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

Input:
Title: CHARACTERIZATION OF SHIFTS OF KOALA (PHASCOLARCTOS CINEREUS) INTESTINAL MICROBIAL COMMUNITIES ASSOCIATED WITH ANTIBIOTIC TREATMENT
Review round: 1
Reviewer: 2

Output:
Basic reporting: The information about pap consumption is very interesting and would be a fascinating microbiome study on its own. (Pre/during/post pap consumption microbiome along with the microbiome of the pap sample itself.)  That said, the first paragraph of the intro, while interesting, seems out of place. Pap is never mentioned again in the entire paper.  I suggest either finding a way to relate pap to the results or drop the information on pap and instead focus the intro on the importance of evaluating the microbiome in a vulnerable (IUCN) species that depends on the microbiome for degradation / detoxification of dietary items. (There are also some good creosote/woodrat articles that discuss microbiome and detoxification that would provide additional support in your intro.)

In your introduction of Chlamydia, including a sentence or two about transmission would also be helpful – primarily STI? But vertical transmission and transmission through pap also possible??

Figure 2: The other piece of information that would be quite useful in this figure is wildlife hospital and antibiotic protocol. (These could be supplemental figures, or you could comment about clustering or lack of clustering by hospital / antibiotic protocol.) This figure would also be more readable if you used shapes and open/closed symbols to differentiate things like antibiotic/control and released / deceased. (You can edit PCoA’s produced in QIIME by opening the “_pc.txt” files in Excel and scatter plotting the first 2 columns (which represent PC1 and PC2). There are ways to do this in R as well.

Lines 351-352: In the intro, your “hypothesis” is: “we hypothesized that the reason for adverse side effects of antibiotics administered to koalas with Chlamydia infections is due to disturbance in the microbial communities present in the koala gastrointestinal tract, especially those microbes responsible for tannin degradation.”
This is not exactly consistent with your discussion statement that reads “This result is consistent with our hypothesis that a higher richness and evenness in the initial gut microbial community composition may be more important to koala health during antibiotic treatment than the direct impact of the antibiotic treatment itself.” The hypothesis is mildly overstated at other places in the discussion as well. (The intro hypothesis is very broad.  The discussion makes it sounds like the hypothesis was specific.)
Experimental design: Sample Collection: Koalas were not randomized to treatment with or without antibiotics, so how do the wildlife hospitals decide which koalas to treat with antibiotics? (Does this selection bias your groups? i.e. only the “clinically mild” animals received no antibiotics??)

Can you provide any information regarding the following: Were any of the animals co-housed or did they have contact with each other or shared spaces? What were typical husbandry / sanitation procedures at the hospitals? What were captive animals fed at each hospital?

“Built environment” samples are included in the PCoA but collection methods for these samples are not described.  (It was a GREAT idea to collect these samples.. nice work. Out of curiosity, did the built environment differ / cluster by hospital?)

What was the treatment protocol (dose, frequency, duration) and did it vary between individuals?

Table 1: Additional information that would be helpful in this table – wildlife hospital from whence the sample came, dose and concentration of the drug and frequency and duration of treatment. (Number of ml of drug given is not helpful.  I’d rather see something like “chloramphenicol, 2 mg/kg, twice a day for 7 days”).

Was the first sample(s) collected prior to antibiotic treatment?

Lines 239-243: So, an OTU can only be a node if it appears in all samples within a group? Please clarify. More typically, I see this analysis with all OTUs as nodes (regardless of whether they appear in multiple samples or not), and edge weight indicates commonness of co-occurrence within samples.  I would expect number of nodes and co-occurrences to be greater with more samples rather than lesser?
Validity of the findings: Lines 295-296: I’m still unclear about the co-occurrence network. There was an edge “between every two nodes” – are you saying every node (OTU) co-occurred with every other node?  Or do you mean “an edge connected each node (OTU) to one or more other nodes in the network”

Lines 300-3001: Why were there more nodes (OTUs) in 3 individuals than there were in 9 individuals? (I know you try to explain this above.)

Line 309: Do you mean, “However they were not present in all samples of koalas THAT DIED.” (instead of “that were released.”)

In the Discussion you state that  “Of the meta data collected (e.g. weight, age, geographical location, koala hospital, sex, Chlamydia status, etc.), antibiotics and fate (lived or died) were the only parameters that were significantly correlated with patterns in our analysis.”  However you do not detail these results / analyses.  Can you provide statistical evidence (PERMANOVA / ANOSIM etc.) or show figures to demonstrate that factors like hospital were not significant in your results? Alternately, limit this statement to the results you tested and shared in the results section.
In the discussion you do not need to restate the t / df / p values from your results section.  (Do not re-write the results in Discussion)
Line 335 – it is difficult for the reader to appreciate “low doses” when dose / concentration / frequency / duration of medication was not provided.
Line 337-338 – Your point about captivity is a good one.  There are multiple studies that support this idea; wild animals that are moved into captivity decrease in alpha diversity.  Citing one or more of these studies here will lend credence to your point.
Lines 341-345 – These results were not included in the results section above.
Lines 351-352 – Were your first samples collected after antibiotics were already given?  If so, then “initial gut microbial community composition” would already have been altered.
Lines 357-361 – This reads more like methods (or results).
Line 413 – PICRUSt is not mentioned in the methods.
Lines 425-428: Other confounding variables may include – different hospitals, different diet / husbandry / handling at each hospital, varying dose / duration / frequency of antibiotics?
 Line 443: This may be a good spot to speculate about the potential benefit of fecal microbial transplants from healthy koalas as a treatment modality.
The network / co-occurrence analysis needs better explanation and likely has more results worth probing. The only thing mentioned is that New.ReferenceOTU265 was “of interest” and is most closely related
to Lonepinella. Did this OTU co-occur with other microbes in the network? It would be important to understand if Lonepinella alone might make a good probiotic or if it needs “friends” that sustain or support its growth in some way… in other words – what microbes co-occur with Lonepinella?
Additional comments: This study examines the gut microbiota of Chlamydia-infected koalas not on antibiotics (n=2), on antibiotics that survived infection (n=6), and on antibiotics that died of infection (n=3). The subject matter is interesting and valuable as Chlamydia is a common and devastating koala disease that is routinely treated with antibiotics. Koalas are also unique in their ability to digest and detoxify eucalyptus leaves and the gut microbiome likely plays a critical role in this process. The sample sizes are small and many variables / possible biases exist (different hospitals, different antibiotic regimens). There are also multiple variables that are not mentioned / described but could be quite important: does diet differ at different hospitals? How does each hospital choose which animals to give antibiotics to? That said, the findings are interesting and despite small sample sizes, many variables, and non-randomized groupings, the findings provide support for the importance of microbes like Lonepinella in koalas. This finding is not novel; however, previous studies have relied on culture of Lonepinella while this study uses 16S sequencing and microbial co-occurrence networks to come to a similar conclusion about the importance of Lonepinella.

My major concerns are around the sample size and variation in groups – much of which is undescribed. Addressing the questions / comments highlighted in the review will be helpful in determining / describing the limitations of the study.

Minor edits are included below:

Line 52: replace “their” with “its” (singular)
Line 53: replace “are” with “as”
Line 235: replace OUT with OTU
Line 245: replace “c-occurring” with “co-occurring”
Figure 1 caption: replace “form” with “from”
Table 1 – replace “chlorampheniocol” with “chloramphenicol” under “Daily Dose” in almost every line.
Supplemental Table 2 caption: replace “OUT Co-occurrence”  with “OTU Co-occurrence” – what does this table mean? Do all of these OTUs co-occur in all koala samples in all groups?


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

Input:
Title: CHARACTERIZATION OF SHIFTS OF KOALA (PHASCOLARCTOS CINEREUS) INTESTINAL MICROBIAL COMMUNITIES ASSOCIATED WITH ANTIBIOTIC TREATMENT
Review round: 1
Reviewer: 3

Output:
Basic reporting: This manuscript is well-written and provides substantial background information regarding the topic. The relevant and appropriate literature is cited and the figures and tables are appropriate for this type of study. Overall, this was viewed as a strength of the manuscript, as it does a good job of explaining the particular research problem for non-specialists in the field.
Experimental design: This work presents original primary research that fits within the scope of PeerJ. The research question itself is well defined, meaningful, and fills in an identified knowledge gap. Given previous work on the Koala microbiome, which is in its infancy, this work advances our understanding of these organisms, and a particular issue that is detrimental to wild populations of koalas.

While the work has a lower number of animals, relative to other work on wild populations, this is understandable given the nature of the study. Methods require a bit more description, as there is presented material both in the results and outside of the results that are not described in detail. Specific details regarding this will be described in section (3) of this review.

However, in general, this work is very interesting and advances our understanding of the koala microbiota as it relates to health.
Validity of the findings: In short, this work presents the microbiota of koalas infected with Chlamydia and treated with antibiotics, relative to koalas that are uninfected. Necessarily, the authors looked at koalas from three different hospitals in order to acquire a larger number of animals for the study.  The authors collected fecal samples from these koalas every 3 days for a period of 21 days. Two koalas did not survive antibiotic treatment, and their microbiotas were also investigated, in comparison to the other groups. Overall, this is an interesting study that addresses a critical concern in koala biology, given that Chlamydial infections are decimating wild koala populations.

However, I do have some concerns regarding this work that needs to be addressed:

1. In discussion, it appears that two new pieces of data are presented that are not included in the results.

First, the authors note on line 323 that meta data associated with these koalas were assessed, but only antibiotic vs. non-antibiotic groups were found to be significantly different. I did not find any reference to this in the results (where this should be presented), nor is there any reference to these meta data and their analyses in the methods. This should be provided, and the particular model included (i.e. interaction variables, etc), as a natural hypothesis here is that animals from the different hospitals would cluster together based on geography, rearing habits, etc. For example, in Figure 2, if labels to the individual koalas are added according to hospital, would clustering appear according to this factor? Moreover, this data should be presented in the results section, not the discussion.

Second, an entire section is devoted to PiCRUST analysis, which is not described in the methods. Moreover, the results from this analysis were inconclusive, given that many of the taxa identified (e.g. Lonepinella) do not have sequenced genomes. I would recommend removal of this analysis altogether, as it does not add anything to the study.

2. In Figure 2, samples are included described as "build environment" and described as materials in the koala wards. However, I could not find any reference to this anywhere in the main text of the study. Why were these included? Did these samples and their analyses provide any insights into the study itself? If these were used as an outgroup, they should be mentioned. Moreover, there is no mention of these samples and their collection in the methods.

3. To me, an important consideration of this study is the fact that the authors conducted a longitudinal sampling of all animals. However, this study really only considered the impact of antibiotic use on the microbiota of koalas, rather than conducting an analyses of how the gut microbiota is changing over time. This is an important fact given that antibiotic use would be expected to alter the microbiota, especially over time. For example, in any given koala, either treated or not treated with antibiotics, is there a core microbiota that persists across time? What groups of bacteria disappear over time with antibiotic use, and are there significant differences in the respective timeframe for those koalas that recovered vs. perished? Given that 100+ samples are presented in this study, significantly more analyses could be performed in order to provide insights into what occurs in the gut of these koalas as a result of antibiotic use.
Additional comments: Overall, this is an interesting study, but requires substantially more analyses given the data available to the authors. The authors should pay particular attention to ensuring that the methods are complete and that no new results are presented in the discussion. Finally, the authors should consider the longitudinal nature of the study, and capitalize on this data in order to glean insights into how antibiotic use is changing the gut microbiota, as this may perhaps explain why two of the koalas perished after antibiotic treatment.


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

Input:
Title: CHARACTERIZATION OF SHIFTS OF KOALA (PHASCOLARCTOS CINEREUS) INTESTINAL MICROBIAL COMMUNITIES ASSOCIATED WITH ANTIBIOTIC TREATMENT
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comments
Experimental design: No comments
Validity of the findings: No comments
Additional comments: The authors have done a good job addressing many reviewer comments, explaining their responses thoughtfully, and providing thorough clarifications throughout the manuscript.

I  suggest only the minor revisions below:

Line 48: Change "intestinal" to "intestines"

Line 82: Change "is" to "are"

Line 134: Change "Leave" to "leaf"; changed "sealed" to "sealing it"

Figure 1 caption: Change "Plotsare" to "plots are"

Line 206: Change "does" to "did"

Line 282 and 355: Change "meta data" to "metadata"

Line 284: Change "gender" to "sex"

Line 341: "They were not present in all samples of koalas that were deceased" - change "were deceased" to "died". Also, this is (unintentionally) misleading.  This sentence makes it sounds like Lonepinella was not found in any samples that came from the koalas that died. In line 442, this is clarified: Lonepinella is "absent in at least one koala that died after antibiotic treatment."  Suggest rewording line 341 so that it becomes clear that Lonepinella was found in some but not all koalas that died.

Line 371: Change "as strong of impacts" to "as strong of an impact"

Line 369-370: Suggest removing the "1) low doses of antibiotics used here. There could be many explanations… for example."  Your beta diversity results (Lived vs. Control and Died vs. Control) demonstrate that antibiotics seem to have a clear effect on microbial composition - even though they did not significantly affect alpha diversity. The other 2 putative explanations you list here are stronger and more plausible.

Line 387: Change "passed away" to "died"

Line 450-452: I suggest adding a brief caveat at the end of this paragraph.  This study (for ethical reasons) did not allow you to examine koalas that died that did not receive antibiotics. As such, it is possible that the course of the Chlamydia infection itself affects Lonepinalla presence / abundance independent of antibiotics.  (That said, this is more of a scientific point than a clinical point, as the treatment for lack of Lonepinalla due either to antibiotics or Chlamydia would still be to help koalas recover their Lonepinalla populations)


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

Input:
Title: CHARACTERIZATION OF SHIFTS OF KOALA (PHASCOLARCTOS CINEREUS) INTESTINAL MICROBIAL COMMUNITIES ASSOCIATED WITH ANTIBIOTIC TREATMENT
Review round: 2
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: The authors have adequately addressed the concerns raised in my previous review.
Validity of the findings: Given the limitations of the study, the work presents a characterization of the gut community of koalas receiving or not receiving antibiotics. While descriptive in nature, this work will be of value to researchers in the field, and greatly expands our understanding of the koala gut microbiota.
Additional comments: In general, the authors have addressed the reviews and this iteration of the manuscript is significantly improved. I do have a couple of minor suggestions for the authors to consider:

1. Line 95 indicates that import approval was received from the "United States of America Government". This is rather non-specific, and should be addressed. In particular, I am guessing import permits of some kind were obtained from UW Fish and Wildlife Services? I do not believe USDA APHIS controls import of materials from animals like Koalas. If so, a proper import permit ID should be included here.

2. In the materials and methods, it is unclear where specific activities were performed. I am guessing that sequencing was performed at UC Davis, from DNA material extracted in Australia? This should be noted and the specific sequencing facility should be referenced.

3. Lines 339 - 342 - is there a reason for including the phrase "New.Reference"? Why not simply OTU131? This would make for a cleaner reading and presentation of the OTU numbers.


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: OUT OF ASIA: MITOCHONDRIAL EVOLUTIONARY HISTORY OF THE GLOBALLY INTRODUCED SUPRALITTORAL ISOPOD LIGIA EXOTICA
Review round: 1
Reviewer: 1

Output:
Basic reporting: This MS uses professional English, provides a very good literature coverage, has a good structure, and offers the necessary raw data in the supplement.
Nevertheless, it fails in one crucial issue: the results obtained by a short mtDNA gene fragment cannot actually test authors' hypotheses in a suficient way, so that all further discussion is redundant.
Experimental design: Experimental design and methods, if we exclude the number and length of gene fragments used, are very good, using state-of-the-art phylogenetic approaches and tools. The research question is valid and interesting, but again, the problem lies with the number of genes targeted, which undermines the whole endeavor.
Validity of the findings: As arleady mentioned, the main problem with this MS is the data used for testing hypotheses. Today, taking into account the availability and reduced cost of relevant analyses, sequences of such a short mtDNA fragment cannot be considered as adequate evidence to test hypotheses of phylogeography and origins of clades. Therefore, I suggest that the authors continue with several more genes, including nuclear ones, or even applying RADseq approaches, so that they are able to support their claims unambiguously.
Additional comments: Given the availability of samples from various localities, I believe that the authors can add more gene markers to their data quite easily and soon, so that their work gains more power and validity. Of course, I see that such data may not be available for all localities (for which GenBank sequences were used here), but I'm sure it's relatively easy to obtain fresh Ligia material from at least some of these via colleagues or even amateurs at the respective regions, given that these animals are easy to sample. I'm sure that even if the authors do not manage to include all localities for which 16S data are available online, the inclusion of more gene markers and, maybe, novel NGS approaches will render their work far more powerful and robust.
A less important issue is that of terminology used for L. exotica, which is characterised as 'invasive' in many parts of the text. The authors might consider using another term, like 'exotic' or 'alien', given that invasiveness has not been actually documented for this species, and in fact, it has been assigned this label only in eastern USA coasts (again without much documentation). Invasive species should have been shown to negatively affect local biodiversity, ecosystems or human economy. If this has not been documented or does not happen, then the species are just 'alien' or 'exotic'.


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: OUT OF ASIA: MITOCHONDRIAL EVOLUTIONARY HISTORY OF THE GLOBALLY INTRODUCED SUPRALITTORAL ISOPOD LIGIA EXOTICA
Review round: 1
Reviewer: 2

Output:
Basic reporting: This is a very interesting dataset from a very successful invasive species. However it seems that the European distribution of the species was completely ignored throughout the manuscript and the only mention to this in Introduction hypothesizes that it has originated in the region. The authors should be more cautious in their discussion since their study area does not include any European locality. The idea mentioned in lines 128-132 is repeated in lines 314-317 and supported only with self citations (6-7 studies). Technically there is nothing wrong however in my opinion this should be avoided.
Experimental design: no comment
Validity of the findings: Although based on the data available the native range of L. exotica seems to be located in Asia, the  entire European distribution of the species is not included in this study and there should be a reference to this in Discussion. Specially since before the closure of the Tethys  Sea these two regions were connected. I think, based on the data, the most objective conclusion would be that the origin of the species is not in the new world. The fact that unpublished phylogenetic analyses retrieved L. exotica and L. cinerascencis (only distributed in Asia) as sister taxa does not in itself support an Asian origin. First there are many species in Ligia genus and it is not clear whether they were all included in the mentioned (unpublished) phylogenetic reconstruction, second if these results are based in only one mitochondrial gene they could also be meaningless. For this reason I think the phrase "Thus, the reciprocal monophyly of L. cinerascens and L. exotica is well-supported" should be removed.  However most of the species of Ligia seem to be restricted to Asia (based on WORMS) which suggests that most of the genus diversified in the region and the authors could use this argument in their favour. Discussion between lines 376 and 414 is also somewhat speculative but interesting.
Additional comments: line 275 please add the word clade before B;
line 280, please add the word clade before C.


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: OUT OF ASIA: MITOCHONDRIAL EVOLUTIONARY HISTORY OF THE GLOBALLY INTRODUCED SUPRALITTORAL ISOPOD LIGIA EXOTICA
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors have clarified all the points mentioned in my previous review.
Experimental design: no comments
Validity of the findings: The authors have changed the manuscript in order to address the previous concerns
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: THE ASSOCIATION BETWEEN ELEVATED SERUM URIC ACID LEVELS AND ISLET Β-CELL FUNCTION INDEXES IN NEWLY DIAGNOSED TYPE 2 DIABETES MELLITUS: A CROSS-SECTIONAL STUDY
Review round: 1
Reviewer: 1

Output:
Basic reporting: The Authors present a paper, in which they evaluate the association between uric acid and beta cell function indexes. It is an up-to-date topic,  since a lot of researchers are investigating this issue and the underpinning mechanisms.
In this paper, gender differences are not focused adequately, as this should implicate two distinct and separate analyses,  showing a first table in which all data are included and successive tables containing data separated by gender.  Therefore, the authors have two possibilities: a) change the title of the manuscript, and omit this issue, or b) reanalyze data accordingly.
English needs improvement.
Abstract: In the Methods section, part of the last sentence should be omitted (“and identified….”) as it is a conclusive remark. In the Results, first line: if UA is measured in μmol/L, this should be added. Also, please specify what are the numbers in parentheses.
Introduction:
Line 67: “Credence in UA as…” should be replaced by “The idea of UA as….”
Lines 75-76: Researches addressing this issue should be mentioned, with the addition of their references (and novelty of this study briefly reported  in the discussion).
Jia L, Xing J, Ding Y, Shen Y, Shi X, et al. (2013) Hyperuricemia Causes Pancreatic b-Cell Death and Dysfunction through NF-kB Signaling Pathway. PLoSONE 8(10): e78284.
Robles-Cervantes JA, Ramos-Zavala MG, Gonzalez-Ortiz, et al. Relationship between serum concentration of uric acid and insulin secretion among adults with type 2 diabetes mellitus. Int J Endocrinol 2011; 2011:107904.
Tang W, Fu Q., Zhang Q, et al. The association between serum uric acid and residual b-cell function in type 2 diabetes. J Diabetes Res 2014; 2014:709691.
Ling Y, Li XM, Gu Q, Gao X. Correlation of serum uric acid and islet beta cell functions in female type 2 diabetics. Zhonghua Yi Xue Za Zhi 2012, 92:541-5.
Methods:
Line 86: “untreated diabetes” is presumably “untreated type 2 diabetets”. Authors should mention how type 1 diabetes was excluded.
Lines 110-111:  Are the authors sure that glucose was measured in plasma and insulin in serum? This implies the collection of two different blood tubes. This should be re-checked.
Discussion:
Line 210: “better” is not clear. Please specify.
Line 247: ref. 28 should be placed after “endothelial cells”.
Line 250: an appropriate reference should be indicated.
Line 254: It could be added “These results may be interpreted as due to differences between rodents and humans”.
Line 255: “obviously” should be omitted.
Line 258: the authors should speculate about potential molecular mechanisms by which UA affects insulin secretion and insulin resistance. For example, they could add the following: “As many studies have been undertaken to better understand the complex molecular mechanisms inducing insulin secretion and insulin resistance, including studies that address potential target genes and pathways (ref….), further investigations are necessary to delineate the molecular role of UA in this context”.
Arcidiacono B., Iiritano S., Chiefari E., et al. “Cooperation between HMGA1, PDX-1, and MafA is Essential for Glucose-Induced Inuslin Transcription in Pancreatic Beta Cells”. Front Endocrinol 5:237. (2015)
Ohneda K., Ee H., German M. “ Regulation of insulin gene transcription”, Seminars in cell & Developmental Biology, Vol. 11);. 227-23. (2000)
Chen CC, Wu JY, Chang CT, et al. “Levels of retinol-binding 4 and uric acid in patients with type 2 diabetes mellitus. Metabolism 58:1812-6 (2009)
Bianconcini A., Lupo A., Capone S., “ Transcriptional activity of the murine retinol-binding protein gene is regulated by a multiprotein complex containing HMGA1, p54 nrb/NonO, protein-associated splicing factor (PSF) and steroidogenic factor 1 (SF1)/liver receptor homologue 1 (LRH-1)”, Int J Biochem Cell Biol, vol.11; pp. 2189-203. (2009)
Zhang Y, Yamamoto T, Hisatome I, et al. Uric acid induces oxidative stress and growth inhibition by activation adenosine monophosphate-activated protein kinase and extracellular signal-regulated kinase signal pathways in pancreatic beta cells. Mol Cell Endocrinol 2013; 375:89-96.
References:
References should be implemented as suggested.
Experimental design: Gender differences should be properly addressed, unless this is not indicated in the title (see basic reporting).
Validity of the findings: The novelty of this study should be briefly addressed in the discussion, in the light of previous similar findings.
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: THE ASSOCIATION BETWEEN ELEVATED SERUM URIC ACID LEVELS AND ISLET Β-CELL FUNCTION INDEXES IN NEWLY DIAGNOSED TYPE 2 DIABETES MELLITUS: A CROSS-SECTIONAL STUDY
Review round: 1
Reviewer: 2

Output:
Basic reporting: Authors investigate the relationship between uric acid and insulin secretion and function. Authors should better address previous literature in the field, and novelty should be adequately discussed (see references below, which should be cited).
Robles-Cervantes JA, Ramos-Zavala MG, Gonzalez-Ortiz, et al. Relationship between serum concentration of uric acid and insulin secretion among adults with type 2 diabetes mellitus. Int J Endocrinol 2011; 2011:107904.
Jia L, Xing J, Ding Y, et al. Hyperuricemia causes pancreatic beta-cell death and dysfunction through NF-kB Signaling Pathway. PLoS ONE 2013, 8: e78284.
Methods and statistics
Why did authors use BMI criteria for Caucasian instead of Asia-Pacific WHO criteria? The study participants were from China; thus, it would be more proper to use Asian-Pacific BMI cut-off levels in statistic. Please redo do statistic using the Asian-Pacific WHO BMI criteria.
It is not clear if the participants were only diagnosed using 75g OGTT. Did participants were diagnosed under any other WHO criteria?
Discussion
Line 264, there are no references concerning the important role of diet and weight loss in diabetes.  References could include:
Greco M, Chiefari E, Montalcini T, et al. Early effects of a hypocaloric, mediterranean diet on laboratory parameters in obese individuals. Mediators of Inflammation 2014, 2014:750860.
Grams J, Garvey WT. Weight loss and the prevention and treatment of type 2 diabetes using lifestyle therapy, pharmacotherapy, and bariatric surgery:mechanism of action. Curr Obes Rep, 2015, 4:287-302.
English should be well checked all over the text for grammar and typo errors.
Experimental design: See Basic Reporting
Validity of the findings: Authors should point out in the introduction or in the discussion what is the novelty of this paper in consideration of previous similar reports.
Additional comments: This manuscript requires additional analysis.


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: CURRENT STATE OF KNOWLEDGE ON WOLBACHIA INFECTION AMONG COLEOPTERA: A SYSTEMATIC REVIEW
Review round: 1
Reviewer: 1

Output:
Basic reporting: - language ok, but many typos and orthographic errors
Experimental design: - interesting topic
- severe doubts on completeness of data source
- table S1 incomplete
Validity of the findings: - review article, no essentially new findings
Additional comments: Kajtoch and Kotásková present a review about Wolbachia infections in Coleoptera. Similar reviews have, in the last years, been published for other insect species and, while not adding many new facts to the body of literature, they are usually helpful tools for further research. Until now, such a review was missing for beetles.

My main concern here is the integrity of the original dataset. The authors used Google Scholar for literature search. This uncurated, crawler-based search engine is without any doubts extremely valuable for everyday literature recherché, but has some notable limitations: It is notoriously missing important papers, especially if published in the pre-digital era, and, at the same time, adding doubtful or obviously non-scientific sources to the search results. The latter issue may be overcome by careful manual inspection of the search results, the former one not. For these reasons, Web of Science (WoS) has remained the gold standard for scientific literature research. This database has its limitations, too, and is furthermore prohibitively expensive for smaller research institutions, but it is manually curated and covering all SCI journals since more than 100 years.

The authors mention that they retrieved 113 hits by searching for “Wolbachia” AND “Coleoptera”, “Wolbachia” AND, “beetles”, and “Wolbachia” AND “[names of all beetle families, separately]”. It is slightly disturbing that these hits also contain work not found in the database but added by the authors based on not further defined "expert knowledge", and that this material contains non-citable publications like unpublished articles and conference talks. I did a small experiment and searched WoS (retrieved 26 November 2017) for the first two terms the authors have used. "Wolbachia AND coleoptera" gave 164 hits, "Wolbachia AND beetles" 157 hits, and the merging of both lists resulted in 232 papers. While several of these hits would be lost in the manual verification step, I am still sure that the data source used here is highly incomplete.

I have also one important technical remark on the data source as given in Supplementary Table S1: The citations are worthless when no biographic information (year, journal name, volume, page numbers) is provided. This essential information must be added, otherwise the work is unpublishable.

Minor remarks:

- l156: "Maximum likelihood trees were inferred using Maximum likelihood" – well, this does not come as a surprise.
- l159: "substation model" ?
- l343: Is this a "tree", or is it a "network"? Only one can apply.
- l409: Please do not begin sentences with words like "But".
- l411f: NGS is currently revolutionizing molecular ecology and will have its merits in many Wolbachia-related projects yet to come. Anyway, I do not agree that NGS is mandatory to understand Wolbachia diversity. The majority if insect species, and thus Wolbachia strains, is located in countries that, for simple economical reasons, cannot afford NGS in the near to middle future. In contrast, universities in low developed countries are capable of PCR and Sanger techniques, and they sit at the source of large parts of Earth's biodiversity. We should rather encourage such institutions to assess the local biodiversity with simple but efficient techniques like MLST, not discourage them with the NGS overkill.
- l453: Wolbachia gene transfer into the nucleus has been firstly described ten years ago (Dunning Hotopp et al., 2007), and that only two examples are known today is simply not true. Koutsovoulos, Makepeace, Tanya, & Blaxter (2014) and Funkhouser-Jones et al. (2015) are two quite recent examples out of several others. It is shameful when a literature review article misses a broad body of published research.
- Finally, the paper contains a lot of typos, false uses of the comma, missing or additional spaces, and some orthographic errors. It should be copy-edited carefully.

References

Dunning Hotopp, J. C., Clark, M. E., Oliveira, D. C. S. G., Foster, J. M., Fischer, P., Muñoz Torres, M. C., … Werren, J. H. (2007). Widespread lateral gene transfer from intracellular bacteria to multicellular eukaryotes. Science (New York, N.Y.), 317(5845), 1753–1756. doi:10.1126/science.1142490
Funkhouser-Jones, L. J., Sehnert, S. R., Martínez-Rodríguez, P., Toribio-Fernández, R., Pita, M., Bella, J. L., & Bordenstein, S. R. (2015). Wolbachia co-infection in a hybrid zone: discovery of horizontal gene transfers from two Wolbachia supergroups into an animal genome. PeerJ, 3, e1479. doi:10.7717/peerj.1479
Koutsovoulos, G., Makepeace, B., Tanya, V. N., & Blaxter, M. (2014). Palaeosymbiosis Revealed by Genomic Fossils of Wolbachia in a Strongyloidean Nematode. PLOS Genetics, 10(6), e1004397. doi:10.1371/journal.pgen.1004397


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: CURRENT STATE OF KNOWLEDGE ON WOLBACHIA INFECTION AMONG COLEOPTERA: A SYSTEMATIC REVIEW
Review round: 1
Reviewer: 2

Output:
Basic reporting: see below
Experimental design: see below
Validity of the findings: see below
Additional comments: Review for Peerj-21704

The paper by Kajtoch & Kotásková is a nice summary of current knowledge on Wolbachia in beetles. Wolbachia is arguably the most common, and may be the most important endosymbiont of arthropods. There are a lot of studies on Wolbachia in many host taxa, and especially for people new to this field, the large number of studies may be overwhelming. Reviews on endosymbionts of particular host taxa such as the one presented here are therefore very helpful and represent valuable resources for the community.

I want to commend the authors for the effort put into compiling this dataset, which is mostly clearly presented and illustrated. The only major issue I see with this manuscript is the lack of any synthesis that goes beyond summarizing the findings of previous studies. It would be interesting to know if, in the authors opinion, beetles are peculiar Wolbachia hosts in any respect, or if there is something especially noteworthy that only seems to apply to beetles and not any other Wolbachia hosts. Furthermore, everything that is mentioned in the “outlook” section of the manuscript applies to Wolbachia studies in general and is not specific to Wolbachia-beetle interactions.

There are other -mostly minor- issues that should be addressed in a revision. Please find details on these below, hopefully constructive.

Line 81ff:
As potential addition to this list, there are reviews on mites (Chaisiri et al. 2015) and ants (Russell 2012) as well. The latter one also compares Wolbachia incidence between many different arthropod groups, and might be worth having a look for inspiration.

Line 88:
“[beetles] are the most species rich organisms on earth […]” – One often finds similar statements, but they do not make sense at all. Insects are even more species rich than beetles, and arthropods are more species rich than insects. This is just to illustrate that all phylogenetic ranks (except maybe species) are artificial, and therefore those statements should be avoided.

L109–112:
I don’t know of any study showing that Wolbachia is “responsible” for speciation, if the authors claim this here, it should be referenced with an example.

L120–121:
As far as I know, google searches always use the boolean “AND”, regardless if it is typed in the search field.

L126:
I searched my personal literature database and found a number of papers about Wolbachia in beetles that are not mentioned in your manuscript (Pankewitz et al. 2007; Chafee et al. 2010; Kageyama et al. 2010; Toju & Fukatsu 2010; Xue et al. 2011; Toju et al. 2013; Iwase et al. 2015). I am unsure whether this is due to these things not showing up in your search because the papers used are not listed anywhere separately. I would suggest to provide a list of all the papers used and, should you have missed the papers mentioned above, re-design your search strategy to accomodate potential shortcomings that have led to the oversight of these.
Another way to discover potentially overlooked Wolbachia-beetle associations would be to check the NCBI nucleotide database for Wolbachia sequences from beetles. Maybe also worthwhile is to search the databases used by previous meta-analyses investigating global Wolbachia incidences (Weinert et al. 2007; Hilgenboecker et al. 2008; Russell 2012).

L178–179
Please clarify or rephrase.

L198
From here on, the figure numbering seems to be wrong. Also, Figure 2 (“ Change in the number of publications considering Wolbachia infection among Coleoptera”) is not mentioned anywhere.

L229ff
The numbers here and elsewhere in the manuscript would be more meaningful if they where corrected for the number of known species and the number of species tested. E.g., with 8 Wolbachia- positive species found, Hydraena is listed as one of the most “richly infected genera”.  However, this is a huge genus, with at least a few hundred described species, so what does a finding of 8 infected species mean? I think in a review like this, these numbers should be put in perspective.

L294ff
Were these cases of CI experimentally determined?

L319ff
I am unsure how helpful the phylogenetic analyses are. What is the aim here? The discussion doesn’t really go beyond supergroup designation, and this is already discussed in the original publications. Maybe think about omiting this part or moving it into the supplement.

L327
“Intermediate between supergroup F and other supergroups” is not really a valid description of a phylogenetic tree.

L380
Suggest to change “proof” to “evidence for”

L397–398
Which search is meant here? Is there a reference missing?

L439–440
Please elaborate on how this would help in species designations in Wolbachia, this is not obvious to me.

Fig. 3
Maybe think about replacing the number of infected species with a stacked bar showing the number of tested/infected species.

Fig. 4
It looks like you are comparing all Coleoptera vs two beetle families. If the families are included in the Coleoptera counts, this would not be valid. If that is not the case, please call this group it “other Coleoptera” or similar for clarification. Also, please provide more details in the Figure legend.

Fig. 5, 6, 8, 9
This is more a matter of personal taste, but it was repeatedly argued that pie charts are very difficult to interpret (especially 3D pie charts).

Fig. 7
As mentioned above, relative proportions would be more insightful here.

Fig. 9
This is a bit hard to follow. What is “some infected” and “all infected”?

References

Chafee ME, Funk DJ, Harrison RG, Bordenstein SR (2010) Lateral Phage Transfer in Obligate Intracellular Bacteria (Wolbachia): Verification from Natural Populations. Molecular Biology and Evolution 27, 501–505.

Chaisiri K, McGarry JW, Morand S, Makepeace B (2015) Symbiosis in an overlooked microcosm: a systematic review of the bacterial flora of mites. Parasitology FirstView, 1–11.

Hilgenboecker K, Hammerstein P, Schlattmann P, Telschow A, Werren JH (2008) How many species are infected with Wolbachia?- a statistical analysis of current data. Fems Microbiology Letters 281, 215–220.

Iwase S, Tani S, Saeki Y, Tuda M, Haran J, Skuhrovec J, Takagi M (2015) Dynamics of infection with Wolbachia in Hypera postica (Coleoptera: Curculionidae) during invasion and establishment. Biological Invasions , 1–10.

Kageyama D, Narita S, Imamura T, Miyanoshita A (2010) Detection and identification of Wolbachia endosymbionts from laboratory stocks of stored-product insect pests and their parasitoids. Journal of Stored Products Research 46, 13–19.

Pankewitz F, Zollmer A, Hilker M, Graser Y (2007) Presence of Wolbachia in insect eggs containing antimicrobially active anthraquinones. Microbial Ecology 54, 713–721.

Russell JA (2012) The ants (Hymenoptera: Formicidae) are unique and enigmatic hosts of prevalent Wolbachia (Alphaproteobacteria) symbionts. Myrmecological News 16, 7–23.

Toju H, Fukatsu T (2010) Diversity and infection prevalence of endosymbionts in natural populations of the chestnut weevil: relevance of local climate and host plants. Molecular Ecology 20, 853–868.

Toju H, Tanabe AS, Notsu Y, Sota T, Fukatsu T (2013) Diversification of endosymbiosis: replacements, co-speciation and promiscuity of bacteriocyte symbionts in weevils. Isme Journal 7, 1378–1390.

Weinert LA, Tinsley MC, Temperley M, Jiggins FM (2007) Are we underestimating the diversity and incidence of insect bacterial symbionts? A case study in ladybird beetles. Biology Letters 3, 678–681.

Xue HJ, Li WZ, Nie RE, Yang XK (2011) Recent Speciation in Three Closely Related Sympatric Specialists: Inferences Using Multi-Locus Sequence, Post-Mating Isolation and Endosymbiont Data. Plos One 6, .


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: CURRENT STATE OF KNOWLEDGE ON WOLBACHIA INFECTION AMONG COLEOPTERA: A SYSTEMATIC REVIEW
Review round: 1
Reviewer: 3

Output:
Basic reporting: The review on Wolbachia in Coleoptera summarizes the data obtained from a thorough literature search and nicely illustrates the basic results by pie charts. As such the paper is a very nice resource for future studies. I am somewhat concerned, however, that the authors are not always sufficiently careful not to overstretch the conclusions of the original papers. To give two examples: I reread two of the heavily quoted papers, Mazur et al. 2016 and Jäckel et al. 2013, and don't agree that Mazur et al. unambigiously demonstrated that Wolbachia induced or reinforced parthenogenesis in Eusomus ovulum (l. 311 - 313) - it could also be that Wolbachia infected the beetles when they were already parthenogenetic. The Jäckel paper on the other hand talks about the possible connection between CI and selective sweeps, but does not unambigiously demonstrate that this was the case in the Altica beetles as the authors claim (l. 294-295). Especially since people tend to quote from reviews, the authors need to be extremely careful to correctly quote the results.
While the structure of the paper is mostly straight forward I feel that the introduction should be restructured. The general information on Wolbachia effects given in l. 95-l. 113 should be moved further up and substantiated with the best quotes across all insects, not just with those from the beetle literature. The aim of the study, i.e. compiling the data for beetles l. 81-94, should be the last part of the introduction.
When the authors come back to the idea of splitting Wolbachia into several species (l. 440-442), they should discuss at least roughly in how far their phlylogenetic analyses agree or do not with the proposed distinctions
The English would benefit from editing by a native speaker, e.g.
l. 233 and all pie charts - replace 'share' by 'proportion'
l. 236 and 243 replace 'verified' by 'investigated'
l. 244 replace 'members' by 'of the species'
l. 256 rearrange to 'supergroups A and B' and l. 259 to 'supergroup F'
l. 270 replace 'within' by 'represented by'
and many more instances where an English correction would help.
Experimental design: o.k.
Validity of the findings: see above
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: CURRENT STATE OF KNOWLEDGE ON WOLBACHIA INFECTION AMONG COLEOPTERA: A SYSTEMATIC REVIEW
Review round: 2
Reviewer: 1

Output:
Basic reporting: English very much improved, references mostly fine, well structured.
Experimental design: Review article, no new findings. Serach strategy for literature now state of the art, inclusion criteria now well defined.
Validity of the findings: Data robust, conclusions clear, except for the wsp phylogeny - see below.
Additional comments: The authors have implemented most of the issues raised by the reviewers and massively improved the ms. Before I can recommend an accept, a few points should still be addressed.

Major issues:

l 78f: Several attempts have failed to reproduce the findings of Jeyaprakash and Hoy (2000), and, although never retracted, most Wolbachia researches tend to not citing this reference anymore. The current valid reference for Wolbachia abundance is Zug and Hammerstein (2012).
l 142: Please provide details which statistical tests have been used and where.
l 355f: It is not valid to use wsp for phylogenetic reconstruction, see Baldo et al. (2005). I would like most if this phylogeny is simply removed – the ms would lose in fact nothing from it. If the authors decide not to remove it, they have, anyway, to discuss why it is invalid. And by the way, it is still not a network!
l 416: I absolutely agree on the causes of Wolbachia underestimation, but there is another and important cause that should be mentioned: Low titer infections that are under the detection limit of conventional PCR, see, e.g., Arthofer et al. (2009), Schneider et al. (2013).
l 458: "led to speciation" is very strong, until now there is not a single, hard evidence that Wolbachia alone can split a species into two. Tone down to something like "have probably been involved in speciation".
l 469f: Horizontal transmission was considered as an event that happens in evolutionary timescales. Only recently, Schuler et al. (2013) showed that such a transfer can happen within a few years after arrival of a new strain – I think this should be mentioned here.

Minor issues:

l 41: Testing and examining are in fact the same. Please remove "and/or examined".
l 42: Add comma before "and".
l 61: Add comma after "research".
l 87: One dot too much in the reference.
l 221: Insert comma after "however".
l 244: Insert "of" before "species".
l 247: Replace colon with comma.
l 278: Missing space after "tomentosus,".
l 285: Insert comma after "22)".
l 307: Missing space after "Euwallacea,".
l 379: was -> were
l 432: Remove comma after "et al.".
l 443: Tautology, remove "single".
l 444: also -> only
l 469: suggested -> suggest
l 473: Remove comma.
l 487: Remove comma.
l 488f: The authors talk about "only three studies" but have seven papers in the according reference; can it be that this is misplaced?

References

Arthofer W, Riegler M, Avtzis DN, Stauffer C. 2009. Evidence for low-titre infections in insect symbiosis: Wolbachia in the bark beetle Pityogenes chalcographus (Coleoptera, Scolytinae). Environ. Microbiol. 11:1923–1933.
Baldo L, Lo N, Werren JH. 2005. Mosaic Nature of the Wolbachia Surface Protein. J. Bacteriol. 187:5406–5418.
Jeyaprakash A, Hoy MA. 2000. Long PCR improves Wolbachia DNA amplification: wsp sequences found in 76% of sixty-three arthropod species. Insect Mol. Biol. 9:393–405.
Schneider DI, Riegler M, Arthofer W, Merçot H, Stauffer C, Miller WJ. 2013. Uncovering Wolbachia Diversity upon Artificial Host Transfer. PLoS ONE 8:e82402.
Schuler H, Bertheau C, Egan SP, Feder JL, Riegler M, Schlick-Steiner BC, Steiner FM, Johannesen J, Kern P, Tuba K, et al. 2013. Evidence for a recent horizontal transmission and spatial spread of Wolbachia from endemic Rhagoletis cerasi (Diptera: Tephritidae) to invasive Rhagoletis cingulata in Europe. Mol. Ecol. 22:4101–4111.
Zug R, Hammerstein P. 2012. Still a Host of Hosts for Wolbachia: Analysis of Recent Data Suggests That 40% of Terrestrial Arthropod Species Are Infected. PLoS ONE 7:e38544.


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: CURRENT STATE OF KNOWLEDGE ON WOLBACHIA INFECTION AMONG COLEOPTERA: A SYSTEMATIC REVIEW
Review round: 2
Reviewer: 2

Output:
Basic reporting: see below
Experimental design: see below
Validity of the findings: see below
Additional comments: Admittedly, I am a bit disappointed by this revised version of the ‘Wolbachia in beetles review’ of  Kajtoch & Kotásková, as they have chosen to ignore several of my suggestions. I do understand that responding to reviewer’s comments can be tedious and sometimes annoying, but just as I haven taken the time to carefully review this paper, I wished the authors had taken the time to carefully address my comments. This does not at all mean they have to agree with everything I said, but I think its fair to expect a response.

Specifically, I suggested to check the NCBI Genbank database for potentially overlooked beetle-Wolbachia associations. I further suggested to check previously databases of Wolbachia-host associations that were compiled by authors of other meta-analyses, such as the one by Weinert et al (2015, http://doi.org/10.1098/rspb.2015.0249). I did the suggested searches and found an additional 184 (!) genera of beetles that were reported to harbour Wolbachia in the literature, but are missing from the current paper (the list is attached below). Especially the search in the Weinert et al database would have been very straightforward, as the authors have provided their dataset as supplementary file to their paper (freely accessible here: http://rspb.royalsocietypublishing.org/highwire/filestream/66583/field_highwire_adjunct_files/0/Database.xlsx). As the current paper aims to summarize all current knowledge on Wolbachia in beetles, I suggest that the authors check these missing entries and the accompanying papers, and include the valid reports to their list of Wolbachia infected species. Each of the genera should be in either the Weinert et al database or retrievable from NCBI’s Genbank through ‘genus AND Wolbachia’ searches.

Other, minor comments:

L41–42 ‘Future studies on Wolbachia diversity in Coleoptera should still be based on the Multi-locus Sequence Typing system’ – why? This is not really discussed in the paper.

L90–91 ‘Some of these effects are responsible for […] speciation […]’ – There is no evidence for that (or if there is, please cite). I already mentioned this in first my review.

L106–107 ‘[…] beetles (Coleoptera), which are the most species rich and diversified group of organisms on Earth […]’ – This doesn’t make sense. I already mentioned this in first my review.

L144 I am puzzled by the fact that my search on NCBI’s Genbank revealed many additional Wolbachia- beetle associations (see above).

L228ff I think it would be helpful to relate the numbers of detected species to the number of known species of that taxon. This would put statements such as ‘most richly infected genus’ in perspective. Although in the rebuttal you claim these numbers are in the paper, I can’t find them anywhere. If you disagree with my view that this would be helpful, please explain. This is another point I have already mentioned in my first review.

L488–491 You say there’s only 3 studies, but then cite 8?

List of beetle genera with reports of Wolbachia not mentioned in the paper:
Acanthoscelides, Acoma, Acromis, Adoretus, Aeolesthes, Aeoloderma, Agelasa, Agra, Allonyx, Alphitobius, Anadastus, Anaspis, Anatis, Ancylopus, Anisosticta, Anomala, Anthonomous, Apalochrus, Aphidecta, Aslamidium, Asphaera, Aspidomorpha, Astycus, Aulacophora, Basilepta, Blosyrus, Bolbocerastes, Bolitotherus, Brachysomus, Brentus, Bruchidius, Bruchus, Brumoides, Byctiscus, Calomyterus, Calypteron, Calyptocephela, Canthidium, Canthon, Carpophilus, Centricnemus, Cephaloleia, Cetonia, Chauligognathus, Chersinellina, Chlaenius, Chrysolina, Cicindela, Cis, Clytus, Coelophora, Colaspis, Coleomegilla, Colpodes, Coptocycla, Coptodear, Cossonus, Cryptoglossa, Cryptolaemus, Cryptolestes, Cyclocephala, Cycloneda, Cycnotrachelus, Cypherotylus, Deloyala, Delphastus, Dicladispa, Dicranoncus, Diplotaxis, Disonycha, Drypta, Echinocnemus, Enoploplactus, Epilachna, Eubrianax, Eucryptorrhynchus, Eugnathus, Exochomus, Formicomus, Foucartia, Galerita, Gallerucida, Geotrupes, Germarostes, Glaresis, Gnathocerus, Grammoptera, Guignotus, Haptoncus, Harpalus, Hippodemia, Hotaria, Hybosorus, Hydrochus, Hydroglyphus, Hydronomidius, Hydrophilus, Imatidium, Larinus, Lema, Leptinotarsa, Leptura, Ligyrus, Liparus, Listrus, Lixus, Lobiopa, Lucanus, Lycostomus, Lygaria, Medythia, Megalocaria, Megalodacne, Micraspis, Monolepta, Mordellistena, Morion, Myrrha, Myzia, Neoglanis_or_Donus, Nicrophorus, Notoxus, Omorgus, Oncocerna, Onthophagus, Ophionea, Oryzophilus, Oulema, Oxythyrea, Pachyschelus, Palorus, Paracycnotrachelus, Parathyce, Passalus, Pentagonica, Peridinetus, Phelypera, Phrixopogon, Phyllobius, Phyllophaga, Phyllotreta, Platyphora, Pleocoma, Pogonocherus, Polychalma, Propylaea, Prosopodonta, Pselaphacus, Pseudimatidium, Pseudopthalmus, Psyllobora, Rhagonycha, Rhaphuma, Rhinostomus, Rhynchophorus, Rhyzobius, Rhyzopertha, Scarabaeus, Scarites, Sciaphilus, Scymnus, Semiotus, Serangium, Serica, Smaragdina, Spaethiella, Stegotes, Stenopterus, Stenotarsus, Sthenias, Subcoccinella, Submera, Sueus, Tapinaspis, Temnochila, Tenebrio, Tenebroides, Tetraopes, Trachyaphthona, Trogoderma, Typocerus, Tytthaspis, Xestolabus, Zigia


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: CURRENT STATE OF KNOWLEDGE ON WOLBACHIA INFECTION AMONG COLEOPTERA: A SYSTEMATIC REVIEW
Review round: 2
Reviewer: 3

Output:
Basic reporting: The authors have significantly improved the paper and adhered to most points raised in the review. The paper can be accepted almost as is, just some minor mistakes or inconsistencies caught my attention upon rereading it.

minor comments:
l. 116 - 'aspects of research' would be better than 'groups of research'
l.326 - 'both Chrysomelidae' - what does that refer to?
l. 339 - rearrange to 'Diabrotica virgifera virgifera on maize'
l. 403 - delete 'for'
l. 464 - the singular of bacteria is bacterium; otherwise put your verbs in plural
l. 469 - et al. misplaced
l. 501 - only three studies have found ..... the number of references indicated is far higher
Experimental design: Has been improved by redoing the literature search on WoS.
Validity of the findings: no further comments
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: FIRST ENDEMIC FRESHWATER GAMMARUS FROM CRETE AND ITS EVOLUTIONARY HISTORY—AN INTEGRATIVE TAXONOMY APPROACH
Review round: 1
Reviewer: 1

Output:
Basic reporting: I think this is a wonderfully thought out and performed experiment with excellent results. The manuscript is clear with some grammatical issues (I suggested edits directly in the PDF file). The introduction and background are sufficient. My only concern are some missing references (Barnard & Barnard, 1983, Fabricius, 1775, Fiueroa et al., 2013, Latreille, 1818, Leach, 1814, Linnaeus, 1758, Pinkster, 1970, Stebbing, 1899). There are also several references in the reference section that are not cited in the text (Agusti et al., 2006, Azzaroli et al., 1980, Blackman et al., 2017, Creutzberg, 1963, Dermitzakis et al, 1981, Felsentstein, 1985, Hou and LI, 2010, Katoh et al., 2002, Popov et al., 2004, Stock 1977, 1980).
Experimental design: This is original research within the aims and scope of PeerJ, the experiment, methods, and results are well defined with clear relevance and a very important description of a new cryptic species.
Validity of the findings: The data is robust with multiple methods coming to the same conclusion. The conclusions are well stated and answer the original question without ambiguity. The DNA sequences were not provided, which is not a problem for me, but I am not sure about PeerJ's standards. The authors do state that they will be available upon publication in BOLD and GenBank.
Additional comments: I recommend to accept this publication but do suggest minor grammatical changes. Nicely written!


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

Input:
Title: FIRST ENDEMIC FRESHWATER GAMMARUS FROM CRETE AND ITS EVOLUTIONARY HISTORY—AN INTEGRATIVE TAXONOMY APPROACH
Review round: 1
Reviewer: 2

Output:
Basic reporting: Clear and relevant paper on the evolutionary history of endemic freshwater species. Convincing evidence. The English needs careful checking on the use of plurals and adjectives.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Complete and relevant paper on the evolutionary history of endemic freshwater species. Convincing evidence. The English needs careful checking on the use of plurals and adjectives. Sentences are sometimes too long. Punctuation might help clarity in such cases.


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: VALIDATION AND APPLICATION OF THE CHINESE VERSION OF THE PERCEIVED STRESS QUESTIONNAIRE (C-PSQ) IN NURSING STUDENTS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript requires through revision to conform with academic writing style. Specific comments are provided in the general comments section.
Experimental design: Design have some concerns, for example, probable bias in back-translation procedure, lack of validity measures. Specific comments are provided in the general comments section.
Validity of the findings: Data need to be checked again however, further details on methods and procedures of analysis used by the authors are required.
Additional comments: Considering the extensive amount of data, I would suggest the authors to separately present validation (?) and application as two sub study (with a split sample) in this article. With detailed analyses and separate discussions that could be more useful for the readers.
	The following section presents a few specific comments, however, these are only examples, when revising please check the manuscript for similar problems.
1.	The conclusion written in the abstract section seems inappropriate. Please revise.
2.	The CI values can be removed from the "Abstract" section.
3.	Line 39, 273: Check in-text citation, some characters are missing.
4.	The manuscript requires formatting. For example,  parentheses of many in-text citations are not separated by space after the last world immediately before it (line 44, 48).
5.	Line 45-46: It would be better to describe the "complicated environment" and "depressed atmosphere" instead of using these in their commonsense meaning (which may mean different things to different readers).
6.	Line 60-61: Please rephrase "stress-caused depression".
7.	Exaggerated claim: please rephrase these
a.	 irreparable damage (line 64)
b.	can only (line72);
c.	ideal universal scale (line 87).
8.	It would be a good idea to discuss other available scales for measuring perceived stress scale (such as the "Perceived Stress Scale" developed by Cohen) in the introduction section.
9.	Language correction required: line 81 - "content is" need to be "contents are";  line 88-90;
10.	Please add description/statistics on different validity and reliability of the PSQ 30 reported in original as well as different translated versions.
11.	Line 77: It sounds like two ways of using this questionnaire (general and recent) instead of two versions. Please clarify and revise subsequent sections as required.
12.	Line 85-86: It is not clear what the authors meant to express with the last clause of this sentence. It seems that this sentence is unnecessary (in its current form).
13.	Section 2.1: In the current form of paragraph, Firstly, Secondly, . . . . would fit better compared to First, Second, . . . ..
14.	Line 122: It is crucial that the comparison between original and back-translation version of the scale is done by a person outside the research team. The possibility of bias may undermine the value of the entire translation process. Please justify the reason for using the research team members in this. Clarify how this might have not caused any negative impact on the confidence regarding similarity of the translation and original version.
15.	The flow chart provided as Figure 1 needs to be parsimonious.
16.	Line 123-124: The word "points" is misleading and may be deleted.
17.	Line 126-129: How was the norm developed for the Spanish version? and on which population? It is not clear how that norm can be considered useful for (1)Chinese (2) Nursing students. Please justify the reason for using the Spanish norm for interpretation.
18.	Line 140: What is meant by "normative" is unclear.
Line 140-141: If you want to use this sentence, please clarify how you tested if the "type setting and printing of the scale was standardized".
19.	Line 159: Please clarify how you matched the test-retest data sheets as the responses were anonymous?
20.	Line 158: As the ethics committee has approved this, I believe possibilities of unequal relation between participants and administrator/researcher should not be a concern from my side. However, a 100% response rate is very high considering such large number of student participants in this study.
21.	Line 167: It is not clear why excel was used where the analysis used can be done with SPSS and AMOS.
22.	Line 174: revise to avoid redundancy.
23.	Table 1: Explain the purpose of grouping age in this manner (17-20 and 20-23).
24.	Note below Table 1 is redundant.
25.	Figure 2: It is unconventional to correlate error terms of different factors. Please explain the considerations based on which these were done. Please also compare the uncorrelated base model with the modified model. Discuss the influence of this modification in interpreting the findings.
26.	Provide citation for the critical values for each of the fit indices used in the Table 4.
27.	Line 216: Name of the dimensions (or factor number) need to be reported aside respective Cronbach's alpha values. An alpha value of 0.526 is not "acceptable" however, considering the low number of items (2; I assume it is Factor 5) it is understandable to have a low alpha.
28.	Line 241: The authors' claim of C-PSQ to have good validity is unjustified and should be revised. There are several important types of validation including construct validity and concurrent validity  which were missing in this research.
29.	Line 247-249: Visible difference in the structure and items clustering in the factors are present among different versions of PSQ (Table 3). Therefore, authors' claims regarding "similarity" and high "structural stability" can be debatable and require revision.
30.	Supplementary materials are in Chinese language, which need to translated for review.
31.	Please provide further details on the data collection procedure (one to one/group, self administered/interviewer administered, who collected that data, who took consent and how).
32.	Please provide details of the method used for factor analysis, my quick analysis with the provided data revealed some difference.


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: VALIDATION AND APPLICATION OF THE CHINESE VERSION OF THE PERCEIVED STRESS QUESTIONNAIRE (C-PSQ) IN NURSING STUDENTS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Basic reporting in this study is adequate.
Experimental design: Experimental design has been well defined.
Validity of the findings: This study has adequate analysis and interpretation. However, a few additions would have made the study design better:

a) There are no comparator scales to establish criterion and concurrent validity of the scale being assessed. Please, list it as a limitation of this study.
b) It would be interesting to make a table providing reliability and validity of this scale and different factor structures arising in different nations.
c) If different factor structures have been reported in different nations, it would interesting to compare them in this study sample using AMOS software and see which one has the best fit. AIC statistic can be an important measure in comparing them. Please refer to this paper to adopt their methods: https://www.ncbi.nlm.nih.gov/pubmed/28815479
Additional comments: I would like to congratulate the authors on conducting this study of public health importance. However, there are few comments that should be addressed before

a) This statement should move to discussion:  This score was lower than that of
ulcerative colitis patients in Susan Levenstein’s research(Levenstein et al. 1994).
b) The manuscript can benefit from improvement of English by a professional Anglophone editor.

Best wishes,


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: VALIDATION AND APPLICATION OF THE CHINESE VERSION OF THE PERCEIVED STRESS QUESTIONNAIRE (C-PSQ) IN NURSING STUDENTS
Review round: 2
Reviewer: 1

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


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

Input:
Title: LINKING INFLUENZA EPIDEMIC ONSETS TO COVARIATES AT DIFFERENT SCALES USING A DYNAMICAL MODEL
Review round: 2
Reviewer: 1

Output:
Basic reporting: -	The paper is written in professional English throughout. There are a few minor grammatical errors (e.g. line 23 the use of “the same factor”, line 71 the use of “on” and line 83 the use of singular “agent” and a few others) but all very minor.
-	The raw data is supplied but would be much better if it were in a standard machine-readable format like .csv or .txt. Having it in a PDF file is unusual and a bit annoying for anyone wishing to replicate the analyses. Ideally, the data could be in the .zip file containing the code with the same name as is used to import in the code. As it is, I don’t think the analysis is reproducible at least in part because the data cannot be easily read in.
-	In Figure 1 (and perhaps Figure 2 as well, although I feel less strongly about it here) it would be better to show the raw data. The boxplot is summarizing six data points with five and giving a false sense of a large dataset and estimated std deviation when there is actually very little data per row.
-	Overall the literature review is thorough.
-	Subscripts on lines 204 and beyond are not consistent. Are years subscripted with S or Y?
Experimental design: -	The rules for defining onset are not sufficiently precise or well-defined. E.g. What is several? More than 1? What does without explanation by another phenomenon mean? What if the week itself meets criteria 1 and 2? Under this definition, it would not be included because the previous and following week do not meet the conditions?
-	The most severe limitation of this study is the limited number of onsets (19 regions and 6 years, so just over 100 total observations). Given this, the authors are estimating a large number of coefficients from this dataset, in Table 4 there are 11 coefficients, which means barely 10 observations per coefficient. And other coefficients are fit and interpreted as well.
-	It is not statistically justifiable that this study has power to detect associations from as complex a model as this with as little data as they have. This is a larger concern given the complexity and multiple stages of the modeling that occur.
-	The “holiday effect” has been demonstrated to have an impact on flu dynamics in the US, so it seems like a major limitation that it is not incorporated here (line 145). (see, e.g. http://dx.doi.org/10.1371/journal.pcbi.1004382)
-	Is it a problem that the model (on line 222, e.g.) may be overly constrained by not having an intercept?
-	Some data appears to be missing (seen visually in the graphs). How is this dealt with in the analysis?
Validity of the findings: -	The authors spend quite a bit of time extolling the virtues of their approach but not enough time acknowledging the limitations. E.g. lines 81-89 discuss advantages of dynamic models without discussing their disadvantages (one that comes to mind is that they can be mis- or over-specified).
-	There is little discussion of the major limitation of the study, which is the sample size. More needs to be said about this, relative to the strength of the conclusions that are being drawn. How can we be confident in our conclusions with such a heavily adjusted analysis with such few datapoints?
-	I do not see how the conclusion on lines 367-369 are justified by the results shown. At best it is an over-confident statement.
Additional comments: Overall, my major concerns with this article revolve around the sample size and the complexity and quantity of the fitted models. I am concerned that many different inferences are being drawn from multiple multi-stage analyses of a small dataset, with no adjustment for multiple comparisons. Since the method is somewhat new and specialized, there is little intuition or formal work that we can rely on to understand how much power these models could be expected to have to detect true associations in the data.


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: LINKING INFLUENZA EPIDEMIC ONSETS TO COVARIATES AT DIFFERENT SCALES USING A DYNAMICAL MODEL
Review round: 2
Reviewer: 2

Output:
Basic reporting: One of my biggest criticisms of this paper is the writing. I realize that English is not the first language of the authors; I am sympathetic and can only imagine what an article I wrote in French would be like. That being said, I would strongly encourage the authors to seek out the help of someone who is a native English speaker or some sort of professional editing service. I am attaching a marked-up version of the manuscript with places where I noted problems with phrasing, word choice, etc, however, it is not an exhaustive list of corrections. The writing/language issue was severe enough that it was difficult to interpret what the authors were trying to communicate at times. One acute example of this is the word "variations" that the authors use frequently. I think in some cases, like when the authors discuss decomposing covariates, the appropriate word would be "deviations" (that would be the standard statistical word choice). In other cases, I think the authors actually mean "variability" when "variations" is used. The word "variations", in my opinion, indicates several different realizations of something (e.g. "variations on a theme"), and I don't think the authors ever intend the word in this manner in this manuscript. Anyway, this is just one example of many from the paper (again, see the marked up PDF).

The literature discussed by the authors is relevant but somewhat limited in scope. Analyses such as the one being presented here have been used for other disease, most recently the spread of Ebola in West Africa where researchers were interested in when Ebola might reach a particular region (e.g Merler et al. 2015, http://dx.doi.org/10.1016/S1473-3099(14)71074-6, or Fang et al. 2016, http://dx.doi.org/10.1073/pnas.1518587113). The authors should discuss their modeling strategy in the broader context of other spatiotemporal modeling strategies that are used for non-influenza diseases (Table 1 covers many influenza models).

Figure 1 is a bit hard to read. I would suggest compressing the x-axis to allow for bigger labels on the axes in order to increase legibility. The y-axis could be expanded. Also, because there are only six data points per regions plotted, it would be better to just show the data points and not box plots (which obscure the actual distribution of the data).

The decomposed variable labels (e.g. "OWV") should be shortened to a single letter or symbol. It would be okay to have something like OWV if it some type of acronym (the authors state it is the "overall global variations"), but even then it would be preferable to use a symbol with some kind of systematic sub/super-scripting.

Along similar lines, way too many of the modeling details are placed in the appendix. It was quite hard to assess the models because of a continuous need to go and look at the appendix. Given that there are no space limitations in PeerJ, the reader should be able to sufficiently assess the modeling strategy by simply reading the body of the manuscript and not need to read the appendix to understand what is being done.

It is mentioned in several places (e.g. line 32, line 81, etc) the authors suggest that they are using a "dynamic modeling" approach. I think this is a bit misleading. Dynamic modeling implies that ODEs/PDEs are being used in the modeling; there really is none of that in the model presented here. Just because disease incidence and movement patterns are being used to make statistical inference doesn't mean that the model is dynamic. As a reader, I was disappointed when there was not more of "dynamic" component to the modeling.
Experimental design: I have some concerns about the modeling that has been done. First and foremost, it is unclear to me why the authors chose not to build a model that included all covariates simultaneously. Rather, they have 4 different models (based separately on temperature, humidity, mobility, and demography). If you want to model the onset of the epidemic, it is better to include all of these factors in a single model and see which factors are significant. I understand that the covariates have different scales, but these can easily be accommodated using appropriate hierarchical modeling strategies (see Gelman & Hill's book on the topic if needed). Along similar lines, I can't figure out why the authors have chosen not to do their (rather routine) statistical analysis using a standard statistical package (R, SAS, Stata, etc). While it is entirely possible that the authors coded thing appropriately in Python it (1) seem like reinventing the wheel and (2) is impossible to tell whether their models are correct without going through all of the rather lengthy model code (which was provided, but seems like a totally unnecessary action given that using a standard package would automatically provide assurance that the model is correct). Furthermore, the authors have chosen to test significance using permutation tests. While this should be okay, it could (again) be done in a standard statistical package but seems inferior to just using the asymptotic estimates that would be provided via, for example, Cox regression. (The authors argue that their data set is small, but it seems like they should have 19 regions * 6 seasons of data regarding epidemic onset times which seems like it would be ample.)

I don't understand why 2 regions of France are excluded from the analysis (Limousin and Languedoc-Roussillon). I doubt that adding the two regions would significantly alter the results, but they should be included if at all possible (or at least reasons for their exclusion should be given).

How were the data for each region summarized? By this I mean, each region has a broad range of temperatures, population densities, humidities, and travel patterns and thus has to be summarized for use in the model. So, for example, when a regional temperature is summarized, is this done using a population density weighted mean? (You wouldn't want temperature from unpopulated areas being included.) In the case of mobility flows, do you take a distance weighted average? These details need to be provided in order to assess the validity of the modeling strategy.

It is unclear if random factors were used. The authors state in some places that random factors were used (e.g. lines 176, 179) and in other places that they were not used (e.g. lines 199, 271). It would seem that random factors should be used for the hierarchical modeling that should be occurring, but it is unclear. The authors need to be consistent in their statements.

The authors talk about "movement of sick individuals" in their mobility analyses (and their model reflects this concept). Sick individuals are likely to have different movement patterns than healthy individuals. For example, if someone is severely ill, they may be confined to a bed for the duration of their infectious period. Hopefully, ill individuals will choose to self-quarantine and not attend work or go to public places. Thus it seems unreasonable to model the onset of epidemic influenza based on movement of sick individuals. Really, one would want to model sub-clinical cases (i.e. individuals who have the disease but are still "healthy"), but there are no data for this. In the end, it probably doesn't matter for the outcome (assuming the subclinical cases = clinical cases * proportion), but it would be good state this assumption and/or change the language related to this issue. If the authors truly want to talk about the movement of sick individuals, the movement patterns should be altered to reflect likely changes in behavior.
Validity of the findings: Given the issues I have outlined with respect to the writing of the manuscript and the modeling that was done, it is unclear to me whether the findings are valid. (Particularly when it seems that "sub-models" were run each covariate without a model that unified all covariates and a "homemade" Python script was used for analyses.) Further clarity on how data were processed prior to use in the analyses is needed to accurately assess validity.
Additional comments: In their paper "Linking influenza epidemic onsets to covariates at different scales using survival analysis models" the authors use several spatially varying factors (temperature, humidity, mobility, and demography) to model when seasonal influenza epidemics start in France. The underlying idea of modeling onset times using a spatiotemporal model could potentially be of interest to public health agencies in France (and perhaps more broadly if others chose to employ the same modeling strategy). I have a number of concerns however regarding the presentation of the work and the modeling that was performed that should be addressed before the work would be publishable 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: LINKING INFLUENZA EPIDEMIC ONSETS TO COVARIATES AT DIFFERENT SCALES USING A DYNAMICAL MODEL
Review round: 3
Reviewer: 1

Output:
Basic reporting: The article meets standards for publication for this criteria.
Experimental design: The model, data, and results remain poorly described:
 - I continue to have major concerns with the ways that the methods are described - it is not clear to me what parameters are being estimated. For example, it is not clear to me what Table 2 is showing.
- In the second term for the equation for phi (line 463 of track-changed manuscript), the sum is taken over an index j which does not appear in the term being summed. This appears to be an error of notation.
- The notation for lambda on line 430 is not consistent with that used on line 619.
- Overlapping points in Figure 2 are not acceptable. At least jitter, or display in a different way.
Validity of the findings: While the revision addressed some of my major concerns from the first round, it raised additional fundamental concerns with the execution and presentation of the models.

 - Bootstrap-based CIs would be a much more standard choice than permutation-based CIs. What is the theoretical justification for using the sampling distribution of the parameters under permutation?
- Paragraph starting on 638 states that non-epidemic years were left out. This is a somewhat justified approach, given that the outcome is only defined for epidemic years, but the limitations this introduces in terms of the interpretability of the results (e.g. results only being relevant for epidemic year dynamics) are substantial, and undiscussed.
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: LINKING INFLUENZA EPIDEMIC ONSETS TO COVARIATES AT DIFFERENT SCALES USING A DYNAMICAL MODEL
Review round: 3
Reviewer: 2

Output:
Basic reporting: The authors have greatly improved the clarity of the manuscript since the previous submission. That being said, in the attached PDF I have suggested numerous changes and potential areas where the manuscript could be shortened. There are some inconsistencies in notation in spots that certainly need to be corrected.
Experimental design: No comment.
Validity of the findings: I have some concerns about the identifiability of the model the authors propose. Given that

lambda = beta * phi ^alpha

and

beta = exp(X*b)

thus

lambda = exp(alpha*log(phi) + X*b)

the parameters end up being present in complex combinations (e.g., alpha and c seem particularly confounded). Therefore, I'm not sure given the current model specification, anyone would ever correctly infer these parameters (given perfect data). This could be why the authors had difficulty with the c parameter.
Additional comments: I appreciate the effort the authors have put into revising their previous submission in accordance with my concerns and those of the other reviewer. Most of my comments in the new version are related to improving clarity and quality of the writing. Other than those, I think the manuscript would be improved by including the results from the analysis with the 5 "missing" epidemics (perhaps as in the supplement). This way readers can evaluate for themselves whether dropping these data was a good choice. My only other substantive comment on this version is that the authors discard the idea of using asymptotic approximations for p-values in favor of permutation tests. See my comments in the attached PDF regarding this issue. The most important of these comments basically is that, if the authors are going to favor permutation tests so heavily, they should include some of the drawbacks of permutation tests (I listed a couple of these in my comments). I think it is also interesting to note that the asymptotic approximations agreed fairly well (in my opinion) with the permutations tests (with only 1 qualitative difference).


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: LINKING INFLUENZA EPIDEMIC ONSETS TO COVARIATES AT DIFFERENT SCALES USING A DYNAMICAL MODEL
Review round: 4
Reviewer: 1

Output:
Basic reporting: No comment.
Experimental design: I continue to have questions about how the model is formulated and don't think that the methods are described with sufficient detail to replicate the analysis. The new text (lines 221-239 in tracked changes document) does not clearly state what the linear mixed model regression uses as an outcome. Furthermore, the distributions of the random effects are not specified. With each iteration, the paper appears to be getting more confusing instead of having a clearer description of the methods.
Validity of the findings: No comment.
Additional comments: No additional comments


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

Input:
Title: RELIABILITY AND CONCURRENT VALIDITY OF THE IPHONE® COMPASS APPLICATION TO MEASURE THORACIC ROTATION RANGE OF MOTION (ROM) IN HEALTHY PARTICIPANTS
Review round: 1
Reviewer: 1

Output:
Basic reporting: No Comment.
Experimental design: No Comment.
Validity of the findings: No Comment.
Additional comments: Overall, the manuscript meets all three of the standards for publication with PeerJ, with only a few minor modifications recommended:

1.	The concurrent validity portion of the experiment would be strengthened if the authors could provide evidence for the validity of the UG for measuring thoracic rotation.  Each of the references provided in the introduction and methods referred specifically to the reliability of the UG.  Is there some gold standard to which the UG has been compared previously for measuring thoracic rotation?  Or, perhaps the UG is the current gold standard?  Without this type of reference it is difficult to interpret the relationship between the two measurement techniques (comparing iPhone app with another technique that itself has not been validated). However, this may not be possible if no previous data exists.  If this is the case, the authors should mention this in their discussion.
2.	In table 2 it appears that SEM was greater for rotations to the right side vs left side for 3 of the 4 combinations of rater/measurement technique.  Can the authors explore whether there are differences in reliability to one side vs the other for any of these combinations, and if so, briefly discuss why this might be the case.  It appears that Rater #1 may have been more consistent toward one side.  However, when measures from both observers are combined it appears that these differences are much smaller (table 3).
3.	The authors could briefly discuss the unique challenges with using the iPhone over an analogue device like the UG.  For example: 1) measurements with an iPhone could be subject to RF noise, 2) an iPhone may not be usable in certain locations (if GPS is required but connection not possible in certain buildings), and 3) one cannot calibrate sensors in the iPhone (they are set at the factory and may lose calibration over time) – an older iPhone may therefore be less accurate.

Minor corrections:
Methods:
Line 122: …sessions “were”
Line 128: …Compass app (Apple…) “were” utilised.
Line 131: Does the app also make use of the phone’s gyroscope?
Lines 138-143: Can the authors define thoracic rotation from an anatomical perspective for a broader scientific audience?  For example, does motion occur exclusively between thoracic vertebrae? Can motion occur between other articulations?
Line 196: …reliability “were” determined…

Discussion:
Lines 267-269: Would the authors therefore speculate that the iPhone app was more accurate?  Perhaps this should be stated?  This might be a good place to address the validity question of the UG (mentioned above).
Line 286: …transverse “plane” joint ROM.
Lines 288-293: Can the app be used with other axes of iPhone rotation?  Perhaps using different axes of the iPhone may influence accuracy?  The authors briefly mention this in lines 339-343.
Lines 316-318: Can the authors re-consider their definition for r2 (coefficient of determination)?  The classic definition is that it describes the amount of variance in one measure that can be explained by the variance in a second measure.
Lines 327-329: Can the authors provide a little more rationale for their decision?  Is there a criterion level of difference that would be acceptable in a clinic?
Line 333: …measuring “t”horacic rotation…

Figures:
All: consider including information about number of subjects/number of measures included in each table/figure (i.e. n=?)
Figure 3 – Consider increasing the font of r2 data and best-fit line equation, and move the equation to the side so that it doesn’t obscure data points.


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: RELIABILITY AND CONCURRENT VALIDITY OF THE IPHONE® COMPASS APPLICATION TO MEASURE THORACIC ROTATION RANGE OF MOTION (ROM) IN HEALTHY PARTICIPANTS
Review round: 1
Reviewer: 2

Output:
Basic reporting: This article is written in clear and unambiguous English.
The introduction is generally good,but it should not be mentionned an "unpublished review". and all the more that there is one which could suit : https://www.hindawi.com/journals/bmri/2015/328142/
The introduction also does not insist on articles that validate the use of internals Smartphone sensors comparing to godl standard in the clinical pratice.

The structure of the article is confomr to acceptable format. Figures and tables are relevant.

Raw data are available but only in SPSS format and with no meta-data explanation. Although it is still possible to convert the data and interpret meta-data, it could be more usefull to get raw data in csv format and with a text document which explain meta-data.

This submission is well 'self-contained'.
Experimental design: Research question is clearly and well defined. Investigation respect the state of art of such research so technical level is good.
Methods are described with sufficient detail and information to replicate, although the writing of certain formulas would make it possible to improve even more this good work.
In "instrumentation part", line 128, it would be nice to clearly define which models of inertial units used in these iPhones.
In the Compass App measurement, line 189, it is not clear if the participant return actively to starting position without help of examiner. The sentence seems ambiguous and should be reformulated for clarity.
Validity of the findings: Novelty could be juged insufficient but the limits of the work are very clearly defined and that is very appreciable. So benefit to literature is clearly state.
The discussion is of a good level and all the limits of the results are discussed clearly and well documented.
Conclusion is well limited to supporting results.
Additional comments: This work is a quality work concerning the reliability and validaty of iPhone app when assessing thoracic spine rotation in healthy individuals. It is rather well documented and very well discussed. The limits being very well defined, I encourage the authors to continue and go further in the validation of this tool.


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: CAPTURING PATIENT-REPORTED AREA OF KNEE PAIN: A CONCURRENT VALIDITY STUDY USING DIGITAL TECHNOLOGY IN PATIENTS WITH PATELLOFEMORAL PAIN
Review round: 1
Reviewer: 1

Output:
Basic reporting: L45: The GRRAS guidelines recommend a description of what is already known about reliability in the introduction. Since this study was not investigating reliability, it would seems appropriate to demonstrate that the paper and digital methods are reliable.
Experimental design: No Comment
Validity of the findings: No Comment
Additional comments: The aim of this study was to determine the validity of digital drawings of pain area compared to paper drawings. This study is very simple and well-designed, and the manuscript is well written. This topic is important since digital drawings might be a more efficient method of collecting this information both clinically and in research.

Specific Comments

L91: Did the order the participants completed the drawings influence the percent difference between the drawings? It would seem that one might become more confident in what they draw the second time around (like a learning effect). Looking at the raw data, it is almost evenly split between which had a greater percent (just subtracting the two values) paper or digital. Could the order have influenced the findings. This likely would be a limitation or something discussed later.

L151-152: Were participant drawing only excluded from the digital drawings? This is what it looks like from the figures but were their paper drawings similar? Could this be a limitation?

L167: Please provide the actual percent difference for the largest and smallest.

L177: This study only compared percent areas; however, this does not assess the location of the pain. I would be appropriate to include a limitation that this study did not investigate validity of the location, which would be clinically important if different.