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

Input:
Title: CHARACTERIZATION OF RETINAL REGENERATION IN ADULT ZEBRAFISH FOLLOWING MULTIPLE ROUNDS OF PHOTOTOXIC LESION
Review round: 1
Reviewer: 3

Output:
Basic reporting: This study provides some interesting observations related to photoreceptor regeneration after damage due to light treatment in zebrafish, through the use of repeated light treatments and recovery periods.

Although the concept of repeated damage – and what are the consequences? – is intriguing, the manuscript offers very little in the way of new and important information regarding retinal regeneration. More importantly, this manuscript is missing several key controls, makes numerous unjustified assumptions regarding the outcomes of the experiments, and as a consequence greatly overstates the results. Very few of the authors’ claims are adequately supported by evidence.

The manuscript does not read well and is in need of proofreading. For example, line 47 contains many typos: “Finally, we following the six round of regeneration.” In lines 118-119, do the authors mean “photolytic” rather than “photoletic?” Photoletic does not appear to be a word. Line 143, was this really an antibody directed against UV light? In line 272, “phenomenon” is the singular form of “phenomena.”

Methods, line 112. What ages/sizes of fish were used?

Methods, line 127. Clarify whether the age-matched adults underwent the one round of damage (1X) at the same time/age as when the 6X group underwent the sixth round. The diagram at the top of Figure 1 does not convey this information very well, but implies that the 1X were sampled dozens of days before the 6X were sampled.

Methods, line 168. More detail is needed for the quantification methods. Were cells counted from specific, defined regions of a section? From all retinal layers? What was the denominator for the counts – per section, per a particular distance of retinal section?  Sample sizes for each study should be provided here as well.

Methods, lines 169-171. The use of ANOVA and then T-test makes no sense at all. For multiple groups, ANOVAs and an appropriate post-hoc test should be used.

Methods, line 173. This section must describe the qPCR primers, in a Table or similar. Where are they?

Methods, line 181. Should provide a brief description of quantification methods for qPCR analysis.  What were the internal standards/control transcripts and primers?

Results, line 255. Ectopic and supernumerary neurons in regenerated retina have been shown by many others, including but not limited to Hitchcock et al., 1992, Sherpa et al., 2008, and Sherpa et al., 2014.

Discussion, line 313. This reference does not show Shh function in development of amacrine and ganglion cells. Did the authors mean Neumann et al., 2000, or perhaps Shkumatava et al., 2004?

Figure 2 legend, line 344. Do the arrows point to individual cone opsins?  Why is opsin capitalized?
Experimental design: This study provides some interesting observations related to photoreceptor regeneration after damage due to light treatment in zebrafish, through the use of repeated light treatments and recovery periods.

Although the concept of repeated damage – and what are the consequences? – is intriguing, the manuscript offers very little in the way of new and important information regarding retinal regeneration. More importantly, this manuscript is missing several key controls, makes numerous unjustified assumptions regarding the outcomes of the experiments, and as a consequence greatly overstates the results. Very few of the authors’ claims are adequately supported by evidence.

Major concerns:

It is not clear why the authors carried out these studies. The introduction lays out an interesting context of scar formation vs. regeneration, but the experiments themselves are not clearly related to this context. There is no obvious rationale for the experimental design. Why were six rounds selected as the experimental design?  Why not 3? Why not 10?

The authors did not demonstrate that multiple rounds of degeneration and regeneration were actually accomplished, and with a time-course similar to the single round. This is merely assumed based upon information derived from prior work using the procedure for one round of degeneration and regeneration. It is possible that each round of light treatment results in different levels of damage. It is also possible that the response in each round has different kinetics. The “peak level” of proliferation sampling time (72 hpL) in the 6X group may not be the same as in the 1X group, and so the comparison of gene expression, etc. at this time is completely unjustified. The study, therefore, can only claim multiple rounds of high intensity light exposure, not regeneration. Collectively these concerns constitute a significant shortcoming in this manuscript.

Quantification of data is not clearly described, making it difficult to know what was actually counted and compared. Furthermore, no undamaged controls are included, and so true comparisons across samples are not even possible.

Specific comments:

Title: The title is not consistent with what is actually shown in the manuscript.

Abstract: The abstract also contains information not supported by the findings – six rounds of degeneration/regeneration were not demonstrated.

Abstract conclusions should be changed to say that increased numbers of mislocalized HuC/D cells were found. As is, it suggests that 1X light damage does not result in this feature, but it does based on their presented data. And line 103-104 of intro should be changed accordingly.

Author contributions:  “AR performed, collected…. Except where noted.” Noted where?

Introduction, line 97. Where did the authors study different subsets of Muller glia?

Results, line 197.  What is “key” about the time points of 36 and 72 hpL?

Results, lines 203-204. What is the rationale for the microglial investigation, and the meaning of the microglial data? This finding is not linked to any particular concept here. In the parentheses, what do the numbers refer to (13.8 vs. 46.2)?  Are these #s of microglia per retina?  Per section?  What?

Results, line 206 and nearby. Why was 36 hpL selected, and how is it known that this is a valid comparison for the 6X samples?

Results, line 214. The peak of progenitor amplification may be known from prior 1X experiments, but this is not demonstrated for the 6X experiments.

Discussion, line 258. What is meant by, “sensitive?”

Discussion, line 261. Is it true that phototoxicity is opsin-dependent? Has this actually been demonstrated for any model organism? Also, it would be easy to test this explanation by measuring opsin expression.

Discussion, line 288. Are microglia known to release pro-inflammatory cytokines in this particular context?

Discussion, line 296-297. Please include citations for each of the genes stated to be involved with each process/function.

Discussion, line 291. How do the authors know this is the peak time of proliferation and migration in the 6X example? This is an assumption based upon what is known of the 1X situation. 72 hpL may not be the peak at all.

Discussion beginning in line 307. The authors did not demonstrate a slow build-up of mislocalized neurons in Figure 5. If they have indeed done these studies (data not shown stated), then these data should be included in regards to comments above. Statements should be edited accordingly.

Figure 1 legend. The first figure should really be related to damage rather than “regeneration,” to demonstrate that the approach used actually accomplishes the intended outcome. And again, there is a need to demonstrate that each round causes damage – and is it the same sort of damage?  Also need to demonstrate actual regeneration in each round in order to use this terminology.

Figure 1. The diagram is misleading if the animals (1X vs. 6X) were actually age-matched.

Figure 1, continued. Why are there no undamaged controls for comparison?

Figure 1, continued.  A conclusion based on quantification is stated in the text along with p > 0.05. However, quantification analysis is not presented. Was a quantification of photoreceptor types performed and if so, how? If not, it should be done. This claim forms a basis for the presented study and is an important conclusion (discussion line 317, intro line 100). Further, this conclusion is stated in the text but is missing from the abstract.

Figure 2. The data in this figure needs to include TUNEL stain with quantification. Ideally, co-label and quantification of TUNEL and each of the photoreceptor cell types. As mentioned above, this should probably constitute the first figure. With the increased number of 4C4+ cells found at the site of light damage, it would be interesting to see if they are all associated with TUNEL in some way? Since the antigen for 4C4 is unknown, it is not clear if this antibody marks only microglia or if it also marks macrophages. Text should be changed accordingly. Also, without demonstrating photoreceptor death at each exposure to intense light, it is not possible to interpret the 4C4 images.

Figure 2. In the graph (K), zpr1+ quantification appears equal between 1X and 6X light damage, however the images shown suggest increased numbers of zpr1 present in 6X light damage. If the quantification is correct, then better representative images should be chosen.

Figure 2, continued. In K, the Y axis is not fully labeled. Photoreceptors per what?  And again, undamaged controls are needed.

Figure 3. Where are the undamaged controls for comparison?

Figure 3, continued. C’ to D’ comparisons of Muller glia features. Please provide more information about different visual features between the Muller glia in 1X to 6X. This figure appears to be the basis for the hypertrophy conclusions stated in the abstract, however, this hypertrophy appears transient since the images at 72 hpL and in regenerated retinas (Figure 5) do not reveal Muller glia hypertrophy. The conclusions and abstract should be edited accordingly to specify that this is a transient feature.

Figure 3F. qPCR and PCNA stains suggest increase stat3 without subsequent increase in cell cycle. Please discuss this further and it’s implications, since one function of stat proteins is to induce cell proliferation. Also, what are the transcriptional outcomes of stat3 signaling in Muller glia?

Figure 4. Need undamaged controls for comparison.

Figure 4, continued. Muller glia endfeet appear different in B’’ to A’’, also noted in Figure 3 comparing C to D. 4C: for presentation purposes, helpful to group and annotate the genes by process to facilitate reader comprehension.

Figures 3 and 4. Upregulation of gfap also seems to be transient at 36 hpL (figure 3) as it is not different at 72 hpL (Figure 4). Conclusions and relevant statements should be edited accordingly in abstract and text.

All Figures containing qPCR data. The format for data presentation is rather strange, and cluttered by the inclusion of all of the 1X (which are all, ”1” when using the Fold Change as the Y-axis). Fold-change for each (1X and 6X), compared to levels in undamaged controls, may be a more useful metric, as it will show the response to the treatment in the 1X case vs. the 6X case. However, this reviewer remains skeptical that these time points are truly comparable, because the kinetics of the response to light treatment may be different in the 1X vs. 6X group.

Figure 5. Need undamaged controls for comparison. In E, the Y axis is incompletely labeled. # HuC/D+ cells per what?

Figure 5, continued.  Why focus only on HuC/D+ neurons? Were photoreceptors mislocalized also, as seen after a ouabain lesion (Sherpa et al., 2014)?  There are non-Hu+ nuclei in the IPL.
Validity of the findings: This study provides some interesting observations related to photoreceptor regeneration after damage due to light treatment in zebrafish, through the use of repeated light treatments and recovery periods.

Although the concept of repeated damage – and what are the consequences? – is intriguing, the manuscript offers very little in the way of new and important information regarding retinal regeneration. More importantly, this manuscript is missing several key controls, makes numerous unjustified assumptions regarding the outcomes of the experiments, and as a consequence greatly overstates the results. Very few of the authors’ claims are adequately supported by evidence.

Major concerns:

The authors did not demonstrate that multiple rounds of degeneration and regeneration were actually accomplished, and with a time-course similar to the single round. This is merely assumed based upon information derived from prior work using the procedure for one round of degeneration and regeneration. It is possible that each round of light treatment results in different levels of damage. It is also possible that the response in each round has different kinetics. The “peak level” of proliferation sampling time (72 hpL) in the 6X group may not be the same as in the 1X group, and so the comparison of gene expression, etc. at this time is completely unjustified. The study, therefore, can only claim multiple rounds of high intensity light exposure, not regeneration. Collectively these concerns constitute a significant shortcoming in this manuscript.

Results, line 188. How do the authors know there was regeneration in each round?  The terms, "light treatment and recovery" might be better, with an assumption of regeneration based upon the outcome after 6 rounds of damage. Even then there are still major unknowns regarding kinetics of any damage and/or any regeneration, such that there is little or no justification for the selection of sampling times.
Additional comments: No additional comments


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

Input:
Title: CHARACTERIZATION OF RETINAL REGENERATION IN ADULT ZEBRAFISH FOLLOWING MULTIPLE ROUNDS OF PHOTOTOXIC LESION
Review round: 2
Reviewer: 1

Output:
Basic reporting: This revised manuscript by Ranski et al. is much improved over the original submission and most of my previous concerns have been addressed. In particular, the addition of data for Muller glia proliferation after one vs. two rounds of light damage, better descriptions of the methods, and revision of text in the Introduction and Discussion significantly clarify and strengthen the study. I just a have a few minor changes to recommend prior to publication:

1) Methods, line 156. I’m not sure what the sentence “The null hypothesis was accepted…” is referring to.
2) Results, lines 243-244 and Figure 2. The interpretation that “the same population of Muller glia do not re-enter the cell cycle following each individual light damage event” is not accurate. If 35% of the MG are double labeled, this is in fact a significant proportion of cells that do re-enter the cell cycle. And looking at the quantification of the data in Figure 2, it seems that there is not significantly more PCNA only cells (2nd round) than double labeled cells (1st plus 2nd round). So this indicates that in fact it is mostly the same population from the first round, with some added PCNA single positives in the second round. Therefore, the authors should revise their interpretations of these data accordingly (and should also revise how they refer to these data in the Introduction and Discussion).
3) Discussion lines 387-388: “This suggests a complex re-patterning of cell signaling programs in Müller glia responding to retinas that have been exposed to multiple rounds of phototoxic lesion…” The data also suggest that there may be a ceiling with respect to how much cell proliferation can be induced by light damage.

4) Discussion lines 435-436: “Despite aberrancies seen in recovery after phototoxic lesion, we determined that the long term regenerative potential of Müller glia appears to remain relatively intact.” I agree, but in the Introduction (lines 112-113) the authors state that it's possible the MG are beginning to exhaust that stem cell potential after multiple rounds of LD. The authors may want to pull back on that statement if they don't think there is strong evidence for it.
Experimental design: see above
Validity of the findings: see above
Additional comments: see above


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

Input:
Title: CHARACTERIZATION OF RETINAL REGENERATION IN ADULT ZEBRAFISH FOLLOWING MULTIPLE ROUNDS OF PHOTOTOXIC LESION
Review round: 2
Reviewer: 2

Output:
Basic reporting: This revised manuscript is a much more coherent reporting and contextualizing of the study.
Experimental design: The methods have been greatly revised to make the approach, sample sizes, and data analysis more transparent and repeatable.
Validity of the findings: Given the revisions of the methods, figures, and results, the outcome of the study is now clearer to interpret and better put in context throughout the manuscript.
Additional comments: This resubmitted manuscript is a much more cohesive description of the study examining how multiple rounds of phototoxic damage impacts the regenerative response. The extensive revisions by the authors have greatly improved the readability and ease of data interpretation. I have one small suggestion and something for the authors to consider in ongoing research.

In line 316, the statement "...consistent with a recent report..." should probably read "...consistent with reports..." since there are multiple citations and one is quite old.

The results that there is more photoreceptor death but a comparable proliferative response in the 6x compared to the 1x treatment despite using the same damage paradigm continues to be intriguing. The revised manuscript discusses this much more clearly. It would be interesting to consider in ongoing research if reduction of Muller glial cell function, as the data in the paper indicate, reduces neuroprotection of damaged photoreceptors. That would result in less photoreceptor survival (as indicated by more photoreceptor cell death) in response to the same light damage.


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

Input:
Title: CHARACTERIZATION OF RETINAL REGENERATION IN ADULT ZEBRAFISH FOLLOWING MULTIPLE ROUNDS OF PHOTOTOXIC LESION
Review round: 2
Reviewer: 3

Output:
Basic reporting: This version of the manuscript is greatly improved, with the addition of necessary control samples to the Figures, detailed explanation of the now appropriate statistics, better terminology and referencing of the literature, and the acknowledgment of study limitations with age as a confounding variable.

However, there remain several places in the manuscript that require improvements in clarity, the authors continue to overstate findings, and there are a number of other issues.

Introduction, lines 61-65. It is not clear how the findings from Qin et al. (2009) support the conclusions stated in the last two phrases of the sentence.

Introduction, line 103. “Normal numbers” – same issue as in the abstract.

Introduction, lines 112-113. Since no epigenetic studies (as the field currently considers such studies) were performed here, this statement is not warranted.

Methods, line 156. “The null hypothesis…..”  This information belongs in Results, not Methods.

Methods, line 217 (and in the description of Table 1). “span exons”  Do the authors mean, span introns?  Or span exon-exon junctions (splice junctions)?

Consider re-ordering Figures 1 and 2 (switching them). This would make more sense given the ptic/data in Figure 3 and those that follow.

Results, line 226. This first section would benefit from a brief summary of the characteristics of damage due to the light damage method used (e.g., types of photoreceptors destroyed, timeline, any dorsal/ventral regional differences, etc.).

Figure 1. Are these data following 2X light exposure? Needs to be clearly stated in figure legend and indicated in figure.

Results regarding Figure 1 (line 224). Header should be reworded as some of the BrdU+ MG were also PCNA+ (35% according to the authors’ data).

Results, line 266. Do the authors mean, not significantly different?

Results, line 308. “near-normal numbers” – this is even more vague and confusing than “normal numbers.”

Results, line 316. More than one report is cited, and at least one of them is definitely not recent.

Discussion, lines 340-342. This reviewer struggled to understand this sentence.

Discussion, line 369. Upregulation in stat3 at 36 hpL – in what vs. what?

Discussion, line 371. The 4C4+ microglia could also contribute to increased inflammatory response. At best in this study, they are “associated” with multiple rounds of light exposure.

Discussion, line 373. The wording of this sentence suggests that 4C4+ microglia specifically have been shown to secrete IL-6. This statement should be edited to clarify that “microglia” have been shown the release inflammatory factors, since 4C4 was not used in the cited study. Cited paper is a review, and should be noted as such.
Discussion, line 381. What are “normal circumstances?”

Discussion, lines 347-348. Same struggle here.

Discussion, lines 431-433. The first part of this sentence contradicts the second part. The sentence should be removed.

Discussion, line 442 and 447. The term, “epigenetic” in the recent literature has come to convey primarily chromatin alteration. Although the authors may intend to use the term more broadly, use of the term comes across as misleading, because chromatin was not investigated.
Experimental design: Abstract in general. The statement of gliotic scars followed by the potential of fish MG to become gliotic in abstract is still distracting, as it isn’t directly tested in this study. The abstract should instead start with a more compelling rationale for multiple rounds of light damage, as current wording of the abstract still makes this rationale unclear. Further, the claims of a gliotic response by fish MG here are not fully substantiated, as it is entirely possible that the multiple rounds of light exposure actually damage the MG directly. This should be considered throughout the manuscript and warrants editing in all sections.

Introduction, lines 88-89. Still need more justification for this study. Was the goal to see if multiple rounds of light exposure would lead to a gliotic response and/or failure to regenerate?

Methods, Results, and Figures in general. Regarding damage at each round of light exposure—it needs to be clear in the MS that this damage is assumed (based on loss/alterations of staining for photoreceptor specific markers/proteins) because no cell death was actually directly analyzed. For example, the repeated light exposure could potentially lead to opsin denaturing (ie unfolding or alteration of the antigens detected by the antibodies used).  In addition, along those lines, what can be seen from the DAPI+ nuclei in INL look abnormal (Figure 2, however images are cropped). This should also lead to a consideration of their findings regarding different “subsets” of Muller glia…does repeat light damage damage the MG (would be indicated be TUNEL in INL/colocalization with GFAP/GS) which would lead to characteristics seen (such as different subsets undergoing cell division or alterations in their morphology), or are the MG truly “gliotic”?  Given the above discussion, the terms ‘damage & recovery” are not warranted, instead terminology should be limited to “multiple rounds of light exposure”.

Methods, line 125. Section header “Photoreceptor Lesions” should instead be “Intense Light Exposure.”

Results, first paragraph. It seems odd that the proliferating MG were not simply quantified – in this way the authors could potentially compare 1X to 2X to 6X using PCNA.

The provided clarification of ages in regards to experimental design and sampling is essential to interpreting the study and considering any conclusions. The comparison of 9 mo to 18 mo fish for 1X light treatment data should be included as (supplemental) data. This was described in the authors’ rebuttal but not included in the revised MS.

Results, lines 282-304 and Figure 4J. The 1x vs. 6x ddCT comparison is not justified, the additional age variable is a problem here. This reviewer suggests comparisons of age-matched undamaged vs. 1x, and also age-matched undamaged vs. 6x.

Results, line 309 (and Figure 6). An explanation/justification for the selection of 28 dpL is needed. Again, it is entirely possible that the kinetics to get to this number do not match for 1x vs. 6x.

Discussion, line 359. The authors did not demonstrate six rounds of damage. Suggest the term “phototoxic treatment,” or “light exposure.”
Validity of the findings: Introduction, line 91. Regarding stem cell response of Muller glia—this was not directly tested in this MS beyond their ability to proliferate, and even that was limited.

Introduction, line 94.  Why? Because the Muller glia have limited stemness or because they themselves are damaged?

Introduction, line 100. Again, did not demonstrate damage. Rather, exposing the retina multiple times to intense light.

Methods, Results, and Figures in general. Regarding damage at each round of light exposure—it needs to be clear in the MS that this damage is assumed (based on loss/alterations of staining for photoreceptor specific markers/proteins) because no cell death was actually directly analyzed. For example, the repeated light exposure could potentially lead to opsin denaturing (ie unfolding or alteration of the antigens detected by the antibodies used).  In addition, along those lines, what can be seen from the DAPI+ nuclei in INL look abnormal (Figure 2, however images are cropped). This should also lead to a consideration of their findings regarding different “subsets” of Muller glia…does repeat light damage damage the MG (would be indicated be TUNEL in INL/colocalization with GFAP/GS) which would lead to characteristics seen (such as different subsets undergoing cell division or alterations in their morphology), or are the MG truly “gliotic”?  Given the above discussion, the terms ‘damage & recovery” are not warranted, instead terminology should be limited to “multiple rounds of light exposure."

The provided clarification of ages in regards to experimental design and sampling is essential to interpreting the study and considering any conclusions. The comparison of 9 mo to 18 mo fish for 1X light treatment data should be included as (supplemental) data. This was described in the authors’ rebuttal but not included in the revised MS.

Results, lines 282-304 and Figure 4J. The 1x vs. 6x ddCT comparison is not justified, the additional age variable is a problem here. This reviewer suggests comparisons of age-matched undamaged vs. 1x, and also age-matched undamaged vs. 6x.

Results, line 309 (and Figure 6). An explanation/justification for the selection of 28 dpL is needed. Again, it is entirely possible that the kinetics to get to this number do not match for 1x vs. 6x.

Discussion, line 430. This study did not address recruitment of 4C4+ cells. Findings were limited to a presence of these cells and their origins remain unknown.

Discussion, last paragraph (starting line 435). This study did not demonstrate long-term regenerative potential of Muller glia. Rather, it showed that Muller glia likely re-entered cell cycle (and perhaps were reactive) following multiple rounds of light exposure. See discussion above regarding this point.
Additional comments: This version of the manuscript is greatly improved, with the addition of necessary control samples to the Figures, detailed explanation of the now appropriate statistics, better terminology and referencing of the literature, and the acknowledgment of study limitations with age as a confounding variable.

However, there remain several places in the manuscript that require improvements in clarity, the authors continue to overstate findings, and there are a number of other issues.

Some comments appear under BOTH Experimental Design and Validity of the Findings sections, because these were issues related to experimental design that influenced the validity of the authors' stated findings.


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: PRELIMINARY ANALYSIS OF NEW ZEALAND SCAMPI (METANEPHROPS CHALLENGERI) DIET USING METABARCODING
Review round: 1
Reviewer: 1

Output:
Basic reporting: In general, the manuscript is well-written, the research problem is clearly defined and the sufficient context is provided.
Experimental design: The research question is clearly defined and meaningful. However I feel that the authors could have done much more for the exploration of this question (one may argue that this remark could be applied to any study but I have several specific points to consider).
First, the authors used only two ways to get rid of inhibitors - the dilution and the addition of BSA. Both have limited value - the dilution can be not efficient in case of low DNA content and/or high inhibitor content and BSA is not efficient for several types of inhibitors. PCR inhibitors are well known issue for many metagenomic samples (soil, food, fecal samples). There are many protocols and commercially available kits for the removal of these inhibitors, they are widely used in metabarcoding studies (see, e.g. https://www.frontiersin.org/articles/10.3389/fmars.2016.00096/full). Why they were not used?
Second, the DNA samples obviously contain the host DNA which is coamplified together with the DNA from the digested material. Moreover, the host DNA will amplify with much higher efficiency because it is less degraded. Thus it can mask the presence of certain taxa in teh digested material, especially when samples are sequenced with low coverage (by the way, the number of reads per sample in not mentioned anywhere in the manuscript; it is an important information and should be reported). To overcome this, the blocking oligonucleotides specific to the host DNA are used (see e.g. https://www.ncbi.nlm.nih.gov/pmc/articles/PMC5653352/, https://www.ncbi.nlm.nih.gov/pmc/articles/PMC5112926/). This study would greatly benefit from this approach, given that the diet hit count very low.
Validity of the findings: The manuscript has several methodological shortcomings that decrease the validity and the usefulness of the findings.
Additional comments: - please consider the factor of GC content as it greatly affects PCR efficiency.
- there are several typos and inconsistencies, for example at lane 534: "has oval cells 21-35 pm". What is pm? Picometers? I doubt that the cells are so small.


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: PRELIMINARY ANALYSIS OF NEW ZEALAND SCAMPI (METANEPHROPS CHALLENGERI) DIET USING METABARCODING
Review round: 1
Reviewer: 2

Output:
Basic reporting: A generally well-written manuscript with sufficient background information, relevant literature, and good structure.  A few suggestions for improvement:
line 41: Regarding the Balss 1914 comment on high value of deep sea lobsters. Reference not listed in literature cited.
Some of the methodological details could be moved to a supplemental materials section to make the Methods less involved and lengthy, thus more readable. For example, (Line 144): some of the details in the paragraph describing the PCR cycle.
Discussion is quite long relative to the rest of the paper.

Figure 1:  Not necessary as it is not very informative.  No labeling of islands or depth strata.  A figure like this isn't necessary to show one sampling location.
Experimental design: lines 109-111: "For comparison, frozen individuals of commercially harvested NZ scampi were supplied by Sanford Ltd 110 (Auckland, New Zealand), their location of harvesting unknown."  This is a problematic confounding factor for comparison - different locations, different diets?  Better to have frozen some of their own samples in manner similar to commercial enterprises.

Also missed a big opportunity to compare these methods to the standard gut content analysis.  Could have identified the stomach contents microscopically, then conducted these genomic analyses

A laboratory-based food preference & gut content study would also be a better way to conduct the initial analysis to cross-check the methods before trying to apply them to a field data set.
Validity of the findings: Validity of results suffers from low sample sizes and are confounded by all the distinctions.

lines 280-285:  The contradictory results for the fore- and hind-gut comparisons of the two methods is perplexing and suggests problems with the resolution of the two methods. Which is correct? I agree with authors conclusions in the Discussion that using the entire gut contents seems the best approach.

lines 307-310: "The databases (18S verse COI) did not confidently identify any of the same organisms and the taxonomic resolution and level of confidence varied for the same OTU between databases when assessing the same gene (Table S1 and Table S2)." This result does not instill much confidence.
Line 228: any sequence reads identified as lobster presumed as contamination but some lobsters will eat other lobsters so you would discount this food source?
Additional comments: A generally well-prepared manuscript, but the results are not clear-cut and raise more questions than provide solutions - which is not what one desires in a paper focusing on methods development.  The experimental design also does not lend itself particularly well to the over-arching goals of the study.  Specifically, the study comes across as a latent attempt to do something more sophisticated with basic trawl data, in this case to use genomic metabarcoding of stomach contents of a deep sea scampi to try to ascertain its diet.  However, the authors did not compare their results to a robust, comparable control data set (e.g., their commercial frozen samples), they didn't take the time to conduct a standard gut content study for comparison, and they did not attempt a laboratory food preference study to confirm the methodology.  These are lethal weaknesses.


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: PRELIMINARY ANALYSIS OF NEW ZEALAND SCAMPI (METANEPHROPS CHALLENGERI) DIET USING METABARCODING
Review round: 1
Reviewer: 3

Output:
Basic reporting: On the up side, this study was an interesting use of the metabarcoding approach and provides new information about a species that had very little prior data. That could be a reasonable justification for publishing the results. On the down side, it only reported data from a very small sample size, which makes it difficult to determine whether the results were several points in a “noisy” system and represented an accurate sample of the whole system. The use of BSA to suppress PCR inhibitors and a comparison of preservation methods was not novel, but it was helpful information to report for such a study. Usually this information is briefly reported in the results section and does not become a major component of the discussion. The comparison of polymerase enzymes was limited to two manufacturers and, because suppliers often switch and adjust their products, this may provide limited or short term value. The fact that this study was the first to report information about the diet of Metanephrops challengeri (six samples from one location) is the important result that will provide some benefit to the science community. However, I am concerned that the small sample size might be misrepresenting the total amount of diversity in the diet and the best methodologies to use. One way to address this concern would be to provide a justification that the diet variability is expected to be narrow (among individuals and sites, and over time e.g. seasonal differences) and so a small sample is all that is needed to provide an accurate picture. Alternatively, if the authors believe that their study is not about the species that were detected in the diet, then they should discuss the shortcomings of the sample size and what sample design might be best for this, and similar, species in a full scale study.

• The abstract did not contain any information about the DNA sequencing results (e.g. the number of sequences returned and searched)
• L28: “resulted in better results” seems awkward.
• L65: “through time” is odd, change to "among phylogenetically distinct taxa”
• L66: “powerful” is an ambiguous and loose term that is used to describe the metabarcoding method
• L70” “high taxonomic resolution” - does this mean a wide range of species can be detected, or that the detection can be made to the species (e.g. fine scale) level?
• L73: Sequencing costs are a direct cost, but if all indirect costs are considered (e.g. people’s time) then the new method might be similar to the old method. The overall science system is set up to easily measure direct costs (and largely ignore indirect costs). Presumably it is hard to measure the real costs of the two methods.
• L83-85: A trial of only two polymerases seems small.  It must be hard to work out what is a good sample of polymerases. How many are available on the market? If manufacturers/suppliers change over time the results will be obsolete quite soon.
• L93: It would be better to use the genus-species name instead of the common name
• L126: The DNA concentration of the samples was measured but never reported. Was it used to inform the dilutions for the comparisons of samples? The lack of standardisation of the DNA template concentration and the small sample size means there is a good chance that the results are somewhat uninformative.
• L140: An amount of 1 µl of DNA was added, but would it be better to be consistent with the way all of the other reagents are list and include a concentration of DNA that was added.
• L324: What about the low DNA concentration? Add in something here about how low template concentration might be an important factor for PCR success.
• The labels on Table 1 seem to show that only five different samples were used. Sample 8 looked like in was a combination of Fro1 and Fro2.
• The term "PCR reactions” is repeating the word ‘reactions’, which is a bit strange.
Experimental design:
Validity of the findings:
Additional comments: No additional comments


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

Input:
Title: PRELIMINARY ANALYSIS OF NEW ZEALAND SCAMPI (METANEPHROPS CHALLENGERI) DIET USING METABARCODING
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: Please provide the table on the results of DNA extraction with alternative kits. By the way, did you analyzed the DNA integrity (using capillary or agarose gel electrophoresis)?

Regarding GC content, although GC content of primers is also important, I meant the content of the templates. High GC templates are amplified less efficiently than those with low or moderate GC. Please provide GC content values for M. challengeri marker sequences and for those of diet sequences.

Thank you for providing read counts, this information is important though raises additional questions. Why the number of reads for COI in Fro1 & Fro2 is so low? The number of COI paired reads for 70.9 hindgut sample amplified with Platinum taq is high but the number of merged reads is two orders of magnitude lower. Why? Where the remaining reads come from?
Validity of the findings: no comment
Additional comments: no comment


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

Input:
Title: AN EXAMINATION OF THE DEVONIAN FISHES OF MICHIGAN
Review round: 1
Reviewer: 1

Output:
Basic reporting: Minor structure comment: references to figure are typically in the format of Author (1999: fig. 1). I noted this in the text as a PDF sticky note.

Figure captions easier to read if each letter is in bold. One figure uses A) vs. A, in other figures.
Experimental design: no comment
Validity of the findings: no comments
Additional comments: I have made all my comments as PDF sticky notes. I have a question on two figures whether they are in focus or not.

I have a question as to how the supplemental data is presented. The excel table far exceeds a normal page but if presented as an excel file then the reader can view it.

If you add indet. aspinothoracid arthrodires to the text based on the Antrim list in Elliott et al., 2000 then you need to add it also to the supplemental list.

My institution is listed as Columbia Univeristy Chicago -- it should be Concordia University Chicago


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: AN EXAMINATION OF THE DEVONIAN FISHES OF MICHIGAN
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper is well written and for the most part well illustrated, although one images I've noted in the review  copy could be improved. It reviews the fossil fish faunas well, but could include a few more explanatory comments about dubious genera (eg Ptyctodus, ,a s noted in my comments on the review pdf). Data well presented, structure of the paper is good.
Experimental design: All OK, not really relevant to palaeontology review papers like this.
Validity of the findings: Mostly good, with in depth discussion of depositional environment setc.
I've noted a few things I disagree with or take issue with in my comments on the text.

1. Bothriolepis in Fig 9 is NOT Bothriolepis   but an Arthrodire or Petalichthyid style of plate. Its certainly not an AVL of an antiarch  as it lacks evidence of the lateral lamina or brachial process, and is way too narrow.

2. Fig 10 supragnathal plate can't be attributed yet to Eczematolepis as no-one has yet proven its a ptyctodontid. I have my own evidence for this (not yet published though, , as I've studied this material in the Smithsonian and Field Museum collections).
Additional comments: It's  a good paper with fine illustrations of the faunas, but needs a few more points discussed as I've drawn attention to in the comments attached to the review pdf. Some specific points to address:-

1. Bothriolepis in Fig 9 is NOT Bothriolepis   but an Arthrodire or Petalichthyid style of plate. Its certainly not an AVL of an antiarch  as it lacks evidence of the lateral lamina or brachial process, and is way too narrow.

2. Fig 10 Supragnathal plate can't be attributed yet to Eczematolepis as no-one has yet proven its a ptyctodontid. I have my own separate evidence for this (not yet published though, as I've studied this material in the Smithsonian and Field Museum collections) - perhaps something I could contact the authors about separately as I would welcome a future collaboration on the project I've started with this genus.


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: GΑQ AND PHOSPHOLIPASE CΒ SIGNALING REGULATE NOCICEPTOR SENSITIVITY IN DROSOPHILA MELANOGASTER LARVAE
Review round: 1
Reviewer: 1

Output:
Basic reporting: The article is clear and unambiguous. Sufficient background and context are provided. The figures are professional and the article is self contained with relevant results to hypotheses.
Experimental design: The research is original within the scope of the journal.

Research question is well defined.

The investigation is rigorous.

Methods are described with sufficient detail and information to replicate.
Validity of the findings: The study presents mainly positive data and it also includes one instance of negative data where a NorpA RNAi line does not have a phenotype.

The data are very nicely presented with all the points of data represented in the plots.

Conclusions are well stated.

There is little to no speculation.
Additional comments: The vast amplification that is possible with G-protein coupled signaling cascades may make RNAi approaches relatively ineffective.  Tissue specific Cas9 expression will soon be available for targeting the cIVda neurons. A targeted CRISPR KO might result in a more severe phenotype than has been observed in the study with an RNAi approach.


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: GΑQ AND PHOSPHOLIPASE CΒ SIGNALING REGULATE NOCICEPTOR SENSITIVITY IN DROSOPHILA MELANOGASTER LARVAE
Review round: 1
Reviewer: 2

Output:
Basic reporting: Throughout, by “insensitive”, the authors mean “hyposensitive”?  To this reviewer, “insensitive” means lack of sensitivity, not decreased sensitivity.

188-195, these UAS-RNAi lines are driven by ppk-Gal4, correct?

The Figure 1 legend should describe the temperature of the thermal probe.

213-215, remove interpretation of results to the Discussion section

238, 318 I think instead of “principle”, the authors mean “principal”

343 “branch” should be “branching”?

251-252, remove interpretation to Discussion

286-287  “NorpA is likely an effector of Gαq in the nociceptors, given the defective nociception phenotypes observed in norpA knockdown larvae.”  Does this result really imply any causal relationship?  Could be coincidental?  An epistasis experiment would help with this.
Experimental design: The operator of the thermal probe should be blinded to the genotype.  If this was indeed the case, or there is some other method of reducing the possibility of unintentional operator bias, those details should be included in the description of the method.

What is the accuracy of the temperature-control system of the thermal probe?  How much variability exists in the temperature at the contact point under experimental conditions?

For von Frey probes, it is better to refer not to length (since diameter is also a factor) but to the force delivered, expressed in millinewtons…

Given the modest phenotypic effects observed and sometimes equivocal relationship to IR genotype, does N=40 give sufficient power to resolve?  Has a power analysis been conducted?
Validity of the findings: This reviewer is concerned about the apparently inconsistent application of appropriate controls.  In some experiments, such as Fig 2, comparison of Gal4/UAS experimental genotypes are appropriately compared with both Gal4-only and UAS-only controls.  In contrast, Fig 1 and Fig 3 present just one negative control: Gal4-only.  (Fig 4 appropriately depicts only one control: the Gal4-only control.)  No rationale is given for the omission of missing controls.  Were the unpresented controls not analyzed?  In this reviewer’s opinion, both controls should be analyzed for experiments like those in Figures 1-3.  If only one is presented graphically, the results of the other should be available in a supplement or at least described in the text.  Comparisons in which the phenotype of the experimental genotype is not significantly different from that of both UAS-only and Gal4-only controls are not on the firmest footing.   These control for important effects like leakiness of UAS-RNAi constructs and phenotypes of Gal4 insertions themselves.

Figure 1:  Modest hyposensitivity observed in Gaq under-expression studies of thermonociception, more convincing hyposensitivity observed in mechanonociception compared to Gal4-only.  However UAS-only controls are not presented.  The results depicted in Fig 1A separate from B, and C separate from D, the reason for this separation is not obvious.  If UAS-only controls were analyzed and presented, there would be a separate UAS-only control genotype required for each UAS-RNAi line used. So without comparison to these controls, these results are not as convincing as they could be.

Figure 2:  Modest hypersensitivity observed in Gaq over-expression studies of both thermo- and mechanonociception.  The figure legend for 2A states significantly different compared with both controls, and both controls are depicted, so the claim is fully supported here.  For 2B, both controls are presented, but experimental shows difference only to UAS-only.  So while the control structure of this experiment is satisfactory, because the experimental shows difference to only one of the controls, the mechanonociception results are not as convincing as they could be.

Figure 3:  For norpA, one RNAi line JF01713 showed modest decrement in thermosensitivity, significantly different from Gal4-only control.  However the UAS-only control is not shown or described.  But the RNAi line JF01585 shows no differences from Gal4-only control, UAS-only control not shown or described.  For norpA RNAi and mechanonociception, RNAi line JF01585 showed hyposensitivity compared to Gal4-only, RNAi line JF01713 showed no differences compared to Gal4-only.  So that is the opposite response from these lines, compared to thermonociception.  So these results put the conclusions in doubt.

Figure 4:  Morphometry of ddaC cells.  These are the most dorsal mdIV cells, presumably the cells most stimulated by mechanical stimuli, but thermal stimuli were presented laterally.  The controls presented are complete and appropriate.  These results are not much in doubt, but they are negative results that while they help to interpret, do not directly test the major hypotheses.

This reviewer is concerned that no evidence is presented to confirm the effectiveness of the cell-specific suppression or overexpression of the targets, or other evidence of their normal expression in these neurons.  For example, validated antibodies could be employed for immunohistological analysis of wild-type and manipulated tissues.  Perhaps validated MiMIC lines are available that might indicate the normal expression patterns of the targets.
Additional comments: The authors are to be commended for clear writing style.  The experimental design is to be commended for combined use of over-expression tools and multiple non-overlapping IR transgenes to produce cell specific under-expression.  Analysis of nociceptor morphology is excellent and important for interpretation of any changes in sensitivity phenotypes.   Excellent coverage of the state of the field and context for the experiments.  Record-keeping is excellent.


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: GΑQ AND PHOSPHOLIPASE CΒ SIGNALING REGULATE NOCICEPTOR SENSITIVITY IN DROSOPHILA MELANOGASTER LARVAE
Review round: 1
Reviewer: 3

Output:
Basic reporting: Pass.
Experimental design: Pass.
Validity of the findings: Fail.

The data is not robust and therefore, weakens the conclusion.
Additional comments: In this manuscript, the authors characterize the role of Gq/norpA signaling on nociception in Drosophila larvae. It is an interesting study but I have the following concerns:

1)	The effect of different Gq knockdown lines on thermal nociception is different (Fig 1). Similar inconsistency is seen with different norpA knockdown lines in Fig 3. It is important to show the knockdown efficiency of each line to check whether the amounts of Gaq and norpA transcripts dictate the outcome.

2)	The latency after thermal stimulation for the ppk/+ line in Fig 1 are 1.9 and 1.7 seconds while in Fig 2 it is 2.8 seconds. Although this kind of variability is not uncommon, the Gq knockdown lines show the latency of 3.0 and 2.2 in Fig 1 whereas Gq overexpression line has a latency of 2.2. This shows that the Gq gain- and loss-of-function conditions have very weak effects on thermal nociception and this considerably weakens the premise of the manuscript.

3)	Since the phenotypic effect of Gaq/norpA modulation is very weak, the authors should show how they affect ion influx in these cells in response to thermal stimuli.


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: GΑQ AND PHOSPHOLIPASE CΒ SIGNALING REGULATE NOCICEPTOR SENSITIVITY IN DROSOPHILA MELANOGASTER LARVAE
Review round: 2
Reviewer: 1

Output:
Basic reporting: There are still instances of interpretations this reviewer previously failed to point out in the Results section (eg lines 217-219).  This review is not even very comfortable with the Results headings that state conclusions.  Results is only facts and little/no interpretation.  The Discussion section should refer back to the Results and that is where you draw your conclusions.

About controls, great that all negative controls are presented, but some figures contain both Gal4-only and UAS-only and others in which the UAS-only is contained in Supplemental Figures 1,2.  Both negative controls should be placed alongside the experimental in each figure, so that readers can conveniently compare without having to flip back and forth between two separate figures.  Dispense with the Supplementary Figures, all that data is more clearly represented in the main body.

Where the authors have added description of comparison to UAS-only controls (for example Line 283, 285, 317 etc), in the previously-written text specify that you are describing comparison to Gal4-only controls.  In other words, in each sentence identify which controls you are describing.

Still not sure that Figure 1 A/B and C/D need to be separated.  This arrangement may mean something to the authors, but readers may miss that point and be confused about why they are presented separately.  The choice is the authors'/editors', but all these results focus on the same hypothesis.

Rather than saying in the Methods that these "lines were validated by the database", instead say that some but not all of the lines have been previously validated as described in the database, before going on to describe that validation, as was done.

This reviewer suggests that briefly including this analysis would be helpful:  "We also agree that data about normal expression of NorpA and Gαq in the mdIV would be valuable for the interpretation of our studies. We have used a publically available microarray dataset (ArrayExpress Accession # E-MTAB-3863) to show that NorpA and Gαq transcripts are detected in the mdIV neurons at levels comparable to transcripts of known mdIV genes (trio, painless, dTrpA1, Gr28b). We have omitted this analysis from the revised manuscript, but can include it if needed."

The authors provided explanation of the their thermal probe temperature verification, this should be included in Methods:   "The thermistor and thermometer used to measure temperature at the probe provides temperature information to a tenth of a degree. During experiments, the probe tip temperature is monitored before and after application of the stimulus. Trials in which the probe temperature deviates from the desired temperature by +/- 0.5°C are discarded during analysis."
Experimental design: pass
Validity of the findings: pass
Additional comments: Excellent revision.  My remaining concerns focus on presentation.


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: GΑQ AND PHOSPHOLIPASE CΒ SIGNALING REGULATE NOCICEPTOR SENSITIVITY IN DROSOPHILA MELANOGASTER LARVAE
Review round: 2
Reviewer: 2

Output:
Basic reporting: Same as the first review (Acceptable).
Experimental design: Same as the first review (Acceptable).
Validity of the findings: The authors have addressed my concerns in their revised manuscript.
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: EFFECT OF FLOODS ON THE Δ13C VALUES IN PLANT LEAVES: A STUDY OF WILLOWS IN NORTHEASTERN SIBERIA
Review round: 1
Reviewer: 1

Output:
Basic reporting: I recognize that this manuscript has a standard level of basic reporting.
Experimental design: I recognize that this manuscript has a very nice experimental design, although I feel that data set in this manuscript are relatively scarce or just minimum to conduct this study.
Validity of the findings: I recognize that the findings of this study is valuable and contributable to advances in the study of the related fields.
Additional comments: I am impressed with this manuscript. I recognized that this is a nice study, the demonstration here are valuable in that they impact a very general issue how we can interpret the hydrogel dynamics of the stable carbon isotopic composition of plant products, which is essential for accurate understanding of the ecology and evolution of plant vegetation in modern environments as well as in environmental changes from past to modern. To my knowledge, this manuscript will be the first publication, successfully to interpret the traditional hypothesis on the paradox frequently observed in plant carbon isotopic composition in wet-dry gradients.
As described in this manuscript, we have long studied the physiological response of plants to hydrogel dynamics, particularly for wet-dry gradients, with stable carbon, hydrogen, and oxygen isotopic compositions of plant products (cellulose, lipids, etc). This is because many scientists have simplistically believed that change in the stable isotopes of plant products is a single function of wet-dry gradients, so they have long neglected the other major factor, i.e., in addition to stoma closeness due to wet-dry gradients, photosynthetic activity can also influence much the change in the carbon isotope ratios of plants. It is also true that many scientists have well misunderstood, as hydrogen or oxygen isotope analysis of leaf water or plant cellulose is a unique solution for seeing the effect of stoma closeness on the carbon isotopes, independent of the degree of photosynthetic activity. However, in addition to increased in D/H or 18O/16O ratios due to evapotranspiration (which is closely related to wet-dry gradients), diversity in the water sources can also influence much the change in the oxygen isotope ratios of plants. So, to my knowledge, no study has long been conducted to see both effects of stoma closeness and photosynthetic activity in hydrogel dynamics. I thus recognize that this study used a very nice sample set successfully to see that plant carbon isotopic composition well responds diverse hydrological pressures, with respect to wet-dry gradients and its associated change of photosynthetic activity.
 I also feel that the manuscript is well organized into a readable story, therefore I suggest that this manuscript should be publishable in PeerJ. I am really looking forward to seeing the published paper of this study very soon.


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: EFFECT OF FLOODS ON THE Δ13C VALUES IN PLANT LEAVES: A STUDY OF WILLOWS IN NORTHEASTERN SIBERIA
Review round: 1
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: To Authors

This manuscript evaluated factors controlling the δ13C values of willow leaves in natural environments, especially under flooding and waterlogging conditions. I am really impressed this cutting-edge study.

It is true that we have usually interpreted the change in the δ13C values of plant leaves as the results of the block of CO2 input through stomata in dry conditions, compared to no-block in wet conditions. However, it is also very true that this interpretation should work only in a lot of assumptions, as the Authors well explained them in this manuscript. We thus have long suffered with ‘paradox’ in the interpretation of the δ13C values of plant leaves. Again, I recognized that this manuscript is nicely organized and well explain this ‘paradox’ on the change in the δ13C values of plant leaves, on the standard equation with balance between the CO2 input through stomata and the CO2 consumption attributable to photosynthesis activity. Moreover, this explanation is well verified with the new data from willow leaves under flooding and waterlogging conditions.
Although it is difficult that the most suitable place/samples for such experiments is found in nature environment, the Authors nicely found a riverside area where frequently floods and waterlogged, and leaves of willows, which are widely distribution around river, are likely record such various hydrological conditions. In Introduction, the Authors designed nice explanation of the relationship among the δ13C values, stomata conductance, and photosynthesis activity in plant leaves, which will be highly useful for readers of this manuscript for understanding that among these three factors in plant leaves.
I feel thus that this manuscript has a nice flow with high readability of all contents from Introduction to Discussion.
I can also recognize that the new findings in this study is essential for applying and interpreting of stable carbon isotopic composition of plant products, even in pot experiments as well as environments specific to floodplain with frequent change of water levels. Moreover, I think that advances in understanding the physiological mean on the isotopic compositions (including not only carbon but also other elements) of plant leaves in this study can contribute much how we can see the grow system, ecological function, and biosynthesis/metabolism of plants in future studies.
Based on these thought, I can recommend this manuscript to PeerJ, as a nice publication in there. However, I also feel that the Authors should be carefully reconsider three unclear points before publication (see specific comments below).

Specific comments:

1.  “Balance between A and gs” is the key effect on the δ13C values of plant leaves, for not only “LWL” but also “WL”. However, in the “WL” section, only gs is emphasized as the almost solo factor for increasing the δ13C values, but is neglecting the view of “balance between A and gs”. I thus worry about that such explanation leads readers toward misunderstanding of this key point. I suggest that the Authors modify the corresponding sentences/paragraph(s) accordingly to the “balance” that the gs has a much contribution compared to A in the case of plants under the “WL” conditions.

2.  Can you show the Figure 4 with the data of 2015 or 2016?
The δ13C data of plant leaves were found in willows collected from 2015 and 2016, but the A and gs data were collected in 2017. Also, although I can understand, many readers who are not familiar to such plant δ13C studies may have a common question why the Authors did not show the row values (but relative values to T=0 or PC) for the A and gs in Figure. 4.
I think that this manuscript already did sufficient explanation for the point of A/gs balance, even if the Author did not show Figure 4. However, on the other hand, I very much agree with the Authors’ intention that such physiological data, even in 2017, is important to see the physiology changes of willows under various water conditions in the studied area. Thus I suggest that the Figure 4 move to Appendix from Discussion, to enhance readability of this manuscript and to focus the changes in the δ13C value of plant leaves.
Also, please re-check carefully the following points in Figure 4:
  > The length of blue bars, especially the final date of flooding, on each of conditions.
  > Can the Authors show the specific hydrological condition (e.g., “WL”) for plants measured in Figure 4?

3. I think that the values for mean, cap-delta, standard deviation, etc., reported in this manuscript may be miscalculated for several places. Please re-check carefully for all.

L38: ca, use Italic, Subscript letter for “a”

L54-57: gs and gc, what is difference gs from gc?

L102: predominate

L137: Diameter

L152: 20 m

L163, 267, Table A2, and Figure 1(a): There are 29 sits in text, but 28 sites in Table A2. Also I cannot find 29 sites in Figure 1(a).

L181: S. boganidensis

L214-215: Use italic for S. richardsonii, S. glauca, and S. boganidensis

L237: SBoydom

L250-251: Figure 5

L257: －0.5‰

L309: SBoydom

L322: July 20 and more

L323: Figure 4b

L353: the δ13C

Fig.3: means±SD

Figs. 5 and 6: Please explain “a”, “b”, and “ab”


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: SPATIAL AND TEMPORAL VARIATIONS OF ARIDITY SHAPE DUNG BEETLE ASSEMBLAGES TOWARDS THE SAHARA DESERT
Review round: 1
Reviewer: 1

Output:
Basic reporting: Overall, the writing is good and I enjoyed the manuscript. I have made minor comments throughout. My major concern, however, is over the description of the statistics and analysis. I had great difficulty figuring out what was actually done, and why. I suspect that the analysis is fine, but I cannot properly judge at the moment given the lack of clarity in the methods and results sections. I have suggested improvements that would go some way to fixing this issue.

Line 56-58: OK, so in which ways can the response depend on regions and taxa? I think a couple of brief examples (i.e. "there was a positive/negative response to aridity in these taxa/regions") would help.

Line 72-76: I think you can be a little clearer here. You are saying that Mediterranean zones have hot, dry summers and cold, wet winters. Your next point is that there can still be considerable intra and interannual variation against this "typical" seasonal backdrop, right? At the moment it reads as if this variation is in contradiction to the hot/dry summers and cold/wet winters previously described. Perhaps emphasise that this variation is in addition to the broad seasonal pattern.

Line 74 and 79: You have repeated this exact sentence twice. Consider removing one?
"Importantly, in arid environments the availability of water is unevenly distributed through time, with large and unpredictable variations in rainfall between seasons and years (Ward, 2009)."

Lines 141-145: The explanation of the seasonal differences is very confusing. What are the numbers quoted? The differences between the wet and dry season at particular parts of the gradient? Must be made clearer: e.g "The difference between wet and dry season rainfall (measured as the difference between the wettest and dryest months) was X mm at the coast and Y mm inland."

Figure 1: So is the green-yellow-brown shading the aridity? Please state this in the legend. It should also have a bar showing what green means and what brown means. What are the units of aridity, for example?

Line 171-173: Were the traps separated by 20 m in a straight line? So 80 m separates the 1st and 5th trap? It is not clear if a straight line transect was used or some other design.
Experimental design: The practical methodology is fine and the research questions are well defined and stated in the introduction.

The statistical methods are quite confusing. Would it not be better to arrange them under subtitles (Q1, Q2, Q3) that match your questions and then to have the results presented in a similar way? This would allow these recurring threads to run through the manuscript, and the reader would have a much easier time figuring out which bit of analysis relates to which question.

It is also not clear what has been done with the beta diversity/community composition aspect of the analysis. Multisite indices have been used but in a pairwise fashion…? Why not just use the pairwise indices and use a multiple regression using distance matrices analysis (MRM) to test whether community similarity (measured as turnover or nestedness) was linked to similarity in aridity or any of the other environmental/spatial/temporal factors? MRM are extensions of Mantel tests. See Beaudrot and Marshall (2007, Journal of Animal Ecology, Vol. 80) for use of Mantel and partial Mantel tests. See the MRM function in the R package ecodist, and associated references, for an explanation of MRM techniques.

I am really struggling to understand what kinds of beta diversity have been calculated and how they have been compared. I think you need to break it down and talk the reader through step-by-step. Key to this is state what the unit of analysis is, or, to put it another way, to say what each data point in the corresponding graph would be. I think if you make this information more explicit the entire section would be much easier to read. These beta diversity metrics are tricky, and I cannot properly judge the analysis if I don't know which pairs/groups of sites are being compared to which.

In addition, later on during the environmental correlates section, it seems that point level beta diversity is used. Or, the beta diversity within/between replicates of a given site is used. Is this true? If so it is not clear at all.

There is also a conflation of the terms "species composition" and "beta diversity". In what ways are they different? I would stick to one of terms and use it consistently.
Validity of the findings: The data is high quality. My only reservation is that I cannot properly understand the analyses on beta diversity in the current format of the manuscript.
Additional comments: No other 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: SPATIAL AND TEMPORAL VARIATIONS OF ARIDITY SHAPE DUNG BEETLE ASSEMBLAGES TOWARDS THE SAHARA DESERT
Review round: 1
Reviewer: 2

Output:
Basic reporting: The document is clear, well written. The introduction introduces well the problem of the structure of dung beetles communities in semi-arid and arid environments, and the assumptions correspond to the problem of the variation of composition along a gradient of aridity. This study can be part of the broader context of an increase in aridity in the countries of North Africa (climate change).
Literature is relevant. However, it would be appropriate to add one reference that completes the subject (Pierre F., 1958). In the cited bibliography, there are also some modifications to make (spelling, name of the editor to complete ...). The list of changes to be made is given below.
Figures are correct. Tables are precise, but another supplementary file is needed (see below for details).
Experimental design: Research questions are relevant, well defined and meaningful. Investigations were performed with ethical standard. All authorizations to collect insects have been obtained from the administrative authorities of Morocco. Statistical analyzes are particularly efficient and satisfactorily used. Beetle collection methods are consistent with those used in similar works. However, it would be desirable that an additional table be provided (in a new supplementary file) giving in particular for each of the 10 inventoried sites their geographic coordinates, and the environmental conditions (in particular the type of soil, and the feces mostly available). This allows in particular to check the validity of some species determinations, such as that of Scarabaeus semipunctatus (cited from site mor. 4), south of the transect, whereas S. semipunctatus is in principle a species of coastal dunes, only in the sand (unless this site n°4 corresponds to the fossil shoreline of an old chott (a chott is a permanent salt water lake with shifting shorelines located in semi-arid regions). The imprecise location makes it impossible to validate this kind of taxonomic data.
Validity of the findings: The results remain interesting and are an important contribution to the knowledge of dung beetle communities in arid and desertic regions. The results and conclusions are well supported by the data analysis. Aridity determines the composition of beetle communities, by filtering species in both space and time. However it is not sure that aridity leads to a functional shift to generalist and saprophagous species. It is not sure the dung beetle species mentioned in Suppl. S2 are saprophagous species. They are dung feeders, and mentioned lines 413-415. In general, detritivorous Scarabaeidae feed on plant residues more or less in putrefaction, which is not compatible with the environmental conditions of semi-desertic sites. This explains it is very important to give the coordinates of the surveyed sites, with the main environmental variables.
Additional comments: The work gives a lot of new data on the organization of dung beetles communities. It is important because very little similar data exists.
However minor corrections are proposed to improve the manuscript..
Line 151: soil
Line 162: prepare a supplementary file on geographic coordinates, as explained previously.
Line 166: forêt
Lines 333-336: need of a short discussion (information) about the dung diversity in sampled sites (cattle vs sheep + other dung categories). The data provided (Appendix 3, fig 1) are too synthetic to provide useful information for understanding the organization of communities.
Line 399: Piera
Line 402: constraints
Lines 420-421: Comments: in dung beetles, the abundance of species depends on the trophic resources (dung) present at the moment of emergence of beetles. When the authors measured the dung density in the sites, did they verify that they counted only fresh or very recent excrements? In arid environments, excrement unused by dung beetles can remain intact for long months, which may overestimate the available trophic resource. What matters is the resource immediately available (see Van Vliet et al. (2009). Factors influencing duiker dung decay in north-east Gabon: are dung beetles hiding duikers? African Journal of Ecology 47(1): 40 – 47). Don’t forget also that often cattle receive in spring veterinary medicinal drugs at moments which can coincide with the time of reproduction of dung beetles. Another possibility: if cattle is scarce (feeding on remnants of crops), this can explain the loss of abundance of dung beetles.
Line 440: remark: it is also the case for Mendidius palmenticola (see Pierre F. (1958). Ecology et peuplement entomologique des sables vifs du Sahara Nord-occidental. Publication du Centre de Recherches Sahariennes, série Biologie, n°1. CNRS édit., Paris).
Line 480: add the reference Pierre, 1958.

References: some changes needed.
Line 642: Institut (with “t”)
Line 705: Revue d’Ecologie et de Biologie du Sol
Line 705: DOI ?? Complete the reference or delete “DOI”
Line 706: Lumaret, J.P.
Line 706: modify the organization of the reference, according the Journal recommendations. Add pagination: 95-115. In Dung beetle Ecology
Line 719; replace “Taylor & Francis” with Blackwell Science, Oxford, U.K.
Line 738: insert her the reference “Pierre, F (1958). See detail of the reference above.
Line 752: add: PhD thesis
Line 765: Gases*  (“*” ????). delete
Lines 775-776. Coleopterists Bulletin
Line 785; add; “PhD thesis”

Supplementary S2. Several additions and corrections are needed.
Under the first line “  wet season  - Dry season  “, insert the numbers of the 10 sites of the transect, in order to make reading easier of the data.

A correction of the spelling of the name Chilothorax is to be made (3 times for the list of 2013, and 3 times for the list of 2014)

Supplementary S3, Table 1
A correction of the spelling of the name Chilothorax is to be made (3 times)

Despite the changes and additions requested, which should improve the work, I consider that it is particularly interesting. The work is well written, the data collected is invaluable. A verification of the identity of a species is necessary (S. semipunctatus). If the determination is correct, it is a major biogeographical contribution for this species (it would be a relictual distribution, a reminder of an ancient period when the level of the Mediterranean Sea was higher than currently).

I suggest a conditional acceptance of the work, after correction and complements.


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: SPATIAL AND TEMPORAL VARIATIONS OF ARIDITY SHAPE DUNG BEETLE ASSEMBLAGES TOWARDS THE SAHARA DESERT
Review round: 2
Reviewer: 1

Output:
Basic reporting: Again, I enjoyed this manuscript. It is well written, thorough, and the authors have dealt with the comments from myself and the other reviewer well.
Experimental design: Again, this is great.
Validity of the findings: I think the findings are valid.
Additional comments: The manuscript is much improved following the reviews. I have just a few minor points to make. Perhaps just spell out what you mean even more clearly in the text in these few cases.

Line 58: "Diversity patterns of birds are opposite than those for scorpions". But the previous sentence says that scorpion diversity increases with aridity. in America but decreases in Australia. So what is the pattern for birds? Just say what it is without reference to the other taxa.

Line 223: "Significance levels were Bonferroni-corrected to account for multiple comparisons." Are the multiple comparisons you are referring to the temporal pseudoreplication? I.e. the same site is represented multiple times in the dataset as it was sampled in two years and two seasons?

Line 227: So this is Bray-Curtis between each site during each sampling period and every other, correct? Please state.

Multiple-site dissimilarities: so you have computed the multi-site beta among all sites of the gradient within a given year and season? Is this right?

Line 258: This is confusing because I thought you had already described a comparison between seasons and years for each site in line 230 with a PERMANOVA? In which case, what are you describing in line 230? This is still not much clearer from the first version of the manuscript. State what you want to gain from this analysis and the one in line 230.


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: SPATIAL AND TEMPORAL VARIATIONS OF ARIDITY SHAPE DUNG BEETLE ASSEMBLAGES TOWARDS THE SAHARA DESERT
Review round: 2
Reviewer: 2

Output:
Basic reporting: The authors took into account the comments and remarks of reviewers. The answers given to the various points are satisfactory and reflect a real reflection.
I suggest that the revised version be accepted
Experimental design: Modified and completed
Validity of the findings: OK
Additional comments: Your comments are relevant


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: INFLAMMATION-BASED PROGNOSTIC SCORES PREDICT THE PROGNOSIS OF LOCALLY ADVANCED CERVICAL ESOPHAGEAL SQUAMOUS CELL CARCINOMA PATIENTS RECEIVING CURATIVE CONCURRENT CHEMORADIOTHERAPY: A PROPENSITY SCORE-MATCHED ANALYSIS
Review round: 1
Reviewer: 1

Output:
Basic reporting: In this study, the authors aim to determine the clinical impact of inflammation-based prognostic scores in locally advanced cervical esophageal squamous cell carcinoma (ESCC) patients who have undergone curative CCRT. Patient data were collected retrospectively in the Kaohsiung Chang Gung Memorial Hospital from January 2005 and December 2015. This study may be interesting for oncologists who are mainly interested in ESCC. The ethical approval and consent to participate are available in the manuscript. However, the paper needs additional works, and some minor changes are recommended before considering the paper for publication.
Experimental design: I also attached the Turnitin report for plagiarism check. The similarity index at the 33rd page of the Turnitin Originality Report was 40%, and this value exceeded acceptable level range between 15%-20%. Authors must be careful about citing papers appropriately in their study.
Validity of the findings: My concerns are as follows:

In abstract,

•	In Line 38-42: Please give details for statistical methods in methods section of the abstract.
•	In Line 43: Please correct “(N=0.013)” as “(P=0.013)”.

In introduction,

•	In Line 67: I think the reference for this sentence is missing.

In material and methods,

•	In Line 135 and 137: The reference of (Edge S) should be corrected as (Edge S et al. 2010).

In results,

•	In Line 217: Please correct “(N=0.013)” as “(P=0.013)”.
•	In Line 216: Table 2 should be refereed in line 216.

In references,

•	In Line 375: This reference was not cited in the manuscript.

In Table 2 and 3,

•	Please write the phrase “*Statistically significant” in the footnotes of the tables (same as Table 1).
•	To be consistent, please use 2 or 3 digit for decimals of the p-values (P value 0.047 or 0.04).

In Figure 2,
•	To be consistent, please use 2 or 3 digit for decimals of the p-values (P value 0.010 or 0.01).
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: INFLAMMATION-BASED PROGNOSTIC SCORES PREDICT THE PROGNOSIS OF LOCALLY ADVANCED CERVICAL ESOPHAGEAL SQUAMOUS CELL CARCINOMA PATIENTS RECEIVING CURATIVE CONCURRENT CHEMORADIOTHERAPY: A PROPENSITY SCORE-MATCHED ANALYSIS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Minor language editing is required in the Dsicussion and Conclusions sections.
Experimental design: No Comment
Validity of the findings: No comment
Additional comments: The study population was overwhelmingly male. Was this particularly chosen in order to match the cervical and thoracic ESCC patients, or is it because more men are affected by ESCC than female? A couple of sentences in the Discussion explaining whether there is a bias in the data due to an overwhelming male study cohort would be beneficial.


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: INFLAMMATION-BASED PROGNOSTIC SCORES PREDICT THE PROGNOSIS OF LOCALLY ADVANCED CERVICAL ESOPHAGEAL SQUAMOUS CELL CARCINOMA PATIENTS RECEIVING CURATIVE CONCURRENT CHEMORADIOTHERAPY: A PROPENSITY SCORE-MATCHED ANALYSIS
Review round: 1
Reviewer: 3

Output:
Basic reporting: English editing should be done again, because grammatical errors and typos are seen.
Experimental design: Fair
Validity of the findings: Fair
Additional comments: This manuscript by Chia-Che Wu et Al. is a retrospective study to identify the prognostic signiﬁcance of inﬂammatory biomarkers on patients with cervical esophageal squamous cell carcinoma, a relatively rare disease. The result shows many easily assessable biomarkers which relate to worse survival of these patients. There are points in which this study can be adjusted to be more beneﬁcial.

1. The reference pattern is not standard. Please follow the journal instructions.

2. Your introduction, in line 76-77, is not quite accurate, when standard protocol to date stated clearly on which patients with cervical esophageal squamous cell carcinoma are indicated for surgery.

3. In line 135-137, 205, 289, The sentences are incorrect.

4. The eligibility criteria may need to be clariﬁed when ﬁrst criteria is the patients included are stage III. Firstly, according to 8th AJCC Cancer Staging Manual, T4 tumors are classiﬁed into stage IV. According to your data, the majority of patients included had T4 tumor stage.
Secondly, squamous cell type should be included in the criteria.

5. Other parameters that concern survival should be shown, such as ECOG status and underlying diseases, since they are confounders to the study outcome.

6. These biomarkers are easy-to-measure and can be very helpful if the comparative group are diﬀerent treatment modalities.

7. The cut-oﬀ values of each biomarkers should be calculated because the cut-oﬀ values depend on speciﬁc populations.

8. The conclusion should be based on results of the analysis. By concluding all biomarkers as a predictor for cervical esophageal squamous cell carcinoma is misleading.


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: INFLAMMATION-BASED PROGNOSTIC SCORES PREDICT THE PROGNOSIS OF LOCALLY ADVANCED CERVICAL ESOPHAGEAL SQUAMOUS CELL CARCINOMA PATIENTS RECEIVING CURATIVE CONCURRENT CHEMORADIOTHERAPY: A PROPENSITY SCORE-MATCHED ANALYSIS
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: From the changes made in the revised manuscript and responses provided, this manuscript may be accepted.


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: INFLAMMATION-BASED PROGNOSTIC SCORES PREDICT THE PROGNOSIS OF LOCALLY ADVANCED CERVICAL ESOPHAGEAL SQUAMOUS CELL CARCINOMA PATIENTS RECEIVING CURATIVE CONCURRENT CHEMORADIOTHERAPY: A PROPENSITY SCORE-MATCHED ANALYSIS
Review round: 2
Reviewer: 2

Output:
Basic reporting: No further comments/suggestions.
Experimental design: No further comments/suggestions.
Validity of the findings: No further comments/suggestions.
Additional comments: All concerns raised during the evaluation process 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: INFLAMMATION-BASED PROGNOSTIC SCORES PREDICT THE PROGNOSIS OF LOCALLY ADVANCED CERVICAL ESOPHAGEAL SQUAMOUS CELL CARCINOMA PATIENTS RECEIVING CURATIVE CONCURRENT CHEMORADIOTHERAPY: A PROPENSITY SCORE-MATCHED ANALYSIS
Review round: 2
Reviewer: 3

Output:
Basic reporting: Good to be enough
Experimental design: Good to be enough
Validity of the findings: Good to be enough
Additional comments: Authors approximately revised the manuscript and now, this manuscript has a value for publication.


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: DISCOVERY OF TWO SKIN-DERIVED DERMASEPTINS AND DESIGN OF A TAT-FUSION ANALOGUE WITH BROAD-SPECTRUM ANTIMICROBIAL ACTIVITY AND LOW CYTOTOXICITY ON HEALTHY CELLS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The paper is written in clear English and well-structured. Figures are of good quality.
Some typos that were found:
1. Page 1, line 30: "...system, which..."
2. Page 2, line 31: "...[2-3]. "
3. Page 3, line 82: remove "structurally determined" and write analyzed/identified. (HPLC and MS gives no indication about structure within this setup.)
4. Page 8, line 207: remove "that"
5. Page 9, line 259: insert "is" before "generally"
6. Table 2:write "Horse Erythrocytes"?
Experimental design: The experimental design is well-thought-out. Reserach question is well defined and meaningful. Methods are described with sufficient detail. However, within the caption to Figure 4, the authors should again give the reference to the software, with which they have created the helical wheel projections.
Validity of the findings: The presented data is robust and controlled.
Additional comments: I have some more remarks and comments to this work:
1. The authors should give a more detailed discussion about the possible intracellular targets of DP-2 and how they could identify them.
2. Line 194: Possibly the activity of DP-1 is much lower due to its smaller size/shorter sequence? As can be seen from the CD, DP-1 might not be able to form an adequate helix for membrane interaction?
3. Line 204: The authors should discuss why they observed reduced cytotoxicity against HUVEC when using DRS-DU1. The higher activity of DP-2 is possibly only a matter of increased positive charges?
4. Line 235. During the last years, resistancies also against AMPs have emerged. The authors should include at least one statement.


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: DISCOVERY OF TWO SKIN-DERIVED DERMASEPTINS AND DESIGN OF A TAT-FUSION ANALOGUE WITH BROAD-SPECTRUM ANTIMICROBIAL ACTIVITY AND LOW CYTOTOXICITY ON HEALTHY CELLS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The article is quite clearly written but the backgound to the study is not adequately presented. There is an extensive literature on the biological properties of the dermaseptins from multiple species including antimicrobial activity and cytotoxicity to tumor cells that should be reviewed for the reader. The relevant results do not support the claim that the peptides are anticancer (see General Comments).
Experimental design: The topic of the research is within the scope of the journal and the experiments appear to have been performed to a satisfactory technical standard. A serious  limitation of the study is that no attempt has been made to show that the dermaseptins are actually produced by the frogs and have the structures predicted from the nucleotide sequences of cDNAs
The frogs in question presumably synthesize a wide range of host-defense peptide including not only dermaseptins but also phylloseptins, dermatoxins, and others. The study has been submitted for publication at a too preliminary stage and would be improved enormously if a comprehensive account of the full range of peptides produced by these species were provided rather than just two peptides whose selection for publication is not explained.In its present form, the article does not fill an identified knowledge gap.
Predictions of secondary structure are not of great value. As the authors have performed CD measurements, the data should be analyzed quantitatively to determine % helicity.
.
Validity of the findings: The validity of the findings are called into question by the fact that no attempt has been made to confirm the identity of the frogs or to state where they were collected. It is simply stated that they were provided by a commercial supplier. The reader must be certain that the animals used really are the species that they are claimed to be.
In order to justify the claim that the dermaseptins are active against drug-resistant bacteria, MIC values against a wider ranger of clinical isolates whose resistance profile is fully characterized are needed.The present study involves the use of a single NCTC strain.
As regards potential as "anticancer" agents, the authors should compare the cytotoxicities against tumor cells of their peptides with those of other dermaseptins previously described.
Although the authors claim that the properties of the conjugate are "significantly better" than the native peptide, no statistical analysis is presented.
Additional comments: The authors are not justified in using the term anticancer. For an agent to be described as anticancer it must produce tumor shrinkage in humans. To use the term antitumor, the agent must produce tumor shrinkage in an animal model. The authors has shown only that the dermaseptins are cytotoxic to tumor cells in vitro.
Phllomedusa duellmani has now been reclassified as Callimedusa duellmani. and should be referred to as such.


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: DISCOVERY OF TWO SKIN-DERIVED DERMASEPTINS AND DESIGN OF A TAT-FUSION ANALOGUE WITH BROAD-SPECTRUM ANTIMICROBIAL ACTIVITY AND LOW CYTOTOXICITY ON HEALTHY CELLS
Review round: 1
Reviewer: 3

Output:
Basic reporting: The manuscript submitted by Zhu et al. describes the identification of two novel dermaseptins from two different cDNA libraries from two species of Phyllomedusa frogs. In addition, the authors report on the antimicrobial, hemolytic and anticancer properties of the natural peptides. By creating structural analogs of DRS-DU-1, the authors confirm the essential role of the N-terminal part of the peptide for the biological activity, as well as design a TAT-fusion N-terminus-truncated version with enhanced anticancer activity. The later serves as an example of strategy that can be used in designing novel antimicrobial and anticancer therapeutic agents that lack hemolytic activity.
The manuscript can be accepted for publication. However, the authors need to  respond to the following comments before the paper is published:
1.	I would strongly encourage the authors to think about modifying the title of the paper. The way it is written now, it is not clear and doesn’t provide enough information about the content of the paper.
2.	The article overall is written in clear and unambiguous English language. However, there are some issues that need to be addressed: typos with the name of the peptides – dermaspetin (example l. 165, 233); the names of the frogs should be given as P. camba and P. duellmani throughout the text after the first time they appear in full.
Experimental design: 3. The experimental design is straightforward, and the research questions are well stated.
4. Even though the information included in the Introduction is enough to justify the antimicrobial part of the work, it doesn’t familiarize the reader about the reasons for studying the anticancer effect of the peptides and their analogs on various tumor cell lines. More information needs to be included to show context.
Validity of the findings: In my opinion, the study is technically sound and the conclusions are supported by the results. It is important that the authors discuss their findings comparing them to reports by others on the antimicrobial, hemolytic and anticancer activity of dermaseptins. This peptide family is actively researched and numerous publications are available in the public domain.
Additional comments: 5.	In the Acknowledgements – l. 272 – 275 – the sentence is not clear.
6.	It is not clear to the reviewer why the sequence in Table 1 for DRS-DU-1 is given as ALWKSLL… and for the two analogs is different, e.g. ALWSKLL… for DP-1 and TAT-GALWSKLL… for DP-2 respectively. Is it a typo? KSLL, and SKLL? As it should be the same sequence, please clarify which one is the correct one.
7.	There is a typo in Table 2 – hourse ethrycytos? Needs to be corrected. In addition, it is important to add the strains of the microorganisms used as listed in the Materials and methods section, or alternatively the title of the column should be modified.
8.	 The authors need to define either in the Materials and methods section, or when describing the results what is therapeutic indices (TI), HC50 and IC50. The text to Table 3 – starting with “half maximal inhibitory concentrations (IC50) needs to be modidfied. It is not a proper scientific description.
9.	The text to Fig. 1 contains “single-underlined” – perhaps it is a typo and needs to be modified.
10.	In Fig. 2 are included sequences of other dermaseptins with their abbreviations. However, the authors must specify in the Figure text the names of the frog species these dermaseptins have been isolated from, e.g. DRS-PS1, DRS-H2, DRS-B4.
11.	The text to Fig. 3 contains “membrane-mimic” – perhaps it is a typo and needs to be modified. The usage of proper terminology is encouraged.

I would be happy to review the revised manuscript.