanical data” are the authors referring to? Survey data? Morphological data? Genetic data? This should be clear from the abstract, even on reading the entire abstract it is unclear to me exactly what types of data are going to be dealt with in this paper. (Indeed, this is not broached until L123 of the paper)
L20 of the Methods in the abstract. Again, this is ambiguous, what type of “text-based query results” are the authors referring to? SQL queries of a relational database? API queries to a webservice of some sort? Some other GUI query to a custom catalogue of some type?
L42, ref should be in the format Willis (2007), not (Willis 2007).
L43-49 This very general discussion of woody plants does not seem hugely relevant to the paper.
L62-L122 This seems to contain a large amount of background material, most of which seems tangential to the method being presented in this paper. Do we really need to know about two separate JavaScript libraries? The topic (introduced in L123) should be introduced a lot earlier.
Experimental design: I'm afraid that, to me, this paper seems to be outside of the PeerJ aims and scope. It seems to be describing a fairly special case of constructing a graphical web-based querying service for a small local dataset. The general way in which the authors have approached this challenge may be of interest to a small technical readership interested in doing something similar, but it does not seem to have importance as a piece of research filling a knowledge gap.

L239-241 The descriptions of the two tests here seem to me to be describing the same thing! Whilst I can understand how Fisher's Exact test might be applied to a 5 x 2 table of counts (five levels of usability x two user types for each case), I struggle to understand how this type of data is suitable for a t-test (and how the question being answered by the t-test approach is any different to that being examined by Fisher's Exact text (i.e. did novice and expert users report different usabilities), but perhaps this is just down to a poor explanation of what was actually done). [ In fact, in the results it emerges that the FE test was applied to the usability heuristics data, and the t-test to the other data; this is not at all clear from the methods. I still seriously doubt the appropriateness of a t-test for examining differences in small (20 v. 30) groups of numbers  between 1-5 see e.g. https://en.wikipedia.org/wiki/Student%27s_t-test#Assumptions ]
Validity of the findings: As noted above, I don't think this paper meets the PeerJ aims and scope; although, having said that, with the exception of the issues above under (1) Basic reporting and (2) Experimental design (particularly the t-test), the paper could be said to be 'valid', in that it presents a database structure and then asks some people (novices v experts) to test its usability. However, I would classify this firmly as a case study or case report rather than a Research Article (see https://peerj.com/about/aims-and-scope/)
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: PLANT DATA VISUALISATION USING NETWORK GRAPHS
Review round: 2
Reviewer: 1

Output:
Basic reporting: In general the revised paper is well written. Although all parts of the manuscript are intelligible to an intelligent native speaker of English, the general standard of English could be improved upon by a copy-editor or proof-reader. All other basic reporting criteria appear to be met.
Experimental design: The research question and methods are now much better described than previously; the comprehensiveness of the figures is particularly good. The description of the statistical tests are also improved. Although I still have my doubts that a t-test is really suitable for the data presented under the query and visualisation evaluation (a point not clearly responded to by the authors in their rebuttal letter), the figures presented make it blindingly clear that there is almost no difference in the evaluations of novices and experts, and so the statistics are barely necessary.
Validity of the findings: The findings are clearly stated, although it would be nice to have a bit of critical reflection on the wider use of the approach by the authors. For example, where countries have millions of sample points for species (e.g. in the UK the national set of species occurrence data held by the database of the Botanical Society of Britain and Ireland totals ~40 million 'samples'), is a visual graph approach likely to be practical?
Additional comments: L120 what type of sample are you referring to? Not quite clear here whether a sample is a record of a species’ occurrence in space and time, or a herbarium or other physical sample of the plant.


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: MOVEMENT AND JOINTS: EFFECTS OF OVERUSE ON ANURAN KNEE TISSUES
Review round: 1
Reviewer: 1

Output:
Basic reporting: Overall, the paper met the primary standards of being self-contained, having proper tests of the hypotheses and relevant results, and sufficient background information.  The author's figures were very well done, and I would like to particularly single out Figure 5 as the most useful methods figure I've seen in a while.  Overall, the text was quite readable, but there were some odd word choices and unclear sentences (particularly line 139-140); I would recommend a native English speaker giving it a look over and some suggestions.
Experimental design: The experimental design was largely satisfactory, except for the tissue alterations score, which had two significant issues.

First, the coarse 0-1-2 raking doesn't leave a lot of room for subtlety.  The scales these were based on (Maffulli et al 2008 and Pauli et al 2011) have four categories, not three, so why were the number of categories reduced?

Second, no statistical analysis methods were included for this data, not even Chi-squared tests. One cannot simply take the distributions of categorical variables at face value, anymore than one can for continuous variables.

Additionally, no method for adjusting for multiple tests was included.

Finally, although multiple species were used, there was no consideration of differences between species or locomotor style given, beyond cursory mention in one table, and no statistical framework for evaluating this was provided. Why were these data pooled?  At the very least, jumpers vs walkers should be separated, given the dramatic difference in the loading levels presumably experienced by the joints.
Validity of the findings: The fundamental problem with this paper is that the tissue alteration scores were not statistically evaluated.  As stated in the prior section, just as with continuous variables, you cannot assume differences in categorical variable distributions aren't the product of random chance and sampling error, especially with limited sample sizes.  With a few exceptions, the differences between control and treatment groups was small, only a few samples difference, as shown in Figure 6.  Perhaps these are real, but without statistical testing, there is no was to be sure.  Almost the entire discussion rests upon these results, making it all of questionable validity.  These results need to be tested in a statistically rigorous way which accounts for the categorical nature of the response variable and the multivariate nature of the evaluation.

The articular cartilage cell quantification runs into another problem of significance: in spite of no significant differences being found between treatment and control in either bone's articular cartilage, the authors insist on discussing these non-significant differences in the results (lines 282-286) and discussion (343-369).  Examination of Figure 8 does not reveal any visible trend matching the author's claims, regardless of statistics.

Per this journal's mission, negative and inconclusive results are not viewed unfavorably, but the statistical tests must be conducted in the first place (tissue alteration scores) and acknowledged as negative when the statistics show it (articular cartilage).
Additional comments: Lines 91-93 are not up to date. Nauwelaerts & Aerts 2003 did not actually quantify long-axis rotation, and while Kargo, Nelson & Rome 2002 predicted it based on a simulation, no long axis rotation of any limb bone was observed in Astley, H. C., and Roberts, T. J. (2014) The mechanics of elastic loading and recoil in anuran jumping. Journal of Experimental Biology, 217, 4372-4378

In line 91, I would add the following citation, which shows the highest peak jump forces known in anurans: Work and power output in the hindlimb muscles of Cuban tree frogs Osteopilus septentrionalis during jumping.  Peplowski M, Marsh R. The Journal of experimental biology. 1997 vol: 200 (Pt 22) pp: 2861-70

I would add "anuran knee tissues" to the title for clarity.

The supplementary video was entirely superfluous, and can be omitted.  For citation on the largely sit-and-wait lifestyle of anurans, see: Movement patterns in leiopelmatid frogs: Insights into the locomotor repertoire of basal anurans. Reilly S, Essner R, Wren S, Easton L, Bishop P.  Behavioural Processes 2015 vol: 121 pp: 43-53.


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: MOVEMENT AND JOINTS: EFFECTS OF OVERUSE ON ANURAN KNEE TISSUES
Review round: 1
Reviewer: 2

Output:
Basic reporting: The article “Movement and joints: Pathological effects of overuse on knee tissues of frogs (Reviewing Manuscript 21173v1)” represents a pioneer study about the understanding of the dynamics of anuran knee tissues during the ontogeny and in relation to locomotion. It was written using clear and professional standards of the scientific language. The English wording is very good. The article included sufficient background in relation to theme and showed a good presentation of the field of knowledge. The structure of the article is organized in the traditional format of scientific manuscript sections. The figures represent the content of the article and they are appropriately described and labeled. All data has been made available in accordance with PeerJ Data Sharing policy.
Experimental design: The research question is relevant and clearly defined. The investigation method was described with a high technical standard and conducted in conformity with the ethical guidelines of the animal experimentation.
Validity of the findings: The data are robust and they are related with the conclusions. These were connected to the original questions and supported by the results.
Additional comments: No 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: MOVEMENT AND JOINTS: EFFECTS OF OVERUSE ON ANURAN KNEE TISSUES
Review round: 1
Reviewer: 3

Output:
Basic reporting: The reporting is clear and the English is mostly good. Its purpose is however, not clear and the conclusions rather sketchy at best.

The article fails to include sufficient introduction and background to demonstrate how the work fits into the broader field of knowledge. Is there work intended to identify physiological homeostatic changes in tissue architecture induced by an extreme form of exercise or instead to detail the pathology that this kind of challenge produces?

The authors provide Figures showing the whole joint in ‘normal’ anurans but fail to provide similar for those that have been exercised.

Extensive reference is required to prior work by the same authors. Without this their current submission is very difficult to assimilate into a body of work. In particular, the last sentences of the introduction are completely dependent on their prior work, which is not discussed.
Experimental design: Their research question is at best cumbersome to negotiate; it is not particularly well defined or meaningful. Its failure seems to centre around whether there were any merits in studying multiple species, the questionable ‘end points’ the authors select to observe/measure and the methods employed to select and to ‘exercise’ their animals.

The submission does not clearly define a relevant and meaningful research question and hence the knowledge gap being investigated is too ill-defined.

The study design is not rigorous enough, with inappropriately calibrated protocols and end points that do not provide any specific new insights. The investigation is neither performed to a high technical or, seemingly, ethical standard.

The extent of the exercise regimen seems to be based mostly on the basis of the animals becoming exhausted – refusing to complete the task – there are many factors that can contribute to this ‘decision’ and it seems to this reviewer that some quantifiable parameter needs to be used to calibrate this system for the proposed use across animals of different age and species.

Methods: How are juveniles and the attainment of adulthood defined; how long after adult status is reached was it permitted until an animal was deemed too old for inclusion.

Methods: How long were they houses in individual terrariums prior to the start of the imposed treadmill exercise regimen? Was this short enough for there to be no evidence of structural adaptation in the housed animals – adult and juvenile?

Lines 133-4: this implies that there was no growth is the size of the adults or of the juveniles during the course of these studies. Is it surprising that there was no growth in juvenile animals?

Lines 140-1: indicates that there is little movement in these species. Does this make the author’s choice to study adaptation to exercise in these species questionable?

Line 151-3: The exercise regimen seems to be rather excessive in my opinion; fatiguing animals twice daily for 59 days would raise serious welfare issues and, at the very least, require that another group, utilising the same ‘energy’ but without the treadmill endurance exercise, be sacrificed as a control.

Line 157-8: this appears to suggest that a single speed was chosen. This seems rather inappropriate given that animals at different stages of maturity and different species are being exercised. Surely such a system needs some form of calibration in order to make this use of different stages/species meaningful.

Line 196: These methods are using a very ill-defined scoring system that has never been used, to my knowledge, before. Its justification and validation need to be performed in order to give these experiments any meaningful experimental value for other researchers.

Structural disorganisation can be taken to mean very many things. This kind of classification is not helpful.
Validity of the findings: The relevance of the study design and the end points selected for measurement are not obvious.
Additional comments: It is not clear upon which basis the authors have been led to hypothesise that ‘adults will experience deeper morphological changes than juveniles’.

The authors should explain why there is any benefit from examining responses in small numbers of several anuran species rather than larger numbers of one species.

The authors justify the choice of anurans based on the larger joint stresses. What is the evidence for this assertion?

Line 64-66: phrasing ‘does not have time to repair itself’ supposes these are responses to injury, rather than some form of remodelling, which is considered a homeostatic adaptive response.

Lines 104-107: The question to which this work is addressed is not clear.

Lines 107-112: ‘a structural disorganisation process.’ Is this pathological? If the authors are supposing that adult tissues cannot adapt then this is incorrect. It is well established that periods of rapid growth are conducive to adaptation to applied loading regimes. If this is testing the same idea, then it does so rather inelegantly.

Results
Lines 217-233: This reviewer finds it rather difficult to ascertain the value this data provides.
The authors make use of the term laxer as though they have measured collagen fibre resilience/elasticity based on their compactness in histology. No such measurements are made – they are simply commenting on histology.


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: MOVEMENT AND JOINTS: EFFECTS OF OVERUSE ON ANURAN KNEE TISSUES
Review round: 2
Reviewer: 1

Output:
Basic reporting: The paper meets basic reporting requirements as above, though there remain some oddities of grammar and word choice which can make for puzzling sentences.  Figures and tables are good, though the primary subject of the statistical test, the combined tissue alteration score, is not given in any figure or table (though the components are in Figure 7).
Experimental design: The justification of the reduced number of categories in the categorization is uninformative and poor.  The text addition simply says the authors “adapted it to be used in comparative biology”, without further justification or explanation of why such adaptation was necessary or beneficial.  The review response was more elaborate but no more informative.  The authors state it was for accessibility, but this is a poor reason to choose an experimental metric – the objective of the data is to accurately represent reality, and it is the most representative data which should be used; aids to understanding should be confined to the discussion.  The underlying variables are fundamentally continuous, although their responses to exercise are correlated, so why not use either the raw variables or a PCA thereof?  Converting continuous data into categorical data erases information, and choices of cutoffs are crucial.  But even if we accept that the categorical framework of Maffulli and Pauli is accurate and statistically valid, consolidating four categories into three reduces statistical degrees of freedom and erases variation.  Ultimately, the question is “why not just use the underlying continuous data, kept in a continuous form?” must be answered, and “ease of reading” is not sufficient justification for the information loss.  Similarly, if categorical data should be used, “why were the number of categories and their cutoffs chosen?” must be answered.  If the authors simply used the Maffulli and Pauli categorization intact, they could “pass the buck” on both, but altering that categorization requires justification beyond simply accessibility.  If Maffulli and Pauli relied upon more variables, why didn’t you quantify all of their variables?

The statistical evaluations have improved, simply by virtue of existing, but are still insufficient. The authors claim that the use of wild animals results in low sample size (something I’m not unsympathetic to), yet the authors note in their ethical justifications that these species are not rare and reproduce in large numbers.  Why not simply go catch more frogs, particularly during the next breeding season, since they are all native to the region?  This is essential, because you have multiple independent variables – exercise vs. not, juvenile vs. adult, and walker/nonwalker (with species being a nested factor within this).  Multivariate methods are never used, and instead each independent variable is tested separately, with no adjustment for multiple tests or possible confounding or co-variation.
Validity of the findings: The current statistical tests for “tissue alteration scores”, which seem (the authors do not include sufficient detail in the methods to be sure) to be the results of two tests, globally pooling all adults and all juveniles and testing each dataset for exercise vs. not, without accounting for species or locomotor mode (the effects of which were tested separately in a manner not sufficiently detailed in the paper).  Because species and walker/not are not included in these tests (but rather tested separately later), no consideration is given to whether these factors could influence the outcome, especially given the total lack of juveniles of Melanophryniscus and minimal numbers in Phyllomedusa.  It should be noted that the combined “tissue alteration scores” which are tested are not shown in any graph (Fig. 7 shows the components, but not the whole). The juveniles shows a significant difference (if we accept the authors’ reduced categorization), and adults do not, but no adjustment for repeated testing (e.g. Bonferroni correction) is used.  The authors note the lack of significant effects for adults, but then proceed on a statistical fishing expedition (through methods unspecified) to post-hoc justify the exclusion of one of their variables.  Furthermore, none of the asserted differences in Figure 7 were tested for statistical significance; instead, the authors seem to have assumed that if the overall result for combined score was significant, all of the underlying variables must also be significant, which is unfounded to say the least.
Additional comments: No further 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: MOVEMENT AND JOINTS: EFFECTS OF OVERUSE ON ANURAN KNEE TISSUES
Review round: 2
Reviewer: 2

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: The article meets conditions to be accepted in the presented format.


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: MOVEMENT AND JOINTS: EFFECTS OF OVERUSE ON ANURAN KNEE TISSUES
Review round: 2
Reviewer: 3

Output:
Basic reporting: The connection between movement and joint formation is well-established. In this work, the effect of extreme exercise on joint morphology was studied using comparative analysis between wild animals of five species of anurans that were trained to run on a treadmill. The findings are that intense movements lead to changes in morphology, that young joints are more tolerant to stress than those of adults and, finally, that there is no difference between jumpers and walkers.
Overall, this is a limited study as are the conclusions that can be drawn from it. One interesting finding is that extensive usage can lead to morphological changes. On the other hand, the fact that there was no difference between jumpers and walkers, who most likely represent two different mechanical strategies, might suggest that the mechanical test that was applied was either to challenging or unsuitable, thus preventing the identification of differences between species.
Regarding the revision, it appears that the authors made an honest effort to address most of the comments of reviewer 1, but largely objected the comments of reviewer 3, which were indeed very negative and very difficult to reconcile with the author's approach. Because I got involved only during the revision stage, it is very difficult for me to decide categorically between the two sets of arguments.
Experimental design: The connection between movement and joint formation is well-established. In this work, the effect of extreme exercise on joint morphology was studied using comparative analysis between wild animals of five species of anurans that were trained to run on a treadmill. The findings are that intense movements lead to changes in morphology, that young joints are more tolerant to stress than those of adults and, finally, that there is no difference between jumpers and walkers.
Overall, this is a limited study as are the conclusions that can be drawn from it. One interesting finding is that extensive usage can lead to morphological changes. On the other hand, the fact that there was no difference between jumpers and walkers, who most likely represent two different mechanical strategies, might suggest that the mechanical test that was applied was either to challenging or unsuitable, thus preventing the identification of differences between species.
Regarding the revision, it appears that the authors made an honest effort to address most of the comments of reviewer 1, but largely objected the comments of reviewer 3, which were indeed very negative and very difficult to reconcile with the author's approach. Because I got involved only during the revision stage, it is very difficult for me to decide categorically between the two sets of arguments.
Validity of the findings: The connection between movement and joint formation is well-established. In this work, the effect of extreme exercise on joint morphology was studied using comparative analysis between wild animals of five species of anurans that were trained to run on a treadmill. The findings are that intense movements lead to changes in morphology, that young joints are more tolerant to stress than those of adults and, finally, that there is no difference between jumpers and walkers.
Overall, this is a limited study as are the conclusions that can be drawn from it. One interesting finding is that extensive usage can lead to morphological changes. On the other hand, the fact that there was no difference between jumpers and walkers, who most likely represent two different mechanical strategies, might suggest that the mechanical test that was applied was either to challenging or unsuitable, thus preventing the identification of differences between species.
Regarding the revision, it appears that the authors made an honest effort to address most of the comments of reviewer 1, but largely objected the comments of reviewer 3, which were indeed very negative and very difficult to reconcile with the author's approach. Because I got involved only during the revision stage, it is very difficult for me to decide categorically between the two sets of arguments.
Additional comments: The connection between movement and joint formation is well-established. In this work, the effect of extreme exercise on joint morphology was studied using comparative analysis between wild animals of five species of anurans that were trained to run on a treadmill. The findings are that intense movements lead to changes in morphology, that young joints are more tolerant to stress than those of adults and, finally, that there is no difference between jumpers and walkers.
Overall, this is a limited study as are the conclusions that can be drawn from it. One interesting finding is that extensive usage can lead to morphological changes. On the other hand, the fact that there was no difference between jumpers and walkers, who most likely represent two different mechanical strategies, might suggest that the mechanical test that was applied was either to challenging or unsuitable, thus preventing the identification of differences between species.
Regarding the revision, it appears that the authors made an honest effort to address most of the comments of reviewer 1, but largely objected the comments of reviewer 3, which were indeed very negative and very difficult to reconcile with the author's approach. Because I got involved only during the revision stage, it is very difficult for me to decide categorically between the two sets of arguments.


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: SYNERGY BETWEEN ROADS AND DISTURBANCE FAVOUR BROMUS TECTORUM L. INVASION
Review round: 1
Reviewer: 1

Output:
Basic reporting: In this manuscript the authors tested the effects of road verges as contributor for the spread of an introduced grass species into surrounding environments. In particular, they tested whether the invasion success in the surrounding native communities depended on the level of propogule pressure in road verges and the level of disturbance in adjacent habitats.

The manuscript is generally well written, however, English should be improved in some parts (e.g. L 71-76, L 88, 203-205, 221-222, 241,...)

Literature references and sufficient field background/context are provided in most places, with some exceptions noted below:

Dainese M, Aikio S, Hulme PE, Bertolli A, Prosser F, Marini L (2017) Human disturbance and upward expansion of plants in a warming climate. Nature Climate Change 7: 577-580
Lembrechts,J.J.etal.Mountain roads shift native and non-native plant species ranges. Ecography 40,353–364(2017).
Lembrechts,J.J.etal.Disturbance is the key to plant invasions in cold environments. Proc.NatlAcad.Sci.USA 113,14061–14066(2016).

The strucuture of the manuscript is OK.
Experimental design: The research question was well defined and is relevant to the expanding field of understanding biological invasions. The study is designed well, methods were detailed and appropriate, and allowed robust analysis of the results.

Minor points:
L. 167-170: Although the analysis included interaction terms, this was not clearly stated in the description of the model.
L 172-173: Why did you use choose these reference groups?
Validity of the findings: The results were presented clearly, expected those related to Fig. 2 (see L 184-188). Observing the fitted lines in Fig. 2, I have some difficulties to outline this result as described by the authors. It's much clear observing the observed values. In this form, Fig. 2 is misleading. Anyway, conclusions were supported by the results. I would only suggest to develop the interpretation of this result (Fig. 2) a little bit (see L 212-218). Another explanation could be that in fields with high levels of disturbance local communities are already dominated by very competitive species that are able to outcompete with cheatgrass. This could explain the independent effect of road verges on cheatgrass density in moderate or highly disturbed habitats.
Additional comments: In my point of view the manuscript need some minor adjustments only, and, overall, the research is well designed and presented good results. I recommend the publication in PeerJ.


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: SYNERGY BETWEEN ROADS AND DISTURBANCE FAVOUR BROMUS TECTORUM L. INVASION
Review round: 1
Reviewer: 2

Output:
Basic reporting: This manuscript reports on patterns of Bromus tectorum presence and abundance at different distances to road and in response to habitat type. Overall the results seem robust, and confirm what we understand about B tectorum distribution in semi-arid steppes around the world. That is B tectorum as a ruderal winter annual responds positively to many types of disturbance that often occurs along roads and in areas that are overgrazed by livestock. The most interesting and unique aspect is the inclusion of roadside population size in predicting sites abundance away from the roadside; but this needs some clarification.
Experimental design: Overall the experiment is well designed to detect the patterns of abundance or presence-absence on the Patagonian landscape. The inference to separate the effect of propagule pressure (dispersal), or disturbance seems somewhat limited as currently presented.
There is a positive correlation between the abundance at the roadside and abundance as distance from road decreases, the authors present a model (Table 1), but its unlcear if this model is for all data or just the subset away from the road. I wonder how roadside abundance was included in the model if the roadside data was included as a predictor variable, wouldn’t the correlation of the response and predictor affect the robustness of the model?
Validity of the findings: The findings support the idea of greater occurrence of at the roadside, and that there is a correlation between population density at the roadside and at distances further away. Some of the model is not well explained as mentioned above and I couldn’t understand how the model was fit. Why were the models fit as general additive models in the end and what are coefficients being presented in Table 1, it is not clearly stated.
Additional comments: I found the introduction and discussion could be improved by more literature on B tectorum invasion (See a list below). I also feel the title is not informative and doesn’t not convey what paper is about. I feel all mentions of ‘drivers of global change’ could be deleted and instead use a more explicit term like disturbance or propagule pressure interact to influence B tectorum invasion. I think it would increase the impact and visibility of the manuscript.  By deleting these mention the major revisions to the text are needed.
Overall the manuscript reads well, but there is a large number of minor changes to make to language for clarity. I present a list below but it not exhaustive.
Title: Does not relate to actual manuscript, revise to be more direct.
Abstract
I would use only Bromus tectorum in the abstract, and mention in the intro it is also commonly referred to as downey brome
L22 totaling approximately 400 km, better than travelling ca
L33-35; L34, this reads funny, clarify by making two clauses that some where the same and that wetlands had the lowest amount.
L37 synergy is not very informative – interaction of population/propagule pressure habitat and disturbance?
L40 reorder: with healthy environ being .
L45 not a very powerful or informative sentence as the last sentence of the abstract.
Introduction
L49 native species is redundant delete.
L79 These
L86-88 delete these sentence ending with Hulbert citation
I found the last paragraph of the intro needs improvement. Is the last sentence even testable there is a correlation with high disturbance and high propagule pressure how would you separator these results.
Methods
L140 – dirt or gravel road – I suggest using unpaved as a catch all term
L158 states 5 four listed.
L161 feces misspelled
L168 what are co variables? Independent or predictor variables?
L173 label the intercept with reference level in the table. So is the table then the contrast and not the parameter estimates? That should certainly be clarified. I don’t get why a gam was fit in the end, and what is reported in the figure the raw data or the mixed effects fixed parmeters? There was never any mention of spatial autocorrelation in the results or if it was necessary to include.
L184 latter habitats is confusing, rewrite to better reflect you are talking about the only roadsides.
L190 space
L199 fix standard deviation parentheses
L204 roadside, delete that, delete the, better word than favour, promote maybe. How did you separate the effect of disturbance and distance from road? Needs to be addresses if is currently unclear.
L208 Can you really draw that conclusion? They are good habitat but are they influencing spread if disturbance away from the road is a more important factor. Wouldn’t land use in general be a better explanatory variable?
L216-217 addivite and combined effects used the two sentences are confusing, please clarify
L219 The decline in abundance as distance to road increases is better than decay.
L221-222 I feel this is a stretch didn’t it differ by disturbance too? So it is the interaction. A graph that had B tectorum on the y axis and distance to road on the x with lines for each habitat and or disturbance intensity would better convey the results of the study. In fact dropping the wetland habitat would allow a better test of the effect of disturbance, population size, and distance to road.
I felt the conclusion need to be rewritten, were too long, I already stated global change drivers is uninformative, and also the last sentence isn’t directly connected to the paper or results.
Graphs – spell out Bromus tectorum in all axis labels, make the habitat boxes narrow (is that the raw data or fitted data?) The road density field density model is poorly fit where is the last red dot, and black dot does come close to fitted curve. Are these over extrapolated curves?
Tables The caption is uninformative and did state what kind of model it was or what the response variable was.


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: SYNERGY BETWEEN ROADS AND DISTURBANCE FAVOUR BROMUS TECTORUM L. INVASION
Review round: 1
Reviewer: 3

Output:
Basic reporting: I have read this manuscript several times and believe the data tells an interesting story, but I found the current framework for the story confusing, and the graphics and analysis are not clear.  With some major revisions this will be a useful contribution to the literature.
There are three questions addressed clearly by the data from what I understand. 1) what role do roads, and surface type, play in the frequency and abundance of B. tectorum. (It is unclear if this question can include disturbance intensity at the roadside). 2) How resistant are adjacent habitats to B. tectorum invasion, and 3) is this correlated with disturbance intensity. I believe the final paragraph of the introduction would benefit from a clearer articulation of the study questions/objectives.
The introduction references global change several times, stating land use change (e.g. road construction) and invasions as key ones.  If this truly is of interest to the authors they should evaluate age of road in their model, and regardless of that fact type of road should be included in the model.  Thus, overall I find the introduction interesting but don’t feel it really clarifies the purpose of the study. The reference to global drivers confuses rather than clarifies plus it’s questionable if the results provided overlap with land use change (road but not habitats as described).  There are also quite a few newer publications pertaining to roads as vectors that would be beneficial to include.  I will provide a list below.

Overall this manuscript has potential but the story need to be framed more clearly, and the data analysis and presentation more thorough.
Potentially useful references
Balch, J. K., B. A. Bradley, C. M. D'Antonio, and J. Gomez-Dans. 2013. Introduced annual grass increases regional fire activity across the arid western USA (1980-2009). Glob Chang Biol 19:173-183.
Bradley, B. 2012. Distribution models of invasive plants over-estimate potential impact. Biological Invasions:1-13.
Bradley, B. A. 2009. Regional analysis of the impacts of climate change on cheatgrass invasion shows potential risk and opportunity. Global Change Biology 15:196-208.
Bradley, B. A., C. A. Curtis, and J. C. Chambers. 2016. Bromus Response to Climate and Projected Changes with Climate Change.257-274.
Mortensen, D. A., E. S. J. Rauschert, A. N. Nord, and B. P. Jones. 2009. Forest roads facilitate the spread of invasive plants. Invasive Plant Science and Management 2:191-199.
Rauschert, E. S. J., D. A. Mortensen, and S. M. Bloser. 2017. Human-mediated dispersal via rural road maintenance can move invasive propagules. Biological Invasions:10.1007/s10530-10017-11416-10532.
Rew, L. J., T. J. Brummer, F. W. Pollnac, C. D. Larson, K. T. Taylor, M. L. Taper, J. D. Fleming, and H. E. Balbach. 2018. Hitching a ride: Seed accrual rates on different types of vehicles. Journal of Environmental Management 206:547-555.
Vakhlamova, T., H.-P. Rusterholz, Y. Kanibolotskaya, and B. Baur. 2016. Effects of road type and urbanization on the diversity and abundance of alien species in roadside verges in Western Siberia. Plant Ecology 217:241-252.
von der Lippe, M., and I. Kowarik. 2007. Long-distance dispersal of plants by vehicles as a driver of plant invasions. Conservation Biology 21:986-996.
von der Lippe, M., and I. Kowarik. 2012. Interactions between propagule pressure and seed traits shape human-mediated seed dispersal along roads. Perspectives in Plant Ecology, Evolution and Systematics 14:123-130.
Experimental design: The methods are unclear.  I cannot make 88 plots divisible by sampling every 5 m and the distance given. A table with number of samples per road – 14 I assume though I think that means a greater overall distance.  Is there much elevation difference – I assume not given the location but stating this would be useful. How many samples were in each habitat type? These data should be provided.
How far was the interior transect from the road – a minimum, mean and maximum may be useful here. Was disturbance recorded along the roadside? This seems like an important variable.
Validity of the findings: From the results it appears comparisons were made of infestation levels by road type. I don’t believe this is mentioned in the analysis section.
Why choose the intermediate as the mid point, and the shrubland. Were these the most populous?
Fig 2. The lines on the graph do not correspond with the error bars, nor really the model. Is this correct? Please check – it is not convincing as presented. Furthermore, having road type in the model seems vital if it was significant from other analysis that isn’t show – or is it highly correlated with the abundance variable? Wouldn’t it be more informative for management to use road type not abundance if they are correlated? It would agree with recent results from Europe.
For Fig 3 what happens if the 100 m is removed from analysis, is there still a decline? In how many cases was B. tectorum observed more than 100 m.  Several manuscripts I have read recently have used the mid-point of the density group, or better generated random number generation within each group.  Was this considered, does it improve the model? The figure would be better with the raw data displayed as scatter points with the model prediction, rather than the SE bars.
The results and discussion suggest the study was more interested in habitat resistance. If this is true then some references are missed.
The first sentence of discussion is confusing, and I don’t know what to suggest.  Later, line 214, as well as other places I was often confused if disturbance refers only to the interior habitat. Was it not measured at the roadside? That seems so important.
Line 22 – be careful talking about interior   - 50 m is hardly very far.
Paragraph 229-240. This paragraph almost contradicts itself with regard to dispersal, and there are studies that could be cited that are more relevant (see below).
Line 241. Very confusing. The rest of the paragraph discussed data that I do not find in the graphs and tables, nor methods, though it is mentioned in the results. See Rauschert for another study on seed movement.
Additional comments: Overall this manuscript has potential but the story need to be framed more clearly, and the data analysis and presentation more thorough.


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: SYNERGY BETWEEN ROADS AND DISTURBANCE FAVOUR BROMUS TECTORUM L. INVASION
Review round: 2
Reviewer: 1

Output:
Basic reporting: The article is fairly well written, there are some inconsistencies that need addressing.
Experimental design: Clearer now.
Validity of the findings: Clear, figures could be improved.
Additional comments: Synergy between roads and disturbance favour Bromus tectorum invasion
Speziale et al.
Revision 1.
I thank the authors for their improvements to the manuscript, there are now only some minor errors to correct.
The number of sample points is still unclear.  It says 88 in the abstract on line 22, 73 on line 146 and 74 in the response to reviewers.

Abstract:
Line 18, suggest the degree of invasion, rather than what you have
Line 25 suggest In not From, and recorded not registered
Line 30. Unclear. Perhaps put the second sentence first.
Line 40 “healthy”  - intact may be more appropriate word
Line 69 – yes, roadsides can be composed of many short-lived fast growing species, but in my experience this is rare on at least three continents. Perennial grasses, sown or not, are more the norm so I would suggest mediating this statement even if you don’t have a citation.
Line 90 downy doesn’t have an e.  I am not sure what this journal prefers but in this paragraph you have B. tectorum after the first mention but in other places you use cheatgrass.  Be consistent and determine that the journal requires.
Line 92 consider adding “and degraded rangelands” to your sentence, this was found by several of your cited references and helps your arguement.
Line 106 consider widespread not notorious
Line 107 consider with not being, and a comma after persistence
Line 11 consider is not was
Line 129 Spelling of shrublands
Line 144 – units and formatting are all a muddle e.g. kilometres, km, m with and without a space. Check formatting and consistency here and elsewhere.
Line 165 disturbance
Line 169 no Title case in other places so I would drop.
Line 230 While it can germinate in the spring it is really a fall germinating species.
Figures
Please consider that red does not come out differently on a black and white printer so you may wish to alter the colour or pattern.
Fig 2. I still do not find this figure useful because of the poor fit – especially for the low disturbance which looks linear.  The authors seem resolved not to alter the presentation but I would suggest it would improve the citation capacity of the paper.
For all figures (BT) is not needed as it is not used as an abbreviation anywhere. Again, check the journal requirements but having common in title and scientific name on figure seems messy. There is also a mix of Title Case and Sentence case which needs to be rectified.
Units for density need to be on the figures
Figure 3 should have 0 for y axis


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: PROFILING EXERCISE INTENSITY DURING THE EXERGAME HOLLYWOOD WORKOUT ON XBOX 360 KINECT®
Review round: 1
Reviewer: 1

Output:
Basic reporting: This study aims to prove whether an exergame  can be classified as a moderate form of exercise by running a series of experiment on 39 young male participants aged 25.9 +- 4.9.

This is the first attempt to evaluate the intensity of an exergame and whether it compares to traditional ways of exercising

The paper is well-written and well-structured. The style is also adequate. Most sections are clear and concise.

Very relevant work cited in the introduction and discussion sections. This suggests that the results obtained during the experimentation are in accordance with relevant studies done in the past.

I strongly believe this paper is a significant contribution, however, I have a few questions and concerns:

My main concern is that the chosen joystick-based game is not quite in alignment with the study design.

In your study, you exposed your participants to an exigent exercise in Phase 1 and a relatively demanding exergame in Phase 2. Then they play a fictional fighting game with a controller, not a sports game.

I think it would have made more sense to have them play a boxing exergame such as UFC Personal Trainer, or Kinect Sports Boxing, then have them played with the chosen fighting game.

The theme of a game can affect significantly your participants’ responses, feelings and attitudes towards the experiments. It important to understand that even traditional joystick-based games can also lead to increased physiological responses. Suspense intensive games such as the tactical shooter Swat 4 can easily increase the levels of adrenaline which directly affect heart rate, blood pressure, expansion of air passages of the lungs, the pupil in the eye, and even maximise blood glucose levels.

It would have made more sense to expose them to the same activity, but have them interact in different ways.

Also, I would like to know why all participants are males. Was there a criteria for excluding females from the study?

Aside from these, the paper is novel and the contribution is significant to the field of knowledge
Experimental design: N=39
Age 25.9 +- 4.9
Male only
Inclusion Criteria No to all items in PAR-Q
Participants performed exigent exercise
Then played an exergame (randomly allocated) (on a separate day)
Control played with a joystick (randomly allocated) (on a separate day)

The study design is very solid and in my opinion aligns well with the objectives of the study
It’s a bit unusual to use the term ‘control’ given that all participants went into intervention
Control refers to a group of participants that are also observed but are not part of the intervention.
I would probably suggest that this is removed.
Validity of the findings: Most results  obtained during the experimentation are in accordance with relevant studies done in the past. This suggests that such findings are clinically meaningful.
Additional comments: See below some minor comments:

Abstract

Line 22-55 - I believe this line needs re-writing
What I get from this sentence is that you are comparing an exergame session with exergame session. Isn’t this the same?
Would not it make more sense to compare and exergame vs regular exercise vs a joystick-based game?

Introduction
Line 90 - Add Ref to GXT

Methods
Line 136 - Add photo of Participant performing the exercise

Line 159 - Add Screenshot of game and/or photo of Participant playing with the game


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: PROFILING EXERCISE INTENSITY DURING THE EXERGAME HOLLYWOOD WORKOUT ON XBOX 360 KINECT®
Review round: 1
Reviewer: 2

Output:
Basic reporting: -	The article has been written in English in a clear and precise manner. No major errors are observed.
-	The introduction demonstrates sufficient background to understand the need to know the exercise intensity based on metabolic thresholds (first and second ventilatory thresholds (VT1 and VT2)) during the performance of exergames. There are only reports based on clinical and indirect cardiovascular variables. In addition, the introduction shows sufficient evidence in favor of the exergames and the approach to the research hypothesis.
-	The manuscript is structured according to the standards of PeerJ, it has a well-organized abstract of 251 words. The manuscript includes all the results of the investigation.
Experimental design: -	The manuscript complies with the Aims and Scope of PeerJ.
-	The research question is well supported and defined: “It is important to note that none of these studies determined exercise intensity based on metabolic thresholds obtained in a continuous laboratory treadmill test, such as maximal graded exercise testing (GXT)”.
-	The research complies with rigorous methodological and ethical criteria of the international research community. In general, it is a clear and precise method.
Validity of the findings: -	Line 158: “This result corroborates those of Lanningham-Foster et al.(2006) and Mills et al.(2013) who reported HR and V ̇O2 values significantly lower in joystick rather than in exergame sessions. This can be explained by the lower recruitment of large muscle groups during practice of the joystick game, since the participants usually only move their hands and fingers”. This comparison (results of the present investigation with the reports of the years 2006 and 2013) and explanation can not be made, since the participants of the present research differ considerably in relation to age and type of physical activity / exergame. This paragraph must be deleted.
-	Line 267 to 282: carry out a valid discussion and comparison between the results of the present investigation and the reports of previous years. Caution regarding the type of population, age, anthropometric characteristics and types of physical activity / exergame performed. The authors must make a meticulous and extrapolated comparison.
-	The conclusion is related to the objective of the investigation.
Additional comments: -	The research is novel and original since it tries to determine the intensity of exercise performed with exergames. This information is not present in the state of the art about exergames and partial immersion virtual reality.


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: PROFILING EXERCISE INTENSITY DURING THE EXERGAME HOLLYWOOD WORKOUT ON XBOX 360 KINECT®
Review round: 2
Reviewer: 1

Output:
Basic reporting: I'd like to thank the authors of the manuscript for incorporating all the feedback received during the review stage and clarifying all the questions and concerns that were raised.

The latest version of the article reads very well and explains clearly what the study is about and its outcomes.

I was a bit critical of some claims and the study design, but after going through the rebuttal and revising the updated document,  I strongly believe that this is a very significant contribution.

This work is very novel and, in my opinion, it meets the standards of this journal.
I would argue for this paper to be published.
Experimental design: NA
Validity of the findings: NA
Additional comments: I'd like to thank the authors of the manuscript for incorporating all the feedback received during the review stage and clarifying all the questions and concerns that were raised.

The latest version of the article reads very well and explains clearly what the study is about and its outcomes.

I was a bit critical of some claims and the study design, but after going through the rebuttal and revising the updated document,  I strongly believe that this is a very significant contribution.

This work is very novel and, in my opinion, it meets the standards of this journal.
I would argue for this paper to be published.


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: PROFILING EXERCISE INTENSITY DURING THE EXERGAME HOLLYWOOD WORKOUT ON XBOX 360 KINECT®
Review round: 2
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The modifications made by the authors of the manuscript are related to the suggestions and comments made by me. I recommend to accept the manuscript.


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: RHIZOBACTERIAL COMMUNITIES OF FIVE CO-OCCURRING DESERT HALOPHYTES
Review round: 1
Reviewer: 1

Output:
Basic reporting: The language is very clear. The authors have used a language editing service, so there is nothing to be said about it. I have marked some minor errors in the attached pdf file.

The structure of the manuscript is ok all background information is there. I believe that the author should add more details on their data analysis in the materials and methods section as it is I can't fully access if the methods used are 100% correct.

The figures and tables are clear and data is available for reanalysis.
Experimental design: The experimental design is ok. The only issue that I find is that the authors have chosen to identify microbial groups that change between plant species using ANOVA. Why not use methods that were designed to do this such as STAMP, metagenomeSeq, Lefse. Also there are details that can change the final result. For instance, was the OTU table normalized? How? Was the p-values of ANOVA corrected with FDR, Boferoni, etc...?
Validity of the findings: The results are not repetition of known facts it is a brand new view of the rhizosphere of these halophites. The experimental design is alright I just think the authors should explain their choice of methods or change it (as stated above.
Additional comments: My general comments are found in the pdf attached.


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: RHIZOBACTERIAL COMMUNITIES OF FIVE CO-OCCURRING DESERT HALOPHYTES
Review round: 1
Reviewer: 2

Output:
Basic reporting: -	The manuscript is poorly written, difficult to follow/understand and contains a certain number of impressions.
-	Literature is not always well referenced, in particular in the introduction and discussion many recent paper regarding i) association among bacterial and halophyte and ii) ecological/environmental driver in bacterial assembling/recruitment are not reported.
-	The manuscript should be re-written with much more precision and style improvement in order to improve general clarity.
-	Figures are not always relevant (see specific comment below in Figure section), moreover they are not well labelled/described.
Experimental design: -	Research question and experimental design pf the work is not well defined. Authors not state/identify a specific knowledge gap to be addressed.
-	The methodology is not detailed, no enough information are available to replicate the work.
-	Only three replicates are used to analyze variability of bacterial community associated to different plant species, additional analysis are necessary to confirm that this number is enough to describe the variability associated to each species.
Validity of the findings: -	Conclusions depict only how rhizosphere select different bacterial community then bulk soil. No correlation to chemical analysis/salt concentration/host or link to original research question is reported. Not always the correct statistical analysis has been used.
Role of plant species  (or of other factors) was not analyses, described, discussed.
Additional comments: The manuscript proposed by Li et al is describing the bacterial associated to halophytic plants in the salty soil of the Ebinur Lake Nature Reserve (Gurbantungut Desert, China). Rhizospheric soils of five different halophytic plants and their respective bulk soil have been collected in triplicates. To study the bacterial communities 16S rRNA-based amplicon sequencing has been applied to a total of 30 samples. The results obtained showed that the rhizosphere and bulk soils selected specific bacterial communities, with different relative abundance of several taxonomic groups.

Below are listed some general concerns which merit attention:

Abstract:
Not clear background and experimental design was reported. Results/Discussion reported in this section should be underline the main findings, underlining also the importance of the work done and of the results obtained in the frame of plant-bacterial interaction in saline soils.

Introduction:
-	Organization of this section is not clear. Concept have been reported and repeated in several point. Not updated bibliography has been provides. Many papers have been recently published on this topic reporting how host and soil parameters (among others salt concentration, tide etc.) can influence assembly and structure of bacterial communities associated to halophytic plants (among others in 2016/2017: doi: 10.1016/j.micres.2016.05.012; 10.1007/s00284-016-1096-7; doi.org/10.3389/fmicb.2016.01286; doi.org/10.3389/fmicb.2017.02288).
-	In this section, taxonomic name should be reported in italic.
-	Add reference or at least some additional description of the group of plants available in the saline system, they are very different ranging from tree to shrub.
Methods:
-	Detail regarding sampling in the field (root depth, soil depth, etc.), preparation of sample (separation of rhizosphere from root) are missed.
-	Details regarding the pipeline used for the analysis of the sequence and the obtained OTUS were not well described.
-	Line 151, modify ‘mother’ with ‘mothur’.
-	Principal components analysis (PCA) cannot be used to analyse matrix of similarity/dissimilarity, as the one obtained by the OTUs table. Please remove this and maintain only the NMDS analysis.
-	Please add stress value to the NMDS analysis.
-	Line 149. Richness, rarefaction, NMDS are not statistical analysis, please modify title of the paragraph
-	Principal components analysis (PCA) (or other adapt to analyze ordinal variable) could be applied to analyse chemical soil analysis matrix (including all the parameters measured) in order to understand how soil change and could influence bacterial composition. It could be associated with an analysis of the factors shaping the bacterial assemblage in order to define which factors drive the bacterial communities (soil parameters vs host). Moreover mantel test could be also useful to depict possible correlation among beta-diversity and soil properties.

Results:
-	A sampling scheme (map) in which plant sampled were associated to different environmental parameters (i.e salt concentration, C, N etc.) could be useful to describe/explain the experimental design used.
-	Chemical analysis have been conducted on the bulk soil, I not think it was possible do the same for the rhizospheric soil. So please modify the caption of table 1 and clarify this point.
-	Line 174 Move NCBI project number in material and method.
-	Figure 1A. Please move it in the supplementary material. Calculation of ‘Good’s coverage’ values can be more clear to understand coverage level of sequencing (they can be added in text of methods since are a pre-requisite to perform the other analysis).
-	Line 179. It is not clear if chimera and chloroplast sequences have been removed before/after rarefaction analysis. Since these can significantly influence the analysis. I suggest to remove them before to perform analysis of richness, coverage etc. Please specify this point and eventually repeat the analysis.
-	Please provide statistical analysis also to evaluate the effect of the factor ‘plant species’. Actually only statistical analysis supporting difference among bulk soil and rhizosphere was provided. Main test and multiple comparison tests should be added to evaluate diversity among plant species, infer is from NMDS graph is not correct (line 203-205).
-	Line 237. I suggest to the authors to define it as ‘community composition’. Community structure has been previously reported.
-	Line 255. Which are these 50 OTUs? Please define and clarify this last part.
-	Line 260. Ven Diagram description could be moved before, in order to better clarify similarity/different depicted by statistical analysis. Please add a ven diagram also for bulk bacterial communities, to underline the different selective process acted by the two categories of samples.

Figure:
-	No detailed caption are available, no letter to distinguish panel are present.
-	Multi-panel figure to describe beta-diversity/bacterial communities structure could be better for reader understanding
-	Figure 3. It is difficult read name of taxa and understand what star (*) mean. In the bottom panel, some names are cut. An additional bar chart with relative abundance (%) of taxa among rhizosphere and bulk soil of the five species could be added as first panel of figure. This will help to better understand the communities composition described in the results.
-	Figure 4. Why taxa distribution mong the 5 plant species has been reported only for rhizosphere samples? This visualization is not really clear and easily understandable (see comment before).
-	Figure 5. Rank of OTUs list for their taxonomy (i.e phylum, class etc.) could be useful to detect pattern of distribution among the 5 rhizosphere groups. As before I suggest t0 do the same for bulk soil groups, since as stated by the authors the work aim to compare rhizosphere and bulk soil.
-	Figure 6. Express the N. of OTUs as percentage of OTUs (and eventually add their relative abundance) could be a more clear way to describe repartition of bacteria among the 5 plant species. Please, do the same for bulk samples.

Table:
-	Additional details in table caption are necessary.
-	Table 1. Please specify that the reported values are referred to bulk soil (see comment before) where plants growth.
-	Table 1 and 2, please add detail regarding statistical analysis used and what letter indicate.
-	Supplementary Table 1. Please add all the phylum/class etc. detected, ad indicated with * the significant one. As the author did, multiple-comparison test has been reported for significant different taxa. Multiple-comparison test should be added also for bulk soil samples.
-	Supplementary Table 2. Caption, methods and results obtained are not clearly explained in the manuscript. Additional detail and discussion of these data are necessary.

Discussion/Conclusion:
No really discussion and conclusion are present. Not really trend or factor correlations have been reported to explain the results obtained. Repetition of results with lack of discussion in the frame of recent publication (see general comments) is the limitation of this section.