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: TCF7L2 RS7903146 POLYMORPHISM ASSOCIATION WITH DIABETES AND OBESITY IN AN ELDERLY COHORT FROM BRAZIL
Review round: 1
Reviewer: 3

Output:
Basic reporting: This manuscript describes the association with genetic variation in the TCF7L2 gene and diabetes and obesity in a Brazilian population. This is a relevant study and overall clearly written. However, before this manuscript can be accepted, there are still some concerns to be resolved regarding the rationale of this study as well as the description and interpretation of the results.

•	My biggest concern is that it is not clear what exactly the hypothesis is that is being tested here. Is the question whether the association with TCF7L2 varies per BMI group, or is the question how strong the association is between TCF7L2 and BMI? This needs to be clarified and the manuscript needs to be adjusted accordingly.

•	Table 2 provides an overview of the population characteristics per genotype, but an odds ratio is discussed in the text. I actually expected a table here that would show an effect estimate for the association with T2DM for both genotypes. Perhaps it could be considered to add such a table. This is because the current table feels more like a second Table 1 (this can be transferred to the supplement), instead of the table with research findings. In addition, it is remarkable that only two genotype groups instead of all groups are listed here.

•	In Table 3 the description of the different models is different than in Table 2. For example CC + CT is now called the Dominant model. This is confusing. It would be better to be more consistent throughout the paper.

•	Why is the association with the CC gene and obesity discussed? What is the hypothesis here?

•	It is not entirely clear why the distribution of genotypes in the BMI variation groups is looked at instead of the strength of the association with T2DM. What is the hypothesis here? What is the rationality to look at BMI in subgroups based on BMI? This is not clearly described.

•	Consider rewriting the sentence 242 as this is unclear.
Experimental design: •	From line 188 it is discussed how the groups are formed based on the genotype. It is not entirely clear why these groups were chosen. In addition, the sample of this study is quite small and I would like to see how many individuals there are per group. Why was a continuous model not chosen?

•	The three groups formed here differ substantially from each other in risk factors associated with obesity. This is plausible since the groups are based on this. However, this is not sufficiently highlighted in the section describing Table 1. This should be added.

•	From the results of Table 3 it can be deduced that there is an association between rs7903146 and T2DM in the normal weight group, but not in the overweight groups. This is difficult to understand and looking at the confidence intervals, the groups could be very small. Please add the number of people per group as well as the number of cases and controls to this table.

•	As far as I understand correctly, there is no adjustment for possible confounders. I understand that these are genetic associations, but it is still common to adjust for age and sex (and principal components of the study). Especially since there are differences in these variables between the groups and the strong correlation with the outcome. My advice would be to add a model that is adjusted for age and sex, and a model that is adjusted for all the confounders mentioned in Table 1. This gives a better picture of the association and how it is driven.

•	It is a consideration to add a formal interaction with obesity. I would like to know what the p for interaction for BMI is in the association of rs7903146 and T2DM. Moreover, this will give a greater power than the stratification that is currently used.
Validity of the findings: •	In the discussion it is discussed that an association with T2DM is only found in the group with lower BMI and possible biological mechanisms are discussed. However, the reason for the absence of an association in subjects with a high BMI is not sufficiently discussed. Could it be that BMI is such a strong factor that the genetic aspect is overruled here and BMI is therefore a stronger risk factor for T2DM than genetic variation in the TCF7L2 gene?

•	The discussion speaks of minimizing selection bias because an elderly population has been chosen. However, the normal-weight and obesity group do differ based on age and it could be that there is  survival bias in these analyses. Please elaborate in more detail on this and possibly give a solution for this in the analyses (adjust for age?).
Additional comments: •	This is a multiethnic cohort. Please provide numbers of the different ancestries included in this cohort.

•	There are several minor grammatical errors in the text. When referring to a model it is better to use 'for' instead of 'on'. See for example rule 219 'on the recessive model' could be better written as 'for the recessive model'. Moreover, 'the' is frequently used, although this is not always necessary. See for instance 220 where 'the obesity' can be better written as 'obesity'. These minor grammatical errors are more common in the paper, please check. In the discussion there are more grammatical errors, please reread and rewrite the manuscript where appropriate.


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: TCF7L2 RS7903146 POLYMORPHISM ASSOCIATION WITH DIABETES AND OBESITY IN AN ELDERLY COHORT FROM BRAZIL
Review round: 2
Reviewer: 1

Output:
Basic reporting: The revised manuscript is much clearer.
Experimental design: Methods and experimental design are clear and sufficient.
Validity of the findings: Conclusions were drawn based on the findings.
Additional comments: All of this reviewer’s concerns have been addressed appropriately by the authors.


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: TCF7L2 RS7903146 POLYMORPHISM ASSOCIATION WITH DIABETES AND OBESITY IN AN ELDERLY COHORT FROM BRAZIL
Review round: 2
Reviewer: 2

Output:
Basic reporting: Further language improvement/ editing is required.
Experimental design: The author did not calculate the sample size. Software is available (e.g. g power). They need, at least, to explain why they included 1,023 patients in their study.
Validity of the findings: OK
Additional comments: None


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: TCF7L2 RS7903146 POLYMORPHISM ASSOCIATION WITH DIABETES AND OBESITY IN AN ELDERLY COHORT FROM BRAZIL
Review round: 3
Reviewer: 1

Output:
Basic reporting: The submitted manuscript describes the association of TCF7L2 rs7903146 polymorphism with diabetes and obesity in an elderly cohort from Brazil.
Experimental design: Previous reviewers' comments were addressed, including the calculation of the sample size.
Validity of the findings: Previous reviewers' comments were addressed
Additional comments: Previous reviewers' comments were addressed. No further comments to be added from my side.


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: TAPHONOMY AND TAXONOMY OF A JUVENILE LAMBEOSAURINE (ORNITHISCHIA: HADROSAURIDAE) BONEBED FROM THE LATE CAMPANIAN WAPITI FORMATION OF NORTHWESTERN ALBERTA, CANADA
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript describes a new lambeosaurine bonebed from the Wapiti Formation of northwestern Alberta, Canada. The new report is very important to add new views on the distribution and evolution of the Late Cretaceous hadrosaurids. Therefore, it should definitely be published in PeerJ, once a few issues written below are solved. Please note that I’m not a taphonomy expert that most of my comments are on anatomy sections of the manuscript. I expect another reviewer could cover the taphonomy part.

Given that I’m not a native English speaker, I cannot tell if the language is professional. However, I find repetitions and redundant sentences throughout the manuscript. I commented a few (please check below), but I suggest the authors carefully go over the manuscript once again.

There are several non-relevant literature citings. I found some cases citing papers to support something the original papers did not intend or never mentioned. I commented on the ones I noticed (please check below), but I assume there must be more. I suggest the authors go back to the original papers very carefully once again.

The article structure is fine except that I didn’t see the Conclusions section, which I thought is a standard of PeerJ. Subheadings should be in bold and followed by a period. Tables are not numbered in the order they appear in the main text.

Figures are relevant except for Fig. 8. Please specify in Fig. 8A where Fig. 8B, C, D, and E come from. I also suggest including a whole section, at least as a supplement. Raw data is supplied.
Experimental design: The research is original and primary. The question is well defined. Methods are relevant and described in detail.
Validity of the findings: The taxonomic identification is done without selective reporting in my view. The histology needs some revision (please check below).

All underlying data is provided except that only one histological section is provided. I suggest providing a few more as a supplement to support the microstructure consistency.
Additional comments: General comments for the author
It is great to see a paper reporting a new lambeosaurine bonebed from Alberta. Here are a few line-by-line comments. The reference list is in the end.

55 – Better to add either (or both) Horner et al. (1999) and Horner et al. (2000) if mentioning growth rate. I believe Horner and Currie (1994) didn’t discuss much on growth rate.
150 – Please specify which Figure. Fig. 1?
184 – Please mention how many humeri from which sides were sectioned here. If there are any reasons why those specimens were chosen, please write that here.
240 – The table number does not correspond to the order it appears in the main text. Please re-order.
256-259 – I believe none of the cited papers actually says the feature is ontogenetically variable. Farke et al. (2013) instead mention that this feature is present in various ontogenetic stages. Please add more detail if there is original data that show ontogenetic differences in the extent of the process.
268-274 – Ontogenetic change should be mentioned here. A small Lambeosaurus (e.g., ROM 758) has a similarly angled premaxilla. Additional comparison with Parasaurolophus would also be helpful.
279 –A picture from an anterior view in Fig. 6 would be helpful.
282 – I’m assuming “a large oblate foramen” is equivalent to the “dorsal foramen” of Fig. 6. Please be consistent in terminology.
302 – A picture from a posterior view would be helpful. Features described in the texts should be visible in the figures as much as possible.
305 – Are these the lateral foramina arrowed in Fig. 6? They seem not covered by the ectopterygoid ridge. If not, please specify in the figure, which foramina are mentioned in the text.
313 – Three processes -> Three major processes. Since the authors spend several sentences on the medial process, the medial process can be introduced here instead.
319 – Incomplete sentence.
326 – Doesn’t make sense to me. The medial process must have a sutural surface with the frontal on its dorsal surface to get such inference.
333 – What are the “other taxa” mentioned here? I don’t know much about foramen on the postorbital, but I thought the foramen was more common in hadrosaurines than lambeosaurines. Also, Horner (1992) noted the number of foramina is subject to individual variations but I believe nothing about presence/absence was mentioned.
341 – Please also compare with lambeosaurines, since this paper describes lambeosaurine materials.
343 – Add closing bracket, please.
345 – I’m not understanding “transversely convex dorsal margin”. If you mean that the anterior and the squamosal processes form a wide-angle (rather than straight) in lateral view, that is a typical lambeosaurine feature.
352 – A picture of the whole thin-section and pictures from other sectioned samples as supplementary files would be helpful to confirm the description.
358 – I’m not a histology expert, but I believe “Haversian bone” is not a common word. Secondary osteon or Haversian system may be a better word.
364 – It is self-explanatory. Regions of Haversian reconstruction is another word for rich in secondary osteons. Please reword the sentence.
360 – 366 Everything in this paragraph suggests the sectioned specimens are young. So I suggest rewording the whole paragraph and bring the “…skeletal growth was incomplete at the time of death” to the end of the paragraph.
374 – In the description section, it was not clear enough which characters were used to refer the cranial materials to Lambeosaurinae. This may be due to the frequent use of “typical” or “most”, which sounds like there are exceptions. Adding a table that shows which characters were used to refer which materials may help.
381 – Large juvenile? Also, I prefer the “growth stage” rather than “age class”.
384 – Table 2, not Table 4. Also, the table does not show comparisons with Parasaurolophus.
384 – Which Spring Creek specimens were measured for Table 2? Are these the largest among the same elements? If so, the estimated total length will be 4.52 m or smaller and no minimum can be estimated from the data provided here.
384-387 – “Rapid bone growth” is mentioned here for the first time. The histology section only stated that skeletal growth was incomplete, without any citation. This last sentence seems redundant to me.
449 “mass mortality event” is mentioned here for the first time. I suggest deleting it or moving the whole section later to avoid confusion.
452 –Taxonomy could be narrowed down a little more. The premaxilla is certainly not of Parasaurolophini. The character distributions presented here makes me feel the SCBB lambeosaurine belong to Lambeosaurini.
452 – A table that summarized the sentences starting here would be helpful.
467 – As far as I know, Horner (1992) presents postorbital of Prosaurolophus but no other hadrosaurids, nor provide a comparative description. Also, I don’t know of any paper saying the laterosphenoid fossa shape may vary ontogenetically.
476 – Change hadrosaurid to lambeosaurine, please. Or, please provide comparisons with hadrosaurines, too.
492 – I agree that the SCBB lambeosaurine may represent a new species. Some comparisons with Asian lambeosaurines may support the claim. Recent phylogenetic hypotheses suggest close affinities of Asian taxa to Lambeosaurus (Kobayashi et al., 2019) or Hypacrosaurus (Prieto-Márquez et al., 2019).
515 – I’m not sure if these citations are relevant. This paragraph says the lambeosaurines died by a mass mortality event because the bonebed is monodominant and the bones experience minimal weathering. However, Scherzer & Varricchio (2010) described a bonebed with a larger degree of weathering and Campbell et al. (2019) described a multitaxic bonebed. I didn’t check all of the papers cited, and I’m not a taphonomy expert, but I feel there must be better papers that support the claim.
529 - Henderson (2014) never stated that hadrosaurs could swim. The paper said hadrosaurs could survive for hours to days in a flood. I also don’t think the paper mentioned anything about ontogeny.
568 – “Haversian reconstruction” is, as far as I know, not a common word. “Presence of secondary osteons” is enough.
571-576 – This part is repeating the result section. I’m also not sure why comparing body size with adult lambeosaurines of different taxa is important to discuss in this paper.
580 – Horner et al. (2000) recognized “small” and “large”, not “early” and “late”.
597 – I’m getting confused. The former paragraph stated the SBCC specimens are 1.1 ~ 2.4 years old and now saying they are less than a year old.
602 – According to Chinsamy et al. (2012), the polar Edmontosaurus does not show any LAGs, only vascular patterns.
603 – Please note that the Alaskan Edmontosaurus sp. is larger than the SBCC specimens (~65% adult size), although I agree that it has a large number of growth marks for its size.
608 – My understandings of Woodward et al. (2015) is that the vascular cycling pattern, not LAGs, is a response to seasonal (probably annual) hormonal shifts. Also, I personally think comparing humerus to tibia is not appropriate, since Fig. 8 shows a large medullary region compared to hadrosaurid tibia (e.g., Freedman Fowler & Horner, 2015; Woodward et al., 2015) that may obscure earlier growth marks.
616 – I agree that the use of LAGs for age estimation is not completely reliable, but I know that at least some of the papers cited here are not relevant to support the claim.
618 – This conclusion is a repeat of the second paragraph of this section. I suggest re-writing this whole section (“Growth dynamics of the SCBB lambeosaurines”). There are some redundancies, repetitions, and wrong use of citations. The subheading does not match the contents.
624 – Lack of perinatal material may be explainable by fluvial factors (as discussed in lines 540~).
651 – Yes, feeding height differences can result in a sympatric niche partitioning called browsing stratification (Arsenault & Owen-Smith, 2008; du Toit & Olff, 2014; Kleynhans et al., 2011). So I wonder if hadrosaur age segregation is for resource partitioning, since different body size seems to force different resource use.

References
Arsenault R, and Owen-Smith N. 2008. Resource partitioning by grass height among grazing ungulates does not follow body size relation. Oikos 117:1711-1717.
Campbell JA, Ryan MPJ, and Anderson J. 2019. A taphonomic analysis of a multi-taxic bonebed from the St. Mary River Formation (uppermost Campanian to lowermost Maastrichtian) of Alberta, dominated by cf. Edmontosaurus regalis (Ornithischia: Hadrosauridae), with significant remains of Pachyrhinosaurus canadensis (Ornithischia: Ceratopsidae). Canadian Journal of Earth Sciences.
Chinsamy A, Thomas DB, Tumarkin-Deratzian AR, and Fiorillo AR. 2012. Hadrosaurs were perennial polar residents. The Anatomical Record 295:610-614.
du Toit JT, and Olff H. 2014. Generalities in grazing and browsing ecology: using across-guild comparisons to control contingencies. Oecologia 174:1075-1083.
Farke AA, Chok DJ, Herrero A, Scolieri B, and Werning S. 2013. Ontogeny in the tube-crested dinosaur Parasaurolophus (Hadrosauridae) and heterochrony in hadrosaurids. PeerJ 1:e182.
Freedman Fowler EA, and Horner JR. 2015. A new brachylophosaurin hadrosaur (Dinosauria: Ornithischia) with an intermediate nasal crest from the Campanian Judith River Formation of northcentral Montana. PLoS ONE 10:e0141304.
Henderson DM. 2014. Duck Soup The Floating Fates of Hadrosaurs and Ceratopsians at Dinosaur Provincial Park.  Hadrosaurs: Indiana University Press, 459-466.
Horner JR. 1992. Cranial morphology of Prosaurolophus (Ornithischia: Hadrosauridae) with descriptions of two new hadrosaurid species and an evaluation of hadrosaurid phylogenetic relationships. Museum of the Rockies Occasional Paper 2:1-119.
Horner JR, de Ricqlès A, and Padian K. 1999. Variation in dinosaur skeletochronology indicators: implications for age assessment and physiology. Paleobiology 25:295-304.
Horner JR, De Ricqlès A, and Padian K. 2000. Long bone histology of the hadrosaurid dinosaur Maiasaura peeblesorum: growth dynamics and physiology based on an ontogenetic series of skeletal elements. Journal of Vertebrate Paleontology 20:115-129.
Kleynhans EJ, Jolles AE, Bos MRE, and Olff H. 2011. Resource partitioning along multiple niche dimensions in differently sized African savanna grazers. Oikos 120:591-600.
Kobayashi Y, Nishimura T, Takasaki R, Chiba K, Fiorillo AR, Tanaka K, Chinzorig T, Sato T, and Sakurai K. 2019. A new hadrosaurine (Dinosauria: Hadrosauridae) from the marine deposits of the Late Cretaceous Hakobuchi Formation, Yezo Group, Japan. Sci Rep 9:12389.
Prieto-Márquez A, Wagner JR, and Lehman T. 2019. An unusual ‘shovel-billed’ dinosaur with trophic specializations from the early Campanian of Trans-Pecos Texas, and the ancestral hadrosaurian crest. Journal of Systematic Palaeontology:1-38.
Scherzer BA, and Varricchio DJ. 2010. Taphonomy of a Juvenile Lambeosaurine Bonebed from the Two Medicine Formation (Campanian) of Montana, United States. Palaios 25:780-795.
Woodward HN, Freedman Fowler EA, Farlow JO, and Horner JR. 2015. Maiasaura, a model organism for extinct vertebrate population biology: a large sample statistical assessment of growth dynamics and survivorship. Paleobiology 41:503-527.


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: TAPHONOMY AND TAXONOMY OF A JUVENILE LAMBEOSAURINE (ORNITHISCHIA: HADROSAURIDAE) BONEBED FROM THE LATE CAMPANIAN WAPITI FORMATION OF NORTHWESTERN ALBERTA, CANADA
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper is clear and well-written. The tables and supplementary information provide all necessary data. There are a few references that should be discussed/added to the manuscript, see comments below. There are also a few images that could be added to the figures, see comments below.
Experimental design: Methods are well described and executed. The bonebed and morphologically significant fossils are described with a good amount of detail.
Validity of the findings: Conclusions are well-supported by the data.
Additional comments: This is a well-written, detailed paper describing a lambeosaurine bonebed from the Wapiti Fm of Alberta. The figures are nice and the description of significant, identifiable lambeosaurine material is well done. I only have a few comments/suggestions:

-Figure 4 caption, state that letters correspond to letters in Table 1.

-Lines 278-280: Can you add in a photo of the maxilla in anterior view showing the tooth families? There is space for this in Figure 6.

-Line 319: sentence incomplete.

-Lines 313-350, post-orbital description. Can you comment on the curvature of the squamosal process that forms the dorsal margin of the lateral temporal fenestra? This curvature is more arcuate in some juvenile lambeosaurines (e.g. Kazaklambia, Bell and Brink 2013), and I’m wondering if this shape changes through ontogeny (which might be hard to determine at this point without new measurements). Also is there any evidence of bossing on the p-o, as in Kazaklambia, or a mound where the p-o meets the prefrontral (Brink et al 2011)? These characters could be potentially significant, since the p-o bossing has been described as an autapomorphy for Kazaklambia.

-Line 419: a large percentage of bones have striae (33%), can you add an example of these striae to Figure 10?

-Line 546, the preservation of teeth in jaws. Take a look at the Bramble et al 2017 (page 8) paper regarding the anatomy of the teeth in the jaws. Teeth fall out likely because of the soft tissue that holds the teeth together, not necessarily the thin wall of lingual bone.

-Line 660, the seasonal variation in cohort age structure. It would be worth discussing the results of the Wosik et al. 2020 paper here (and in other parts of the paper), which has an in-depth discussion about juvenile cohorts and size distributions in the Dinosaur Park Formation, as well as aging juvenile specimens based on the Horner et al (2000) Maiasaura scheme.

References

Bell PR, Brink KS. 2013. Kazaklambia convincens comb. nov., a primitive juvenile lambeosaurine from the Santonian of Kazakhstan. Cretaceous Research. 45:265-274.

Bramble K, LeBlanc ARH, Lamoureux DO, Wosik M, Currie PJ. 2017. Histological evidence for a dynamic dental battery in hadrosaurid dinosaurs. Scientific Reports. 7(1):15787.

Brink KS, Zelenitsky DK, Evans DC, Therrien F, Horner JR. 2011. A sub-adult skull of hypacrosaurus stebingeri (ornithischia: Lambeosaurinae): Anatomy and comparison. Historical Biology. 23(1):63-72.

Horner JR, Ricqlés AD, Padian K. 2000. Long bone histology of the hadrosaurid dinosaur Maiasaura peeblesorum: Growth dynamics and physiology based on an ontogenetic series of skeletal elements. Journal of Vertebrate Paleonotology. 20(1):115-129.

Wosik M, Chiba K, Therrien F, Evans DC. 2020. Testing size–frequency distributions as a method of ontogenetic aging: A life-history assessment of hadrosaurid dinosaurs from the dinosaur park formation of Alberta, Canada, with implications for hadrosaurid paleoecology. Paleobiology. 46(3):379-404.


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: TAPHONOMY AND TAXONOMY OF A JUVENILE LAMBEOSAURINE (ORNITHISCHIA: HADROSAURIDAE) BONEBED FROM THE LATE CAMPANIAN WAPITI FORMATION OF NORTHWESTERN ALBERTA, CANADA
Review round: 1
Reviewer: 3

Output:
Basic reporting: Well written & presented. See additional comments below.
Experimental design: Good, although see comment on humerus histology below.
Validity of the findings: Good.
Additional comments: Geological setting, line 158: “(Fig.)” is missing the number.

Methods- Histology:
I disagree with the choice of sectioning humeri rather than tibiae or femora (although I realize it’s obviously too late to change that). If this had been a bonebed of multiple sizes of individuals, and there were size classes represented by humeri but not tibiae or femora, then it might make sense. However, this is a bonebed remarkable for the consistent size of all individuals, so choosing the best bone for accurate histology results would have been preferable over sample size. In hadrosaurs, the tibia is the best to sample because it is a large weight-bearing bone that does not have large processes near the midshaft. In hadrosaurs, the femur has the fourth trochanter near the midshaft, which causes extra remodeling in that area. In the humerus, the large deltopectoral crest causes even more disruption. Sampling the shaft of the humerus requires deviating far from the mid-length of the bone, which means the early growth record will not be present (when the bone was shorter than the location of the slice).

Scanning the excel file of the specimen list, there are 10 femora plus 4 distal femora, and 12 tibiae plus 3 partial tibiae. So, in the manuscript, please explain in more detail why you chose to use the humeri instead of the tibiae and femora, which are the elements typically used in hadrosaur histological analyses.

How many of the 13 humeri were actually sectioned? Specimen H in figure 4 is far too fragmentary for useful histology.

How many histology specimens were processed at UNE vs UA?

Why were no images at all taken from the UNE sections? Even without a top-of-the-line automatic stage system, most universities have at least some sort of microscope camera-to-computer hookup. I’m not asking for the best photos, just some sort of data record.

Methods-Taphonomy-Voorhies groups: Why was “braincase” chosen to list as a single element? This depends on the degree of fusion/maturity of the specimens. Were any associated braincase elements found?

Description-Premaxilla-2nd paragraph: many comparisons are made with other “juveniles”, and ontogenetic changes are mentioned, but you don’t actually say how the bonebed material compares ontogenetically with these other specimens. Are they all the same size/stage? Did you already define how you are using the term “juvenile” here? I suggest the percent-of-adult-size definition of Evans (2010 ZJLS).

Description-Premaxilla-3rd paragraph: Are those crest-snout angles for adult specimens? Does this change ontogenetically? What are the angles in similarly sized juveniles of known species? (In the maxilla section that follows, examples neatly include the species, specimen number, and ontogenetic stage, which is very useful.)

Description-Postorbital-1st paragraph: Last sentence of paragraph isn’t finished.

Taphonomy-1st paragraph: Line 388 says “NSPS” instead of NPSP.

Discussion line 498: change “likely contemporaneous” to “may be contemporaneous”. Also, the correlations in the stratigraphic chart of Fowler 2017 suggest that Unit 3 may be distinctly below the positions of Velafrons and Magnapaulia, leaving the SCBB in a very unique temporal position.

Discussion-Faunal endemism-lines 504-506: Fowler 2017 suggests that P. lakustai’s uniqueness is stratigraphic, not biogeographic.

Needs separately labeled Conclusion paragraph.

Table 2: Which Spring Creek specimens were used? Are these numbers averages of available specimens? How many of each element type (n=)? Also, it is not easily clear that the numbers in parentheses represent the ratio compared to the AMNH specimen.

Figure 9: Part A is only useful if compared against the size distribution within a complete skeleton. Of course there are more small elements (vertebrae, phalanges) than there are large elements (femora, tibiae). Table 3 covers this already; 9A is not needed.

Figure 11A: In caption, first sentence, list regions in same order as they are in figure.

Figure 11B/C: Why do Velafrons and Hypacrosaurus have small letters behind their silhouettes? I don’t see those codes used anywhere.

Figure 11 figure credits: What was the source of the remaining public domain silhouettes? I assumed they would have been from T. Michael Keesey’s website.

Is there are Table Caption for the supp.info. metadata excel file? What do the dorsal/ventral and anterior/posterior columns mean?


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

Input:
Title: A NEW PHYLOGENETIC HYPOTHESIS OF TANYSTROPHEIDAE (DIAPSIDA, ARCHOSAUROMORPHA) AND OTHER “PROTOROSAURS”, AND ITS IMPLICATIONS FOR THE EARLY EVOLUTION OF STEM ARCHOSAURS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript of Spiekman and colleagues provides a detailed and comprehensive revision of the systematics of “protorosaur” archosauromorphs and the phylogenetic relationships of this group. This is a highly welcomed contribution because the phylogenetic relationships of tanystropheids have been poorly explored in recent analyses and several taxa haven’t been included in quantitative analyses or have been included only in the context of morphological disparity analyses. The introduction provides a detailed description of the problematic and the goals of the manuscript, the material and methods are well explained, and the results are described in detailed. The manuscript includes several anatomical figures that are crucial to understand new character formulations or modifications from previous data sets. As a result, I consider that this manuscript should be published after minor modifications.

Finally, I want to congratulate the authors for this well-built and robust phylogenetic analysis.

Yours sincerely,
Martin Ezcurra
Experimental design: The experimental design of the manuscript is clear and well conducted. I have minor comments about it that the authors should address before submitting the revised version of the manuscript (e.g. exclusion of taxa a priori based only on their high amount of missing data, calculation of retention and consistency indices).
Validity of the findings: The findings are well described and discussed. The main conclusion are well supported, but the authors should comment on the non-monophyly of groups based on the most parsimonious trees and not based on the topology of the strict consensus tree.
Additional comments: Before submitting the revised version of the manuscript, the authors should go through the edited version of the manuscript that I provide together with this letter and take a look to the more than 350 comments and modifications that I suggested. In addition, the authors should address the following minor to moderate comments:

-	This sounds like you selected a priori which taxa should be pruned from the final analysis based only on the amount of missing data. Problematic taxa (i.e. OTUs with highly variable placements among MPTs) are a consequence of lack of phylogenetic information for a low-resolution placement. Thus, sometimes with a high amount of missing data (e.g. >95%) have stable phylogenetic positions. So, I strongly recommend to run a first analysis with all the OTUs (as you did) and after that use the iterPCR protocol to detect and prune terminals a posteriori.
On the other hand, if you have evidence to consider OTUs as problematic from a taxonomic point of view or because of problematic interpretations (e.g. Czatkowiella), I agree with their exclusion a priori from the analysis.

-	You should mention that this character seems to be interdependent for your taxonomic sample, but the scorings of characters 20 and 76 in Ezcurra (2016: PeerJ) (and more recent iterations of this matrix) show that it is not the case. For example, rhynchosaurids have extremely short rostra but with a proportionally long nasal when compared with the frontal. You should mention this here in order to prevent future authors to delete character 76 from the data matrix of Ezcurra (2016).

-	Discretization of ratios: it is not clear how you did that. In Ezcurra (2016), I conducted a cluster analysis to find different discretized states. I found this method very handy and useful.

-	Character 17: I find difficult to find the difference between character state 17-0 and 17-1. In Prolacerta, the postnarial process also overlaps the maxilla laterally. Can you explain better and figure more clearly the difference between both character states.

-	Character 23: it is very difficult to observe the presence of the fossa in the photograph of Dinocephalosaurus orientalis. Can you provide a drawing or a clearer photograph of that feature?

-	I have a query about the calculation of the consistency and retention indices. If you have used the script STATS.RUN of TNT, this code calculates the values including all the terminals included in the dataset, without excluding the terminals excluded a priori before the analysis. You have excluded taxa a priori in some of your analyses, so, if it is the case, I strongly suggest you to use a script that I have modified that excludes these terminals also from the calculation of the indices. You can email me asking for this script, I think that my identity is quite clear.

-	Page 116: you are providing a definition for an unnamed clade. Why? I agree to keep this clade unnamed until further work in done on this clade and the presence of non-tanystropheid taxa more closely related to tanystropheids than to other archosauromorphs is robustly supported.

-	Page 118: why are you providing a new phylogenetic definition of Tanystropheidae. I consider that it is not necessary because the definition of Dilkes (1998: ZJLS) is well built. In addition, you are providing here a stem-based definition contrasting with the original spirit of the node-based definition of Dilkes (1998).

-	Page 121: Unambiguous synapomorphies of Allokotosauria. The presence of three apomorphic character states related to the large palatal teeth of the vomer, palatine and pterygoid, respectively, sounds that they are interdependent for this part of the tree. You showed convincingly that in tanystropheids the presence of large vomerine teeth does not co-occur with the presence of large teeth in the palatine and pterygoid. So, I suggest to merge these three characters into two characters. One describing the presence/absence of large palatal teeth (as I did in 2016) and the other describing the distribution of such teeth across the palate (e.g. only in vomer, in palatine and pterygoid).

-	End of text: I strongly suggest the authors to include some paragraphs in the Conclusion or as a separate section discussing where research efforts should be focused to improve tanystropheid taxonomy and phylogenetic relationships. I think that it is important for future workers and at the moment you are the most skilled people to provide such statements.

-	The authors should provide in the supplementary files (NEXUS and TNT files) the code for character ordination. It is more time consuming to write the line for character ordination than to deactivate character ordination with a couple of clicks or a single command in TNT.


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

Input:
Title: A NEW PHYLOGENETIC HYPOTHESIS OF TANYSTROPHEIDAE (DIAPSIDA, ARCHOSAUROMORPHA) AND OTHER “PROTOROSAURS”, AND ITS IMPLICATIONS FOR THE EARLY EVOLUTION OF STEM ARCHOSAURS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Although early archosauromorphs historically known as the “Protorosauria” or “prolacertiforms” have been subject to several previous phylogenetic studies, the relationships of many taxa remained elusive, as former assessments suffered from low OTU representativeness or were especifically designed to resolve the phylogeny of more crownward clades. As such, the work of Spiekman et al. is most welcome, as it represents the state-of-the-art knowledge on early archosauromorph phylogeny, providing a new comprehensive dataset that icludes most taxa that were once considered as ‘Protorosauria’ or related to them. The manuscript is written in professional English, and I was only able to detect minor mistakes in this regard (but I’m not a native English speaker myself). A complete, fully referenced, background on early archosauromorph relationships is provided, and the MS is accompanied by high-quality images illustrating new morphological characters. The raw data is provided as nexus file, what will help future workers on this particular subject.
Experimental design: Spiekman et al. assembled a new datast based on characters from previous works and several new ones. Many old characters were modified to better fit a broad non-archosauriform sample, whereas others were merged or standardized following relevant criteria. This improved the quality of raw data, contributing to the reliabity of the outcomes. The experimental design and methodologies are robust and were sufficiently described.
Validity of the findings: Spiekman et al. present several trees, resulting from different phylogenetic parameters. More conservative hypotheses (analyses 3 and 4) are well-resolved and represent sound interpretations of early archosauromorph relationships. The main conclusions are derived strictly from the methodology empoyed and obtained results. The phylogenetic hypothesis sustained by the authors is useful in clarifying the relationships of several taxa, and the monophyly of important clades (such as the Tanystropheidae) is accessed with grater confidence than in previous literature. Some apparently aberrant results (such as the position of Prolacerta) could be better discussed by the authors, as it strongly disagrees with recently published hypotheses.
Additional comments: I have several minor issues, all of them are detailed in the attached pdf file. I would especially advise the authors to tone down their suggestion to abandon "Protorosauria". Not because they are wrong in their claim, but because this was already well-estabilished by several previous workers, whereas the authors sometimes seem to suggest that this is a direct outcome of their study (e.g. p. 123, lines 3393-3395).

Please pay special attention to the annotated pdf file I provide. All my concerns are highlighted in it!

Congratulations for the excellent work.


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: INTACT TACTILE ANISOTROPY DESPITE ALTERED HAND PERCEPTION IN COMPLEX REGIONAL PAIN SYNDROME: RETHINKING THE ROLE OF THE PRIMARY SENSORY CORTEX IN TACTILE AND PERCEPTUAL DYSFUNCTION
Review round: 1
Reviewer: 1

Output:
Basic reporting: My main comments concern the terminology, which appears to be used somewhat inconsistently and in a confusing fashion, making it sometimes hard to follow the narrative of the paper. Table 1 very helpful in this regard, but seems to contradict some statements made in the paper. Specifically, ‘tactile sensitivity’ can be used generally, but in most cases refers to neural or perceptual thresholds regarding stimulation amplitude, at least in the psychophysical or neuroscientific literature that I am familiar with. ‘Tactile spatial acuity’ generally refers to tasks establishing the spatial resolution of the skin, such as two-points or grating orientation discrimination. I have not encountered the use of ‘tactile spatial acuity’ for tactile distance tasks.

Similarly, the paper seems to (correctly) suggest that tactile spatial acuity tasks using two-point discrimination paradigms can potentially be mastered using non-spatial cues. Tactile distance tasks are presented as a spatial alternative. I do not agree with this representation. Better versions of these tasks are grating orientation tasks, which also measure the same underlying variable, the tactile spatial resolution, however without non-spatial cues as confounds. Tactile distance judgements are inherently different tasks. They require an underlying spatial representation of the body from which tactile distances can be computed. Tasks that purely test spatial resolution on the other hand do not require such a representation. I apologize if I have misinterpreted the authors’ statements; this is how I interpreted the introduction. Nevertheless, I agree with the use of a tactile distance task as appropriate for this study.

Regarding the involvement of primary somatosensory cortex in tactile distance judgements, the authors might be interested in a recent preprint that contains new data on this question:
Tamè L, Tucciarelli R, Sadibolova R, Sereno MI, Longo MR. Reconstructing neural representations of tactile space. bioRxiv. 2019. doi:10.1101/679241
Experimental design: The experimental design is appropriate and well explained. Minor point: Perhaps ‘measure’ would be a better name for the four different ‘models’ introduced in the methods/results?
Validity of the findings: The paper fills an important gap in the literature and the results are intriguing. I agree very much with the authors’ statement that performance across groups needs to be tested across a multitude of perceptual assessments for a clear picture to emerge on the specific tactile processing changes in CRPS.
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: INTACT TACTILE ANISOTROPY DESPITE ALTERED HAND PERCEPTION IN COMPLEX REGIONAL PAIN SYNDROME: RETHINKING THE ROLE OF THE PRIMARY SENSORY CORTEX IN TACTILE AND PERCEPTUAL DYSFUNCTION
Review round: 1
Reviewer: 2

Output:
Basic reporting: See below
Experimental design: See below
Validity of the findings: See below
Additional comments: This paper, “Intact spatial acuity despite altered hand perception in complex regional pain syndrome: rethinking the role of the primary sensory cortex in tactile and perceptual dysfunction”, by Reinersmann and colleagues reports a study investigating tactile distance anisotropy in complex regional pain syndrome (CRPS). Patients with CRPS were compared to controls both with and without pain. Consistent with previous results, the authors report an anisotropy in tactile distance perception, with distances oriented across the width of the hand dorsum perceived as larger than those oriented along the length of the hand. No differences between groups were observed, however.

This study tests an interesting hypothesis about CRPS and appears to have been well conducted. Though no group differences are found, this null result is nevertheless notable and certainly worth documenting in the literature. I therefore believe that these data should be published. I do however have some comments and suggestions which I hope the authors find helpful in revising this paper.

My biggest comment is that the analyses are confusing and convoluted. While the experimental design seems to have been modelled closely on that used by Longo & Haggard (2011; JEP:HPP), the analysis is completely different, for no apparent reason that I could tell. Four separate “Models” of the data are presented, in addition to curve fitting. But I can’t see anything that these models add to just looking at the PSE and slope of the psychometric function. And Model 4 I couldn’t follow at all. Further, while it is claimed that there was significant anisotropy on both hands in all 3 groups, no actual statistical tests of this are reported.

As I wrote above, I think the only analysis needed is the curve-fitting one, but this is poorly described. No information is given about what kind of curve was fit, with what criteria of goodness-of-fit, how good the fit actually was, or which software was used. While the PSEs from these curves are presented in Figure 4, I can’t understand what is actually being plotted. Is the PSE the ratio between the across and along stimuli? If so, there does not in fact seem to be evidence for anisotropy. But I’m not sure that’s what these data are. It’s also unclear what the error bars depict (e.g., SEM, 95% CI, etc). Further, this seems to be an inappropriate use of a bar graph, since the y-axis is truncated at a seemingly random place (0.6).

Second, I can’t follow the logic of the power analysis (lines 113-118). This is based on an effect size of 0.2, but the authors don’t indicate which effect size measure this is supposed to be (e.g., Cohen’s d, partial eta-square, etc). Further, the analysis used is justified by “the repeated measures design”, but the whole point is to compare different groups of people, which obviously isn’t repeated measures. It isn’t clear which key statistical test this power analysis was based on, nor which software was used. I find it very difficult to see how 15 subjects per group can give 80% power for detecting any plausible smallest theoretically-meaningful effect size. I am sympathetic to the difficulty in finding patients, so do not think that the sample size should be a barrier to publication. But this power analysis is unconvincing and underspecified.

For the template matching task, I can’t understand how hand size was quantified. The “unmodified” hand image is a photo of somebody else’s hand, and not of the subject’s own. Further, subjects will differ from each other in terms of their actual hand size. So what are the statistical tests comparing?

Other points:
1.	In the title, and elsewhere, the authors refer to their task as a measure of “tactile acuity”. While the slope of the psychometric function in a distance discrimination task could be considered a measure of acuity, for the most part what the authors are measuring here is BIAS, not acuity.
2.	Line 16: It’s odd to say that the task “incorporates anisotropy”. The task measures anisotropy.
3.	Line 18: It’s not correct that participants “judged the equivalence of tactile distances”. They in fact judged which one felt bigger.
4.	Line 65: “Knight Fle et al” should be “Le Cornu Knight et al”.
5.	Line 71: I don’t think it’s correct that Weber found that tactile distances across the limb are perceived as larger than those along the limb. He reported that tactile distances felt bigger on more sensitive skin surfaces and (separately) that 2-point discrimination thresholds were smaller across than along the limbs. But I don’t think he combined those two observations. I think that Green (1982, Perception & Psychophysics) is a better reference here than Weber.
6.	Line 135: It would be good to add a citation or two for the template matching method used.
7.	Line 163: It’s not true that there are only three possible distance combinations with this stimulus set. 4/3 is also possible.
8.	Line 170-172: Do these authors really claim that tactile anisotropy is better measure of “S1 morphology” than acuity measures?
9.	Line 175: What are the “further studies” referred to here?
10.	Line 181: Did the subject judge whether the across or the along stimulus felt bigger? Or whether the first or the second stimulus felt bigger?
11.	Line 187: There were 10 repetitions of each stimulus pair. But given that the stimuli were presented sequentially, was the order also counterbalanced?
12.	For all the statistical analyses, appropriate measures of effect size would be a nice addition.


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: INTACT TACTILE ANISOTROPY DESPITE ALTERED HAND PERCEPTION IN COMPLEX REGIONAL PAIN SYNDROME: RETHINKING THE ROLE OF THE PRIMARY SENSORY CORTEX IN TACTILE AND PERCEPTUAL DYSFUNCTION
Review round: 2
Reviewer: 1

Output:
Basic reporting: All my concerns have been addressed.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: All my concerns have been addressed.


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: INTACT TACTILE ANISOTROPY DESPITE ALTERED HAND PERCEPTION IN COMPLEX REGIONAL PAIN SYNDROME: RETHINKING THE ROLE OF THE PRIMARY SENSORY CORTEX IN TACTILE AND PERCEPTUAL DYSFUNCTION
Review round: 2
Reviewer: 2

Output:
Basic reporting: See below
Experimental design: See below
Validity of the findings: See below
Additional comments: The authors have satisfactorily addressed the points I raised in my previous review. I support publication of the paper in its current form.


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: COVERAGE AND QUALITY OF DNA BARCODE REFERENCES FOR CENTRAL AND NORTHERN EUROPEAN ODONATA
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript is clearly written and appears to adhere to PeerJ policies.
Experimental design: The rationale and objectives of the study are clearly described and the Material and Methods section is well structured but more details should be included.
Validity of the findings: The Discussion section is critical and comprehensive, but the Conclusion section is long and extensive.
Additional comments: The authors present an interesting manuscript about the capacity to use DNA barcoding to identify dragonflies and damselflies (Insecta: Odonata) in Central and Northern Europe. The strength of this study is in the use and acquisition of genetic information from odonates of this region.

The manuscript has a good introduction despite small errors (e.g. Line 65 and 69). The methodology is clear, however, I think more detail would assist with the methods section. It is also necessary to identify the authors’ of the species description for practically all species. I suggest to move part of the last paragraph from Result section (L 337-343) to the Material and Methods section. Tables and figures are good, but it is necessary some adjustments. The discussion section is critical and comprehensive; and the references are appropriate in number and up-to-date.

Considering the above-mentioned issues, it is an important study, especially because of its originality, and should be considered for publication in PeerJ once the corrections and modifications have been carried out properly.

Point-to-point revision

Line 65. Please, add some reference here or update this value.
Line 69. Please, add some reference here.
Line 81. See Kalkman, V.J., Boudot, J., Bernard, R. et al. Diversity and conservation of European dragonflies and damselflies (Odonata). Hydrobiologia 811, 269–282 (2018). https://doi.org/10.1007/s10750-017-3495-6
Line 102. Update the information about it – “June 12th, 2019”
Line 203. Get the DOI number before the manuscript has been accepted. Also, you must show the GenBank number for each sequence in Suppl. File 1.
Line 303. What are you so sure about the misidentifications of specimens?
Lines 337-343. Move to the Methods section.
Line 339. Koroiva & Kvist, 2018
Line 516. See Blow et al.2020 (https://doi.org/10.1101/2020.06.06.137828)
Line 561. The conclusion section is long and extensive. Try to summarize this in a few sentences.
Line 843. Advances in Ecological Research, Volume 58, 2018, Pages 63-99
Figures 4 and 5. Please, remove “1a”, “1b”, “Plate IX”, etc. In addition, there is no prior information in the text about “ML-based estimation using model MKY+F+I” or “TIM2+F+G4”. Add this information to the Material and Methods section.
Tables 1 and 2. “* as of 2020-05-18 in BOLD including all records ….” – Explain this information in the Material and Methods section.
Supp. File 1. Please standardize the terms "Imago", "Adult", "A", "a", "I", "larva", etc.
Supp. Files 1 and 2 and References. The scientific names of species are italicized.


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: COVERAGE AND QUALITY OF DNA BARCODE REFERENCES FOR CENTRAL AND NORTHERN EUROPEAN ODONATA
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript is well written, the authors use clear langage throughout the text.
The introduction and background provided by the authors is complete and well referenced. However, some parts of the dicussion could be rewritten or even removed, making the whole section a bit shorter and easier to read. For example, the authors provide some background on Red List assesmentsand conservation issues for odonates. While this information is indeed interesting, I do not see the point of including it here, as the authors do not dicuss any of these points later on. I suggest the authors should delete for example the paragraph on conservation (lines 82-86).
Lines 100-102: I suggest to expand a bit more on this background info (e.g. by providing absolute numbers, or details on particular species that are missing from the BOLD database and that are relevant), as it provides the authors the starting point for their work, and hence they need to clearly state how their work contributes to fill this knowledge gap.
Line 108: the authors mention that «A wider geographic coverage is lacking..» Wider as compared to what? Perhaps they should briefly state the current gepgraphical coverage for odonates in the databases.
Line 145: The authors may provide the readers with references to cryptic odonate species that have been described, for example;
Mitchell A, Samways MJ (2005) The morphological ‘forms’ of Palpopleura lucia (Drury) are separate species as evidenced by DNA sequencing (Anisoptera : Libellulidae). Odonatologica, 34, 173– 178.
Damm S, Schierwater B, Hadrys H (2010) An integrative approach to species discovery: from character‐based DNA barcoding to ecology. Molecular Ecology, 19, 3881– 3893.
Vega-Sanchez et al (2020) Hetaerina calverti (Odonata: Zygoptera: Calopterygidae) sp. nov., a new cryptic species of the American Rubyspot complex Zootaxa 4766 (3)
Overall, I think that the whole introduction section would benefit from a slight re-focus on a few main points, such as the following:
1. Background on odonates as important in monitoring freshwater ecosystems.
2. A good coverage of odonate species in the BOLD database DOES EXIST, BUT THERE IS A GAP IN (and here state that there are severa instances of species represented by a single individual, and also several species (and why are these relevant?) missing from the database).
3. What did the authors do to fill these gaps?
FIGURES AND TABLES:
Figure 1 could be changed slightly by colouring the circles (besides the differences in size), as in some cases it is not easy to distinguish their sizes.
In Figures 2 and 3, please indicate in the legend which are the clades in which you identified BIN discordances. I understand that these appear in blue in both cases, but still this should be indicated in the figure legends.
There are some instances of references cited in the main text which do not appear in the reference list(or they do but the publication years do not match):
Line 66 – Kalkman et al. 2008
Line 93 – Leese et al 2018
Line 141 – Schlick-Steiner et al. 2014
Line 148 – Macher et al. 2016
Line 397 – Hawlitschek et al. 2016
OTHER MINOR COMMENTS:
Line 56 – Cordulia aenea should be in italics.
Line 530 – Please correct Cordero-Rivera, also in the reference list.
Experimental design: The authors should state in a more clear way how their study fills a knowledge gap (see my previous comments). It would be good that the authors explained the reason why different primer combinations and/or DNA extraction protocols are used. I know that this might be due to simple logistical reasons (each laboratory has usually standarized work procedures) but still it would be good to clarify this.
The methodology regarding the laboratory methods used to obtain the barcode sequences is not explained in a clear way. I acknowledge it is difficult to put together different methods used in different institutions/laboratories; however this particular section of the manuscript as it is written now, makes it a bit difficult for the reader to follow the description and hence to clearly understand the methodology used by the authors. For example:
In lines 162-167, the authors enumerate the different institutions that collaborated with the study by providing specimens for DNA extraction. Would be good that they clarify what do the acronyms used stand for (e.g. SNSB-ZSM, NHMW or ZFMK).
Line 164, the authors mention here the University of Lodz in Poland; however, later on (line 208) they refer to the DNAqua-Net from Poland. Please clarify this.
Line 186, «Most studied specimens were adults (see below) of which the majority were stored in >96%» What about the others? Where they dry-preserved specimens? Were they preserved in different ethanol concentration? Please clarify.
Lines 207-248, It is not really clear where the procedures (DNA extraction, PCR and sequencing) were carried out for each of the samples contributed by each country/institution involved. For example, in this section the authors mention the CCDB as a place where some samples were sequenced, but then in the results section (line 277) they mention GBOL (?). The authors should add some statement at the beginigng of this section in which they explain where all the samples from the contributing institutions mentioned previously (lines 162-167) were processed.
There is no mention to the starting tissue for DNA extraction. Was it legs? Thoracic muscle?
Line 220, why does the CCDB uses a different primer set to amplify the samples from DNA DNAqua-Net from Poland?
Line 224, where were samples from ZFMK processed? Was it also at CCDB?
Line 226, what does KFUG stands for? This is mentioned for the first time here.
Line 231, is the NHMW located at the University of Graz, or these are two different insititutions from Austria?
Lines 234-236, Reference for primers is missing.
Lines 237-238, Reference for primers is missing.
Lines 245-246, Reference for primers is missing.
Overall, this whole section (Laboratory Methods) needs to be written in a more clear and concise way. For the sake of clarity and readability, perhaps the authors should consider providing detailed primer information in a separate table, including the institution/laboratory that used each primer pairs, annealing temperature, and original references for the primer pairs; and/or any other information that might be useful for replication of the experiments.
Results section, line 280, perhaps the authors could further explain the reason for those 3 individuals not being assigned to a BIN. Was it because of low-quality sequence data? Presence of nuclear copies? Contamination issues?
Validity of the findings: The discussion section is far too long. Also, the conclusions that the authors make regarding those instances of BIN discordance or BIN sharing go in my oppinion far beyond to what is supported by their results. While I acknowledge that some speculation and hypothesis delineating is needed in a manuscript discussion, I think that in this particular case there are instances in which the authors make conclusions that go far beyond the resolution power of the data available to them (only one nuclear marker), which also makes the reading of this section a bit difficult. I suggest that the authors should cut out this section, focusing on their main findings, discuss briefly potential explanations for their results and mention future avenues of research, which are basically the same for all examples presented: Increase the geographical/specimen sampling, and increase the number and type of markers used (nuclear and mitochondrial). I detail below some specific issues:
Lines 346-355, I think this paragraph is more suited to be provided as background. The Discussion section should open by stating the main findings of the work (perhaps something like current lines 371-376).
Lines 409-410, perhaps the authors could also mention somwhere in the discussion that COI might not be the best mitochondrial marker for resolving species-level relationships? (see e.g. Chen et al (2018) Systematic Entomology; DOI: 10.1111/syen.1229 or De Mandal et al (2014) DNA Barcodes; DOI: 10.2478/dna-2014-0001)
Lines 413-414, This statement seems to be repetitive as it says basically the same as lines 400-401.
The text from lines 422 to 559 needs to be shortened, focusing only on discussing the results in light of the current data available - I feel there is a bit too much speculation in some cases. Also, the authors should present their arguments and also the background they provide on the differens species in question, in a more clear, ordered way.
As a note for potential explanations regarding haplotype sharing between different species, the authors should also consider the possible presence of maternally inherited endosymbionts. There has been recent progress in screening odonates for endosymbionts such as Wolbachia or Rickettsia. I think this might be relevant here, as for example in the case of Coenagrion, Thongprem et al have found that some species of this genus from the UK are infected with Rickettsia.The authors should mention this as a potential explanation for some of their findings, along with the ones that they already provide:
Thongprem et al 2020 Incidence and Diversity of Torix Rickettsia–Odonata Symbioses Microbial Ecology https://doi.org/10.1007/s00248-020-01568-9
Lorenzo-Carballa et al 2019 Widespread Wolbachia infection in an insular radiation of damselflies (Odonata, Coenagrionidae) Scientific Reports https://doi.org/10.1038/s41598-019-47954-3
Salunkhe, R. C. et al. Distribution and molecular characterization of Wolbachia endosymbionts in Odonata (Insecta) from Central India by multigene approach. Current Science. 108(5), 971–978 (2015).
Lines 450-451, the argument on hybridization between Anax species sounds a bit too speculative. I suggest removing lines 450-457 and focus only on what you can argue with your data (currently lines 457-464).
Lines 492-497, too speculative. I suggest removing this bit.
Lines 541, The authors need to be careful to the arguments they provide. For example when mentioning «Interestingly, though, this second C. aenea clade groups with COI data of C. amurensis from Japan (Fig. 5)», they should be aware that they only have one sequence of C. amurensis available, and that the whole picture could change if they sequenced more individuals. Again, the authors need to remove any speculative sentence/paragraph. The same goes for the closing argument of this section «Our finding that the barcodes of some European C. aenea cluster with C. amurensis, suggests introgression of C. amurensis into C. aenea and a rapid spread of this foreign haplotype across large parts of the species’ distribution range».
Additional comments: This manuscript by Geiger et al reports the results of a barcode analysis of nearly all European Odonate species. The aim of this work was to fill the gap that currently exists in the BOLD database, in which, despite having covered nearly all European dragonflies(Weigand et al 2019); several instances exist of odonate species that are represented by a single individual in the BOLD database, and even some species missing from this database.
To fill these gaps, Geiger et al compiled an extensive dataset of nearly 700 specimens of odonates (including adults and larvae), which were sequenced for the COI barcode fragment. The authors examined their dataset using the BOLD database and metrics included there, and perfomed also ML analysis.
They found that nearly 90% of the species included in the study could be readily identified by using the COI barcoding sequence. Interestingly, they found instances of shared barcodes between morpholgically distinct species, as well as deep divergence among representatives of the same morphological species. The authors discuss their results, focusing on the need for more in depth analyses of these discordances.
This work makes a good contribution to the barcode database for European odonates, which is a crucial and neccesary step prior to the use of DNA-based identification tools (as the authors clearly state throughout their manuscript); and as such, I think that the article deserves publication in PeerJ. However, there are some issues related to the methodology description, as well as to the conclusions that the authors make in light of their results; which need to be dealt with prior to manuscript acceptance.
I have tried to address some of these issues, and attach also a copy of the manuscript main document with several other minor comments. I do hope that my review helps to improve this manuscript, and I look forward to receive a new version of the manuscript for reviewing and, eventually, publication in PeerJ.


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

Input:
Title: COVERAGE AND QUALITY OF DNA BARCODE REFERENCES FOR CENTRAL AND NORTHERN EUROPEAN ODONATA
Review round: 1
Reviewer: 3

Output:
Basic reporting: The article is on the whole clear and well written. There are a small number of ambiguous statements, likely due to English not being a first language and these should be corrected, e.g. lines 68 ("...people affectionate by nature" - the meaning intended is surely people who like nature. Perhaps "natural historians"?).

A detailed background is presented and the work is well referenced, well structured, and provided with appropriate figures and tables.
Experimental design: No comment.
Validity of the findings: The underlying data has been provided, although it would be beneficial to provide a DOI for the dataset on BOLD. Conclusions are concisely stated and do not overreach the results.

For Figs. 2 and 3, the notation in parentheses after species names (e.g. (NO 4, DE 6, PL 7) should be explained in the legend to each figure.

Some enigmatic results in Table 2 (e.g. BIN BOLD:AAA2218 contains approx. 15 species of Enallagma) should be discussed in the text. At the very least there should be a comment in the appropriate column of Table 2 for this BIN.
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: COVERAGE AND QUALITY OF DNA BARCODE REFERENCES FOR CENTRAL AND NORTHERN EUROPEAN ODONATA
Review round: 2
Reviewer: 1

Output:
Basic reporting: I am happy to see the revised version of the manuscript by Geiger et al on Odonata barcoding, in whiche the authors have addressed all the concerns by the reviewers. This new version of the manuscript has greatly improved compared to the previous one, and I believe it is now ready for publication in PeerJ.
Experimental design: The methods are now clearer and written in a way less prone to confussion for the readers, the reading of the whole mats &  methods section is now much easier.
Validity of the findings: no comment
Additional comments: I am really happy to see this manuscript in its current form, and it will be great to see it published soon 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: MOLECULAR EVIDENCE FOR CROSS BOUNDARY SPREAD OF SALMONELLA SPP. IN MEAT SOLD AT RETAIL MARKETS IN THE MIDDLE MEKONG BASIN AREA
Review round: 1
Reviewer: 1

Output:
Basic reporting: The authors need to improve on their sentencing so as not to make them ambiguous. Their writing style should be such that will enable readers understand what they mean and the information they are conveying. I have tried to indicate the areas in the manuscript.
Experimental design: The design is okay, however they need to give details of some of the methods they used in the study. I must commend them, its a good work. Their study was in-depth enough.
Validity of the findings: The findings are meaningful, however Table 1 may require a little more statistical.
The data will be more explanatory if they could assign superscripts to each of the values. This will help one to see the values that are significantly different at a glance. Also indicate whether the statistical comparison is along column or row.
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: MOLECULAR EVIDENCE FOR CROSS BOUNDARY SPREAD OF SALMONELLA SPP. IN MEAT SOLD AT RETAIL MARKETS IN THE MIDDLE MEKONG BASIN AREA
Review round: 1
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: In this work, the authors focused their attention on the Salmonella contamination in livestock products that are very common in some areas of the world and specifically in the characteristics  markets of the West Asia.
 The manuscript is well written.
The paper is supported by relevant experimental data, the presentation is clear and most of the conclusions are justified.
I recommend it for publication in this journal.


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

Input:
Title: MOLECULAR EVIDENCE FOR CROSS BOUNDARY SPREAD OF SALMONELLA SPP. IN MEAT SOLD AT RETAIL MARKETS IN THE MIDDLE MEKONG BASIN AREA
Review round: 1
Reviewer: 3

Output:
Basic reporting: The authors have conducted an important study on Salmonella spp. which causes salmonellosis in human.
The manuscript is clear but requires attention for English used. I have worked through the introduction but requires improvement in other parts.
Literature references, sufficient field background/context have been provided.
Structure of the article is correct. Improvements in tables and figures are required. Table 3 requires attention and figure 2 could be more illustrative (than descriptive) and colourful for establishing useful knowledge from it.

Besides language, the major concerns are lack of illustrations (figures) in the manuscript.
Additionally, since the sequencing data of the strains is available, an analysis of sequence comparison is highly recommended to increase the impact of the study.
Circos plots for comparison of various genes, gene annotations, intron-exon annotations of genes, and protein models and homology modelling are few examples of the study that could be included bases on sequence data available with the authors.

Detailed comments are attached as pdf.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: Refer to comments in part 1.


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: MOLECULAR EVIDENCE FOR CROSS BOUNDARY SPREAD OF SALMONELLA SPP. IN MEAT SOLD AT RETAIL MARKETS IN THE MIDDLE MEKONG BASIN AREA
Review round: 1
Reviewer: 4

Output:
Basic reporting: Manuscript submitted by Menusene et al., intend to investigate the prevalence of Salmonella species in meat sold at retail markets in the middle Mekong basin area. Authors have utilized Multi-locus sequence typing to genotype several Salmonella serotypes isolated from 370 Meat samples during January to May 2019 from five retail markets in Vientiane Capital, Lao PDR and six retail markets in Nong Khai Province, Thailand.

Comments:
 1)  Title of manuscript is ambiguous and confusing. Authors should consider rephrasing the title based on findings in the manuscript.

2) Authors have mentioned that " Rates of 65%, 73% and 82% were chosen to calculate the sample sizes for pork, chicken and beef, respectively". Authors should elaborate how they defined "expected prevalence" and calculated sample size for this study.

3) Manuscript suffers a lot from grammatical errors and spelling mistakes. Authors should get the manuscript proofread by a native speaker to ensure that an international audience can clearly understand the text and findings.

4)  Throughout the manuscript, authors missed to italicize the species name. For example, Line 39/ 40:  S.London,  S. Corvallis, S.Rissen.   Scientific name of the species is always italicized without exception.
Experimental design: Question addressed by authors in the study is well defined and relevant. Antimicrobial resistance is a pertinent problem and addressing Salmonella resistance in livestock meats   around Thai-Lao friendship bridge highlights importance of stringent food safety regulation and implementation of standard hygiene protocol in pre-retail meat industry.

Comments:

1) Authors mentioned in line 147 that " an association between a Salmonella positive proportion and the relevant specifications were determined by descriptive statistical analysis" what kind of statistical analysis they are referring here ?

2) What were the Primers, PCR conditions used for multilocus sequence typing? Authors should provide sufficient details in methods section so that findings can be replicated and reproduced.
Validity of the findings: 1) Underlying data have been provided with proper control.

2) Conclusions are well stated and linked to original research question addressed.
Additional comments: Manuscript submitted by Menusene et al., intend to investigate the prevalence of Salmonella species in meat sold at retail markets in the middle Mekong basin area. Authors have utilized Multi-locus sequence typing to genotype several Salmonella serotypes isolated from 370 Meat samples during January to May 2019 from five retail markets in Vientiane Capital, Lao PDR and six retail markets in Nong Khai Province, Thailand.  Question addressed by authors in the study is well defined and relevant. Antimicrobial resistance is a pertinent problem and addressing Salmonella resistance in livestock meats   around Thai-Lao friendship bridge highlights importance of stringent food safety regulation and implementation of standard hygiene protocol in pre-retail meat industry.

Comments:
 1)  Title of manuscript is ambiguous and confusing. Authors should consider rephrasing the title based on findings in the manuscript.

2) Manuscript suffers a lot from grammatical errors and spelling mistakes. Authors should get the manuscript proofread by a native speaker to ensure that an international audience can clearly understand the text and findings.

3) Authors have mentioned that " Rates of 65%, 73% and 82% were chosen to calculate the sample sizes for pork, chicken and beef, respectively". Authors should elaborate how they defined "expected prevalence" and calculated sample size for this study.

4)  Throughout the manuscript, authors missed to italicize the species name. For example, Line 39/ 40:  S.London,  S. Corvallis, S.Rissen.   Scientific name of the species is always italicized without exception.

5) Authors mentioned in line 147 that " an association between a Salmonella positive proportion and the relevant specifications were determined by descriptive statistical analysis" what kind of statistical analysis they are referring here ?

6) What were the Primers, PCR conditions used for multilocus sequence typing? Authors should provide sufficient details in methods section so that findings can be replicated and reproduced.


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: MOLECULAR EVIDENCE FOR CROSS BOUNDARY SPREAD OF SALMONELLA SPP. IN MEAT SOLD AT RETAIL MARKETS IN THE MIDDLE MEKONG BASIN AREA
Review round: 2
Reviewer: 1

Output:
Basic reporting: They have improved on their writeup compared to their previous submission. However, there are a few technical terms they need to correct. Some have been indicated eg they should replace ‘collect’ or ‘collected’ with ‘isolate’or ‘isolated’. They should also write the names of the microorganisms as approved internationally, the first name begins with upper case letter while the second name begins with lower case letter. They need to correct these in the entire manuscript. If these are corrected the paper can be accepted.
Experimental design: The design is good and the supplied enough information in the methodology. The study was in depth enough and rigorous, and the methods used were appropriate.
Validity of the findings: Their work has provided important information as regards sources of contamination and spread of Salmonella through meat sold in the region. They were able for the first time to isolate and identify some sertypes which before now had not been isolated.
Additional comments: I have said all I want to say.


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: MOLECULAR EVIDENCE FOR CROSS BOUNDARY SPREAD OF SALMONELLA SPP. IN MEAT SOLD AT RETAIL MARKETS IN THE MIDDLE MEKONG BASIN AREA
Review round: 2
Reviewer: 2

Output:
Basic reporting: The authors have improved the manuscript well and appear to be fit for publication.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Despite the suggestion of making the figure 2 more illustrative, the authors want to stick to the original figure. I would suggest the authors for future manuscripts use more illustrative figures as they attract the audience increasing reads and thus citations.
Finally, since the authors plan not to use further analysis of the sequencing data in the present manuscript, plan a separate manuscript using this important data resource that has been generated.


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: MOLECULAR EVIDENCE FOR CROSS BOUNDARY SPREAD OF SALMONELLA SPP. IN MEAT SOLD AT RETAIL MARKETS IN THE MIDDLE MEKONG BASIN AREA
Review round: 2
Reviewer: 3

Output:
Basic reporting: Concerns has been satisfactorily addressed.
Experimental design: Concerns has been satisfactorily addressed.
Validity of the findings: Concerns has been satisfactorily addressed.
Additional comments: Concerns has been satisfactorily addressed.


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: PREDICTION OF DNA BINDING PROTEINS USING LOCAL FEATURES AND LONG-TERM DEPENDENCIES WITH PRIMARY SEQUENCES BASED ON DEEP LEARNING
Review round: 1
Reviewer: 1

Output:
Basic reporting: Prediction of DNA-binding protein is a hot topic in protein sciences. Many researchers worked and published a series of papers using diverse methods. In the current study, the authors proposed the PDBP-Fusion method based on deep learning (DL) to identify DBPs using primary sequences. The current manuscript can be published after covering the following concerns.
Comment 1: In line 169, keep space before “Accuracy”.
Comment 2: In line 232, text “in the follows” is not clear. Please provide alternate text. Similarly, replace “. And we” with “and”.
Comment 3: In line 265, keep space before “Therefore”.
Comment 4: In line 272, write “employed” after “we”.
Experimental design: Comment 1: The authors only used one training dataset. To evaluate the generalization power of the proposed method, authors must use the independent dataset i.e., PDB2272 already employed by Du. X et al. in their method (MsDBP: Exploring DNA-binding Proteins by Integrating Multi-scale Sequence Information via Chou’s 5-steps Rule).

Comment 2: Kindly compare the independent dataset (PDB2272) results with Du. X et al. study and include the comparison discussion in the manuscript.

Comment 3: The manuscript should be in proper structure. Section 3.1. Datasets need to discuss in Material and Method section.

Comment 4: The independent dataset (PDB2272) should be explained in Datasets section before section 2.1
Validity of the findings: Comment 1: The authors did not provide the codes for the proposed method. To reproduced/validate the proposed predictor, authors should be provide complete code i.e. one-hot code, word-embedding code, CNN and BiLSTM code, PDBP-CNN and PDBP-Fusion code, Figure 2, 5, 6 codes.
Comment 2: The authors used the fixed length sequences such as 600, 800. It is possible that important information may be lost. Authors should perform experiments on original length sequences and explain the obtain results in the manuscript.
Comment 3: In line 110, authors stated “we manually removed the sequence length less than 50” What is the number of sequences in the remaining dataset? If the number of sequences reduced in the dataset, how authors claim a fair comparison with the existing predictors.
Comment 4: Authors missed recently developed machine learning methods such as DBPPred-PDSD, DP‑BINDER, StackPDB, PredDBP-Stack for prediction of DNA binding proteins in the literature. Please discuss in the introduction section.

Comment 5: “To assess the performance of a proposed model, several validation methods are adopted. In a series of publications [1-6] in the field of bioinformatics, k-fold cross validation was widely used.”. Please add these lines in section 3.3 Model training and evaluation.
Additional comments: Comment 1: Several mistakes have been found. Please read the whole manuscript for spelling mistakes,  grammar mistakes, and sentence structures.


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: PREDICTION OF DNA BINDING PROTEINS USING LOCAL FEATURES AND LONG-TERM DEPENDENCIES WITH PRIMARY SEQUENCES BASED ON DEEP LEARNING
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper is well written and gives a clear understanding of the idea of using deep learning to predict DNA binding proteins. The figures are clearly annotated.
Experimental design: The research idea is well defined in the literature review and there is substantial evidence in the results to prove the validity of the experimental design. I found a method missing in the comparison of results.

1.	I believe the method I have attached here has great performance on the PDB dataset mentioned in their paper. StackDPPred: a stacking based prediction of DNA-binding protein from sequence has great performance and they also have a local copy of the software. I would like the author to compare the results for this method on the dataset PDB14189. I would highly recommend adding this method in comparison to Table 7 in the manuscript.
2.	In Table 3 and Table 4, the caption should be rewritten.
3.	I highly recommend the author to add an independent test dataset to validate the findings of the research.
4.	The webserver provided doesn’t work. Please fix this.
Validity of the findings: The findings in the paper are slightly better than the methods previously published by the researchers. Conclusions are well stated in terms of answering the question about DNA binding protein prediction. As mentioned above I speculate the performance of the predictor as compared to the StackDPPred. I would highly recommend the comparison of the PDBP-Fusion with StackDPPred.
As soon as the performance of this research outperforms the StackDPPred, I believe the novelty of the method can be validated.
Additional comments: Paper is well structured and clearly 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: PREDICTION OF DNA BINDING PROTEINS USING LOCAL FEATURES AND LONG-TERM DEPENDENCIES WITH PRIMARY SEQUENCES BASED ON DEEP LEARNING
Review round: 1
Reviewer: 3

Output:
Basic reporting: The authors use deep learning methods for the prediction of DNA binding proteins from sequences. However, significant changes must be made to experimental design to justify its relevance (like comparing with other state-of-the-art methods) on test datasets.
Experimental design: Methods are old and hence not appropriate as well as not well described. There are several latest papers with very good results which are not being compared or acknowledged.
Validity of the findings: The work does not include the necessary controls.

As mentioned above, the study does not include a test dataset. Also, the authors mention DNABP on the dataset section which has a different number of sequences than the ones the authors use.
Additional comments: 1) The authors present a method for prediction of DNA binding proteins from primary sequences alone (without PSSM) and have comparable performance to other machine learning methods on the dataset explored.

2)  Ma et. al have a different numbers of sequences in the benchmark dataset and test dataset compared to MsDBP. The authors say both datasets are similar but we didn't find it to be true.

3) The authors perform 5 fold cross-validation without a validation set and don't have a test dataset. The authors are probably aware that deep learning methods overfit easily and there should be a validation/test set at minimum to claim good performance.


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: PREDICTION OF DNA BINDING PROTEINS USING LOCAL FEATURES AND LONG-TERM DEPENDENCIES WITH PRIMARY SEQUENCES BASED ON DEEP LEARNING
Review round: 2
Reviewer: 1

Output:
Basic reporting: I believe the revised manuscript addresses all the concerns mentioned in the review. The implementation outperforms the previous methods and is a great addition in the field of DNA binding protein prediction.
Experimental design: The experimental design is concise and well thought.
Validity of the findings: The findings can be validated through the PDB14189 dataset results.
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: ASSESSING KINESTHETIC PROPRIOCEPTIVE FUNCTION OF THE UPPER LIMB: A NOVEL DYNAMIC MOVEMENT REPRODUCTION TASK USING A ROBOTIC ARM
Review round: 1
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: Methods should be improved.
Validity of the findings: No 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: ASSESSING KINESTHETIC PROPRIOCEPTIVE FUNCTION OF THE UPPER LIMB: A NOVEL DYNAMIC MOVEMENT REPRODUCTION TASK USING A ROBOTIC ARM
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper is well written and easy to read. The structure with the two studies being presented separately is not ideal (creates some repetition, and many subsections), but this is a rather minor point.
In the introduction and discussion, authors should better define/justify the aspect of proprioception they target with their task, and consider further comparison with other work that looked at proprioception assessments using robotic platforms (please refer to the general comments section for more details).
Finally, a figure presenting raw data (e.g., from one or two subjects) would be helpful to better understand how the outcome measure of the DMR task are calculated.
Experimental design: In general, the experiments and the data analysis seem suitable. Additional details on the procedure should be clarified or better motivated (please refer to the general comments section for more details).
Validity of the findings: Providing further data on measurement errors (smallest real difference) would help better evaluate the task and its potential for clinical applications. Given the different nature of the two tested tasks, their direct comparison (and the authors hypotheses in respect to that) is somewhat puzzling. The effect of visual information is a very interesting finding of the paper, however there is no strong conclusion about the actual mechanisms causing the observe differences between tasks. Please refer to the general comments section for more details.
Additional comments: In this paper, authors present a novel assessment of proprioceptive function (the DMR task) consisting of the reproduction of arm movements via a robotic platform, investigate its reliability and compare it to a joint reposition (JR) task. Furthermore, the role of visual information was investigated in both tasks. The paper is well written and the research is of interest (especially the part on the role of visual information). The motivation for the proposed task and its novelty/uniqueness compared to other such robotic assessments could be better highlighted.

Authors should consider the following points to improve their manuscripts.

1) Proprioception is complex and authors should try to better differentiate between the different aspects of proprioception, which contains position sense and kinaesthesia. It seems that the reproduction of dynamic movement patterns would be a kinaesthetic task (e.g., focusing on the perception of motion) while a test like the Joint Repositioning task is a measure of position sense. Thereby, it would not be surprising that the 2 are only poorly associated, since addressing different aspects of proprioception. This should be better discussed (potentially discussing the physiological process involved in the two), and the terminology might need to be adapted. For example, statements such as (in the conclusion) “the DMR task is promising to reliably test proprioceptive function” might need to be adapted to specifically mention kinaesthesia. Also, the hypotheses/expectations of the authors on that matter in the introduction (line 112-116) are rather confusing.

2) Addressing reliability of proprioception measures using robotic devices, authors should compare their work and results to other research that investigated this in healthy subjects and neurological patients. See for example the work of:
Rinderknecht et al. 2016 doi.org/10.3389/fnhum.2016.00316
Rinderknecht et al. 2018 doi: 10.1186/s12984-018-0387-6
Capello et al. 2015 doi:10.3389/fnhum.2015.00198
It would also be interesting to compare the task and its outcomes in terms of clinical applicability (e.g., time for the assessment, space required by the robot, amount of information that can be gathered, etc).

3) Regarding the procedure, it would be important to further explain a few methodological points and the rationale behind them. In particular:
-it is unclear whether the reference movement on the HapticMaster is performed passively by the robot (i.e., the robot moves the subject) or whether the subject has to actively explore the shape while the robot “restricts” the movement (if so, how is this done?).
-as authors briefly mention in their discussion, the shapes presented in the DMR task are complex and drawing them in a plane requires the combination of all joints of the upper limb (and there would be multiple possible joint configurations that would lead to an accurate movement reproduction). It is unclear how such a task could directly be compared to the JR task where one single joint is probed. While it can be argued that the DMR task probes proprioceptive function (e.g., kinaesthesia), it certainly does it in a very different way than JR, and this should be further highlighted. The fact that the DMR task involves multiple joints should be further discussed (possibly also as a reason for visual information not helping, since potentially less helpful or even unreliable for such complex movements?).
-Please specify what vision means. Is there visual feedback provided on a screen (e.g., information about end-point position in real time?) or is this simply that subjects can see the movement of their arm?
-It is unclear why, in the JR task, the experimenter did not physically move the arm to the target angle during the presentation of the reference position. The procedure with verbally indicating subjects to stop seems very inefficient and prone to generate errors and variability. Also, why was only one practice trial (vs 3 in the DMR) provided? This methodological decision may also influence the observed variability in the JR task.

4) Regarding the outcome variables, it is really unclear how the DMR error is calculated (is this based on a fit? is this calculated in polar coordinates?). A figure representing examples of raw data would be very helpful to visualise this metric.

5) In the discussion, authors touch upon clinical usability of their novel task. Besides reliability and ICC values, it would be very important and indicative to report measurement errors (in terms of smallest real difference) allowing to put into perspective the variability of one subject between sessions with the actual range of values (variability) among all subjects. This should help understand what magnitude of a change or deviation could be understood as (clinically) relevant when applying such test longitudinally.

6) When comparing reliability of the JR task to the work of Juul-Kristensen et al. 2008b (from line 361), one additional potential difference to discuss might be the number of subjects and their age distribution. It is known that proprioception declines with age, and since they seem to have tested a wider age range, they might have probed a less homogeneous population, which is in general beneficial for a reliability analysis. In general, the numbest of subjects in the first part of the present study seem rather small for a reliability analysis, especially in an homogeneous group of healthy subjects. This should be listed as a limitation. Also, it would have been nice to test subjects of older age.

Minor comments:
-Please consider adapting the title, as “using robotic arm movements” is very vague. It would be more informative to underline what makes this task novel.

-Abstract- Results: Please be specific and directly mention visual information and not “sensory input” in the fourth sentence, since authors specifically tested for the addition of visual information and not any sensory input.

-Abstract - Discussion: In the first sentence (and in other occurrences in the paper), it is not clear why authors refer to kinetic chain. Should this not be kinematic chain?

-line 65-69: It seems rather obvious that assessment quantifying position sense (i.e., once a posture is reached) provide little insight on dynamic movements, since these tasks should be measuring how well a static arm configuration is reproduced. Please consider rephrasing.