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: SPECIES TURNOVER REVEALS HIDDEN EFFECTS OF DECREASING NITROGEN DEPOSITION IN MOUNTAIN HAY MEADOWS
Review round: 1
Reviewer: 1

Output:
Basic reporting: This study tests the hypothesis that decreasing nitrogen deposition over 14 years causes changes in plant community composition and rates of species turnover. Because the climate has also been warming and some sites experienced land use change, they also tested effects of temperature, precipitation, slope (inclination) and light in addition to nitrogen.
Experimental design: The researchers used plant species data from the Swiss Biodiversity Monitoring program and assigned them Ellenberg indicator values.  The community mean indicator values were subjected to statistical linear mixed models to relate to environmental parameters and to assess species turnover rates.
Validity of the findings: Both declines in nitrogen and increases in temperature were important in driving changes in community composition over time, and somewhat counterbalanced each other.
Overall I found the approach solid and the conclusions well-supported by the data and analyses. I have some questions and suggestions for clarification of some points.
Additional comments: A total of 129 plots were selected based on their location in hay meadows. How far apart were the plots? It would be helpful to have a map with plot locations across the country, perhaps in the appendix.
Changes in N deposition over time are shown in Fig. 1. Since temperature was such an important driver, it would be useful to present changes in temperature over time. This could be reported in the text, if a figure is not of interest.

No information is presented on plant species composition.  What are richness values per plot, and ranges of richness? No plant species names are given, and are not expected in such a diverse assemblage. However, to help the interested reader understand the species composition, the authors should refer to publication(s) that describe the vegetation and species composition of their sample sites.

The term “humidity” is used throughout to refer to the effects of precipitation on soil moisture. However, in English, humidity commonly refers to atmospheric humidity. I recommend substituting “soil moisture” or just “moisture” for humidity throughout the manuscript.

104 “community mean of indicator values”
It would be helpful to explain briefly how these indicator values are determined. Non-European readers may not be familiar with Ellenberg indicator values.

The results from plots with low N deposition are important to the conclusions and interpretations, but data for sites with low N deposition is not presented. In line 227 you state: “the higher colonization rate of species with low nutrient value at the few sites with low N deposition rate seems to affect the spatial pattern of oligotrophic species richness”
However,  Fig. 3 only shows mean values for all sites. Is there a way you could show data from low N deposition sites, to support your statement on line 227?
Conclusions: 313 “where some key information is still missing”
What information is still missing?

Additional suggestions for editorial changes:

line 17 “with an according decrease in N deposition”
CHANGE TO
with a consequent decrease in N deposition

18 “Swiss biodiversity monitoring.”
Monitoring is an adjective in this usage and needs a noun to modify.
CHANGE TO
Swiss biodiversity monitoring program (as in l. 90)

22 “plant community structure”
CHANGE TO
“plant community composition” to be consistent with the rest of the manuscript.

Introduction
41 “with an according decrease in N deposition”
CHANGE TO
with a consequent decrease in N deposition

62 “if colonization and local extinction is compared”
CHANGE TO
if colonization and local extinction are compared

71 “are threatened also”
CHANGE TO
are also threatened

74 “likely to to interact”
CHANGE TO
likely to interact

77 “the shift of plant communities at mountain summits are”
CHANGE TO
the shift of plant communities at mountain summits is

82 “Swiss biodiversity monitoring”
CHANGE TO
Swiss biodiversity monitoring program

101 “These selection criteria yielded a sample of 129 sites.”
CHANGE TO
These selection criteria yielded 129 sites that had been sampled three times during 2003-2017 (is my interpretation correct?)

118 “we expected communities to response”
CHANGE TO
we expected communities to respond

194 “were less conclusive to explain the variation”
CHANGE TO
 were less conclusive in explaining the variation

Table 3
(a)	Plants that disappeard
CHANGE TO
(a)	Plants that disappeared

The wording is unclear in this sentence:
208 “the differences between colonizing species and random colonization was about four times smaller than the difference in the indicator value for nutrients between colonizing species and random species.”
IS THIS INTERPRETATION CORRECT?
….the differences between RICHNESS OF colonizing species and random colonization was about four times smaller than the difference in the indicator value for nutrients between colonizing species and random species.

212” replacement of species with lower temperature value with species with higher temperature values.”
CHANGE TO
replacement of species with lower temperature value by species with higher temperature values.

227 “the higher colonization rate of species with low nutrient value at the few sites with low N deposition rate seems to affect the spatial pattern of oligotrophic species richness”
Data for sites with low N deposition is not presented. Fig. 3 shows mean values for all sites. Is there a way you could show data from low N deposition sites, to support your statement on line 227?

265” how N deposition is affecting disappearing and colonization”
CHANGE TO
how N deposition is affecting disappearance and colonization


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: SPECIES TURNOVER REVEALS HIDDEN EFFECTS OF DECREASING NITROGEN DEPOSITION IN MOUNTAIN HAY MEADOWS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The basic reporting is appropriate, only a few issues to mention:

Line 46-49: A third major factor is dispersal limitation. The authors should discuss either (a) why this is not an issue for the Swiss mountain hay meadows, or (b) include it in their assessment.

Figure 3 needs to be fixed. We can’t see the black line behind the confidence interval, and it’s not clear what this is telling us.
Experimental design: The experimental design and methodology are robust, but there were a few areas that could be clarified more and/or elaborated upon:

Line 105-106: There’s a lot that has to be taken on faith with respect to the indicator values from Landolt et al. (2010). This paper needs to stand on its own, and so these indicator values need to be summarized somehow and/or a table in the appendix provided on their values for different species. If it’s based on Ellenberg, I’ve seen many papers try to extract meaning from Ellenberg values in the past, most fail, and I wish the European ecologists would update that resource. That being said, this is one of the most successful efforts (if Landolt 2010 is based on Ellenberg 1992) I’ve seen in extracting meaning from those indicators, which is another testament to the strength of the analytical approach.

Line 114: Please provide a map of the sites and a table of their environmental values. That is critical background information that is lacking.
Validity of the findings: The validity of the findings is also solid, but could be tightened a little more in a few places:

Line 125-126: The average N deposition in the sites (14.84 kg N ha-1 yr-1) is still pretty high, and didn’t decline all that much in the 15 years, which also likely explains some of why you’re not seeing a large effect. It’ll be interesting to resample these sites in another 15 years, or to add more sites that have changed more. This should be discussed a little more.

Line 187: Interesting that you had 29% difference in the replicate plots assessed by different botanists, that seems quite big to me if the “signal” is 36-38% difference in the survey plots. There’s not much that can be done about this, and it’s very insightful to check, but some greater discussion on why the variation among replicate plots is so high is warranted.

Line 193: You found the “highest species turnover at sites with low N deposition.” That made me wonder, are these sites ones that used to have higher deposition and low are lower (and thus would be indicative of recovery) or sites that always had low N deposition (which would not be recovery). From Figure 1 it looks like these sites never had high N, so there may be something else driving these patterns other than N deposition? Some greater discussion of this possibility is needed.

Do you have any soil measurements that you can see if soil N mineralization or some over measure of soil N availability changed? Seems that is a key missing factor in the analysis. You’re assuming that N dep is a surrogate for N availability, which is may not be after decades of N deposition build up N stores in the soil. If that data is available, please include, if it isn’t, please state that.

It is a little unclear from the methods whether the “colonizers” needed to persist, or whether the species lost needed to not return? This is kind of important because otherwise you’re really just reporting on the seed rain (for colonizers), as colonizers need to persist to matter, and reporting on botanical skill (for those “lost”).

Figure 2: Very cool results!! Impressive that you were able to tease this apart. That being said, I would not call this a “critical load.” A critical load, according to the formal definition, is the level below which bad stuff doesn’t happen. I would not say that once the colonization probability of oligotrophic and eutrophic species are equal qualifies. This is a “threshold” to me. The critical load would be the point, if you had a saturating logarithmic response, where the colonization probability of eutrophic species began to increase, or where the colonization probability of oligotrophic species began to decrease. It’s not where they are equal, though where they are equal is a useful threshold to bring up.
Additional comments: Summary of comments
In this manuscript entitled “Species turnover reveals hidden effects of decreasing Nitrogen deposition in mountain hay meadows,” Roth et al. use a very insightful analytical approach to try and tease out the shift in plant community composition in Swiss mountain hay meadows over a 15 year period. They find that increasing temperature and decreasing nitrogen (N) deposition are having detectable effects on rates of colonization and local extirpation in the community, but they are subtle and often inconclusive. This is a nice (albeit small) study whose main contribution is in the approach (i.e. Bayesian analysis on colonization and extirpation relative to random), rather than in the finding (i.e. species with low N scores are more likely to be gained and lost, species with higher temp scores are preferentially gained and those with lower temp scores are preferentially lost). The approach is very novel and powerful, and I look forward to seeing it replicated with a larger dataset. I have no major objections to the paper, but would have liked to see more sites and a wider geographic gradient to see how robust the results are outside of this small eco-type (i.e. Swiss mountain meadows).

I had no major comments, and consider the above comments as moderate, to improve the quality and clarity of the paper. Minor comments are below:

Line 45: Probably good to give the formal definition of the CL here from Nilsson et al. (1988) or Bobbink et al. (2010).

Line 76: “say’ is too colloquial.

Line 78: Include some discussion of fire (i.e. it does not happen?) since that is also a very important factor in grasslands.

Table 1: Seems odd that such small changes can be significant. For example, light went from 3.56 to 3.55, and you found a 93% chance that this is a real trend. That seems a little questionable.

Line 156-167: This analytical method is very difficult to follow, please clarify.

Line 187: Clarify that “replicated surveys” are where you had different botanists measure the sites, replicates can have multiple meanings here (e.g. replicate plots measured by the same person). These are “validation plots.”

Line 201-206: Very interesting results. New colonizers are adapted to low N and are different from the extant community, species lost are also adapted to low N conditions. Interesting that you were able to detect this!

Line 235-236: That you did not detect a shift is not surprising if these are perennial species (are they?) Some of these grasses could live for years and thus a shift may not be expected when the reductions in N deposition are this small.

Line 254-256: This is a bit of an overstatement, please water down a bit.

Line 257: Compare the reduction nin N dep (-2.7 kg ha-1 yr-1) with the interannual variation, this is probably within the interannual variation and thus is not a large enough reduction to detect more definitive changes. That being said, you did detect some, which again bespeaks the strong analytical approach.

Line 266-267: These results sort of makes sense, N dep is coming down (favoring those with lower N scores), but it's still high relative to historical levels (so you're still going to lose species adapted to low N conditions).

Line 289-290: It’s unclear to me which “space-for-time” substitution you’re comparing your results to. Is it Rowe et al. (2017)? Whatever it is, please cite it in this sentence, and put your number next to theirs for easy comparison.

Line 293: Please identify what the “same model as in Roth et al. (2017)” is.

Line 309: Please re-word, “re-transferring mountain hay meadows,” I don’t know what you mean by re-transferring here.

Line 311-312: “However…instead of species turnover.” This is kind of an unsubstantiated claim, either reword to make it a hypothesis (i.e. water it down), or back it up.


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: DIGGING FOR DNA AT DEPTH: RAPID UNIVERSAL METABARCODING SURVEYS (RUMS) AS A TOOL TO DETECT CORAL REEF BIODIVERSITY ACROSS A DEPTH GRADIENT
Review round: 1
Reviewer: 1

Output:
Basic reporting: The English used throughout the manuscript is clear and unambiguous. There are small points which require attention. See below.

Line 87 -88 – Two sets of brackets present which could be combined together I think.

Line 97 – 99 – While the authors are correct with their quotation Taberlet et al 2018 in his recent book (“Environmental DNA: For Biodiversity Research and Monitoring”) have established a more comprehensive definition of eDNA that I believe should at least be considered by the authors although their current definition would just fall into the extracellular eDNA classification.

Line 104: This is where I believe the clear definition of eDNA is required as eDNA samples targeting protists will have an obvious sign of biological material (even if a microscope is required) and thus would not in a strict sense be included in your classification of eDNA. While personally I do not disagree with the authors about the inclusion of the protists studies as examples of eDNA I think that the definition just has to be clarified.

L113: Should include that this is partially due to the lack of barcoded reference organisms in particular.

L139: I believe as this is the first time as far as I can see you use the acronym RUMS in the main text, you require the word rapid before universal metabarcoding surveys

Line 223: do not require the word those

Line 233 – 238: Could you please shorten the sentence somewhat.

Line 340: Delete one of the “that” and replace with the

Line 343: what is the 1m in the brackets for.

Figure 1: While the figure is easy to understand I have a small issue with the arrows and the one for light especially. It has the shading at the surface and getting lighter with depth. I admit this is just a personal opinion but to me it would be more logical to be light at the surface and get darker with depth as happens in the water column. If they authors did this to match the other two arrows (nutrients and temperature) then maybe using different colours would improve …e.g. shades of blue for light and red for temperature.

Figure 2: The contrast colors – what are the segments within other – is it just smaller phyla?
Experimental design: Line 161: How was the sediment exactly obtained. Was it just scooped up with the falcon tube?

Line 170: I am slightly confused with the 4 replicate samples. On line 161 you mention 2 replicates. Could you please just clarify this.

Line 179: Please see previous comment about replicates. If the number of replicates per site/depth was two of such a small amount of sediment I would be dubious about the reliability of the results. If it is 4 replicates this is better.

L249: What were the BLASTn settings used?

Line 272: What packages with R were used?
Validity of the findings: Line 360: Indeed multiple primers can detect higher diversity but Pearman et al 2018 showed that similar patterns were found using two different primer sets. So it depends on what the aims of the study are. If you just want to find all species then multiple primers would be necessary but in this study if you just wanted to detect changes then maybe only one primer is required. This should be taken into account especial when discussing time and money later on
Additional comments: This is generally a well written article examining the use of eDNA to detect differences in diversity along a depth gradient in two coral reefs in Japan. The study appears robust with just a few clarifications required in the methods section to clarify some of the methodologies undertaken.


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: DIGGING FOR DNA AT DEPTH: RAPID UNIVERSAL METABARCODING SURVEYS (RUMS) AS A TOOL TO DETECT CORAL REEF BIODIVERSITY ACROSS A DEPTH GRADIENT
Review round: 1
Reviewer: 2

Output:
Basic reporting: The writing and grammar are fine. References seem in order for the field of marine eDNA, though there is a lack of discussion/referencing for expected marine ecology. Figures are professional, however the statistical analysis should be treated with caution, especially when comparing between sites due to the experimental design and extraction methods.
Experimental design: The findings are a bit of pilot data that should be treated as such. Overall, the data sampling is unbalanced and lacks spatial structure. Compounded with single 0.5 gram eDNA extractions the data derived from the samples should be interpreted with caution due to the random error associated with the experimental design. In general, drop the statistical analyses comparing between sites and report the overall diversity with some discussion to the expected diversity in the system. Drawing too much from beta-diversity measures is likely to be misleading.
Validity of the findings: see section 2
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: DIGGING FOR DNA AT DEPTH: RAPID UNIVERSAL METABARCODING SURVEYS (RUMS) AS A TOOL TO DETECT CORAL REEF BIODIVERSITY ACROSS A DEPTH GRADIENT
Review round: 2
Reviewer: 1

Output:
Basic reporting: The paper is well written
Experimental design: The authors have addressed the issues that I had previously pointed out
Validity of the findings: no comment
Additional comments: No additional comments


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

Input:
Title: GENETIC ALTERATION OF HISTONE LYSINE METHYLTRANSFERASES AND THEIR SIGNIFICANCE IN RENAL CELL CARCINOMA
Review round: 1
Reviewer: 1

Output:
Basic reporting: 1.	The authors provided an adequate introduction, but the discussion could be improved by adding more literature on the HMTs with genetic alterations.
2.	English need to be improved to remove ambiguous meanings. For instance, in the sentences starting in row 50, 56, 113, 124.
3.	Several sentences reporting the results miss the reference to a specific figure (i.e. row 122, 127, 143) so it is difficult to follow the manuscript.
4.	The figure 6, relative to the MTS assay, in the paragraph starting in row 219 is missing.
5.	In row 122 the author mentioned SETMAR gene that is absent from figure 1b.
6.	In several figure panels, such as all panels in fig.6, the Pvalue is missing (also NEs in GSEA analysis).
7.	In Fig2 a clustering analysis would be more informative.
8.	In fig.2: are MECOM and PRDM16 rally differentially expressed between ccRCC and non-ccRCC?
9.	It is not evident why the data in Fig.6 are consistent with the computational analysis. Please explain.
10.	In fig.4 the interpretation of panel A is not clear.
Experimental design: The rational of the study is well defined.
The methods should contain more details of the performed analysis. It should be clearer in both methods and figure/table legends which and how many samples in each group are used in all the analysis.
Validity of the findings: The authors should control their statistical findings for the different sample size of the cohorts.
Additional comments: 1)	The authors integrated TGCA data (mutations, copy number variation, expression level and clinical outcome) of 50 HMT in renal cell carcinoma. The authors indicated, in several sentences, that their integrated analysis suggest a role of some HMTs in renal cell carcinoma development and progression. However, their analysis could suggest a possible general role in renal cell carcinoma biology. To support their claim, they could assess tumor heterogeneity in term of clonal evolution combining all molecular evidences (i.e. somatic mutations, CNV and expression).
2)	The manuscript needs a lot of improvement in term of details (methods, figures, figure legends) that are missing; an entire figure on MTS assay is missing although the results are reported in the text.
3)	The authors didn’t show properly the “significance” of HMTs in RCC as claimed in the title. To start understanding the functional role, they could perform knockdown of some of the 12 (or 11?) HMTs and perform some cellular assays.


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: GENETIC ALTERATION OF HISTONE LYSINE METHYLTRANSFERASES AND THEIR SIGNIFICANCE IN RENAL CELL CARCINOMA
Review round: 1
Reviewer: 2

Output:
Basic reporting: The fonts in the graphs is very variable. It has to be uniform and legible. In some of the later graphs (figure 6 and others), the font is not legible.
Experimental design: The authors have analyzed the published TCGA with a focus on HMT's. But they have made very little effort to prove the validity of their findings experimentally. This weakens the manuscript. The authors analyzed the data from TCGA downloading the data from CBIOPORTAL. The authors did not make an effort to correlate their findings performing invitro experiments other than the mRNA expression analysis.

The p values/statistical significance values should be incorporated in the figures as well to make sure if the analysis is significant.
Validity of the findings: Validity in findings is the weakest. The analysis of gains/amplifications/deletions is reported very nicely. The GSEA analysis including the expression in patient samples is very detailed. The authors mention to have performed migration/invasion assays and EdU assay and mention the results as shown in Figure 6, while Figure 6 is showing mRNA expression data. I think it is better for the manuscript to have significance if the results are incorporated in the figures appropriately.
Additional comments: The authors made a detailed computational analysis of the various HMT's that are deregulated in Renal Cell carcinoma (RCC).

The authors utilized the data that could be downloaded from CBIOPORTAL and the patient sample in TCGA data set is significant.

The authors need to strengthen their analysis with invitro analysis including the contribution of the major HMT's identified including SETD2. Minimal experiments which the authors mentioned in the text such as results obtained from invasion and EdU assays should be incorporated in the manuscript.

The RNA expression analysis could be expanded to few additional cell lines to strengthen their findings or refer to previous studies if published.

The GSEA analysis revealed pathways involved in proliferation. Are there any common genes that are correlating between the GO/GSEA/pathway analysis. If so they should be tested in the cell lines utilized for gene expression of HMT's.

figure 6 was wrongly indicated in the text, please correct it.

In the survival analysis, Please indicate the n for each condition,


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: GENETIC ALTERATION OF HISTONE LYSINE METHYLTRANSFERASES AND THEIR SIGNIFICANCE IN RENAL CELL CARCINOMA
Review round: 2
Reviewer: 1

Output:
Basic reporting: English can still be improved.

References are ok.

Figures could be improved.
Experimental design: Research question is well define.

it is not clear if the experiments have been reproduced multiple times.

Methods are described with sufficient details.
Validity of the findings: Most of the statistics are now present in the manuscript.
Additional comments: The authors improved the manuscript in term of discussion, details, English, statistics and methods. They also added the figures relative to some functional analysis (proliferation, migration, invasion) on SETD2 and EZH2.
Since they did not analyze the function of the other “critical” HMTs, the title and the abstract should be more specific on these two genes rather than highlighting a broader analysis. Alternatively, the authors should knock down more “critical” HMTs.
(In table 4, it is indicated how “critical” HMTs are selected. However, the word is not the most indicated for the meaning that the authors attribute to it)

There are still sentences reporting the results but missing the reference to a specific figure or table.

The authors added Table 2 reporting the analysis in Fig.2. I still think that a clustering analysis would be informative. This would also help to have more information for the genes that are not in the blue and red boxes.

Figure Legends need to be improved, in particular fig7 and 8.
The fact that the colors, blue and red, in the histograms are swooped (in term right  and left position)  in the different panels denotes a lack of attention to the details.

Fig.7c and 8c are unclear.

Fig5a is still missing some statistics.

Fig.6. It is not clear to which comparison the P Values refer to.

The authors did not control their statistical findings for the different sample size of the cohorts.

English can still be improved.


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: GENETIC ALTERATION OF HISTONE LYSINE METHYLTRANSFERASES AND THEIR SIGNIFICANCE IN RENAL CELL CARCINOMA
Review round: 2
Reviewer: 2

Output:
Basic reporting: The manuscript has been revised as suggested. Literature cited appropriately.  Figures were updated mostly as suggested.
Experimental design: This is a helpful study where the authors did analysis of the epigenetic factors and validated their findings
Validity of the findings: The authors did a good job in validating and the conclusions are appropriate
Additional comments: The authors addressed all the concerns raised and i suggest the manuscript for publication pending editors decision.


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: COMPREHENSIVE ANALYSIS OF LNCRNA-ASSOCIATED COMPETING ENDOGENOUS RNA NETWORK IN TONGUE SQUAMOUS CELL CARCINOMA
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript entitled “Comprehensive analysis of lncRNA-associated competing endogenous RNA network in tongue squamous cell carcinoma” is a well-written manuscript. Language polishing will be much appreciated. In the current study, the authors used existing sequencing data to investigate differentially expressed lncRNA, mRNA and miRNA and used this information to construct competitive endogenous RNA (ceRNA) network. This study will defiantly help in understanding the RNA interaction network and mechanism in TSCC.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Major

1)	Flowchart of the ceRNA network construction must be included for better understanding of the approach used
2)	Gene set enrichment analysis may add value to this article
3)	In the results section, line 183, 184, 185 need to be clear and explained

Minor

1)	The conclusion in the abstract can be clearer and specific
2)	Supplementary figure 4 legend should be clearer and written better
3)	Must include expansion for MRE in line 73
4)	Paragraph transitions need to be improved in the introduction
5)	Resolution of figure need to improve especially for fig 7
6)	Space needs to add in between (TSCC) and remains limited


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: COMPREHENSIVE ANALYSIS OF LNCRNA-ASSOCIATED COMPETING ENDOGENOUS RNA NETWORK IN TONGUE SQUAMOUS CELL CARCINOMA
Review round: 1
Reviewer: 2

Output:
Basic reporting: The authors identified lncRNAs as potential prognostic and therapeutic targets for TSCCs. They analyzed RNA expression profiles from tumor and normal control tissues and identified dysregulated mRNAs, lncRNAs and microRNAs. Importantly, they built a competing endogenous RNA (ceRNA) network that would be useful tool in predicting disease survival. At few places the English syntax needs to be checked. The literature review is not sufficient. Some figures have very small text making them difficult to read.
Experimental design: In this study, Zhang et al utilize the publicly available dataset from the TCGA portal, after filtering criteria chose 122 patients and 15 normal controls for the study. They identified the differentially expressed mRNAs, lncRNAs and miRNAs in TSCCs and generated ceRNA networks that were related to survival.
Validity of the findings: Although highly relevant in studying carcinogenesis, this study lacks a strong hypothesis, rigorous interpretation, and exhaustive analysis, and the inference is restricted to just one type of cancer. This manuscript needs to incorporate broader application of the ceRNA networks they identified, use additional statistical analyses and expand the methodology to link the identified lncRNAs to carcinogenesis and survival.
Additional comments: The authors identified lncRNAs as potential prognostic and therapeutic targets for TSCCs. They analyzed RNA expression profiles from tumor and normal control tissues and identified dysregulated mRNAs, lncRNAs and microRNAs. Importantly, they built a competing endogenous RNA (ceRNA) network that would be useful tool in predicting disease survival.
In this study, Zhang et al utilize the publicly available dataset from the TCGA portal, after filtering criteria chose 122 patients and 15 normal controls for the study. They identified the differentially expressed mRNAs, lncRNAs and miRNAs in TSCCs and generated ceRNA networks that were related to survival.
Although highly relevant in studying carcinogenesis, this study lacks a strong hypothesis, rigorous interpretation, and exhaustive analysis, and the inference is restricted to just one type of cancer. This manuscript needs to incorporate broader application of the ceRNA networks they identified, use additional statistical analyses and expand the methodology to link the identified lncRNAs to carcinogenesis and survival. Additionally, the authors need to address following minor concerns:
•	#34 lncRNA not lnRNA
•	#72 Delete In 2011
•	#148 heat map of?
•	Figure 2A text is not legible
•	Authors need to explain the relevance of their study as only two lncRNAs showed significant relation to overall survival
•	Authors should investigate and report if the lncRNAs in the ceRNA network they identified show any correlation with clinical features of other types of cancers
•	A schematic explaining the workflow could be useful


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: COMPREHENSIVE ANALYSIS OF LNCRNA-ASSOCIATED COMPETING ENDOGENOUS RNA NETWORK IN TONGUE SQUAMOUS CELL CARCINOMA
Review round: 2
Reviewer: 1

Output:
Basic reporting: I am satisfied with the revision. All the text in the figures should be of the same font. Maintain it with same text size where ever possible. Please check carefully and modify
Experimental design: No comment
Validity of the findings: No comment
Additional comments: All the text in the figures should be of the same font. Please check carefully and modify

I am satisfied with the revision.


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: COMPREHENSIVE ANALYSIS OF LNCRNA-ASSOCIATED COMPETING ENDOGENOUS RNA NETWORK IN TONGUE SQUAMOUS CELL CARCINOMA
Review round: 2
Reviewer: 2

Output:
Basic reporting: The authors have adequately acknowledged and addressed the suggestions on the experiments and data representation previously raised by the reviewer. The grammar and syntax has also been significantly improved. The manuscript can be published.
Experimental design: Experimental design has been promptly explained and represented.
Validity of the findings: The competing endogenous RNA (ceRNA) network that the authors have built would be useful tool in predicting disease survival.
Additional comments: The authors have adequately acknowledged and addressed the suggestions on the experiments and data representation previously raised by the reviewer. The grammar and syntax has also been significantly improved. The manuscript can be published.


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

Input:
Title: BEHAVIORAL CORRELATES OF SEMI-ZYGODACTYLY IN OSPREYS (PANDION HALIAETUS) BASED ON ANALYSIS OF INTERNET IMAGES
Review round: 1
Reviewer: 1

Output:
Basic reporting: I'm not a native English speaker, but the manuscript seems to be written in clear, unambiguous and technically correct English.
The literature is well referenced, exhaustive and appropriate.
The structure of the article fits to the PeerJ journal standards.
Figures are relevant and of high quality (some minor points regarding Figures 1 and 3 are detailed in the pdf file).
Experimental design: The article suits with the aims and scope of the PeerJ journal.
The research question is well defined and meaningful, since the article seeks to rigorously test the association between facultative zygodactyly of the Osprey with capture of the prey, a statement that so far was based on anecdotal observations.
Methods are described with sufficient detail.
Validity of the findings: The results are well presented and conclusions are well stated.
These are interesting findings and deserve to be published.
Additional comments: This is a novel and interesting article where the authors, based on internet images, cross-tabulated the three possible toe configurations for the Osprey (i.e. anisodactylous, zygodactylous, and the intermediate condition) with different grasping scenarios, contact conditions, object sizes and grasping behaviours. Their results confirms an association between zygodactyly and grasping behaviour in general for the Osprey, with greater odds of exhibiting zygodactyly while grasping objects in flight than whilst perched and in single-foot grasps with fish compared to other objects, suggesting a functional association between predatory behaviour and zygodactyly. Minor specific suggestions are noted in the manuscript pdf.


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

Input:
Title: BEHAVIORAL CORRELATES OF SEMI-ZYGODACTYLY IN OSPREYS (PANDION HALIAETUS) BASED ON ANALYSIS OF INTERNET IMAGES
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper meets all these basic requirements. All papers in the literature cited are in the text. I did not do the reverse check to confirm that all citations in the text of the paper are in the LitCit.
Experimental design: This is an interesting topic and an admirable use of the amazing resources available in the form of thousands and thousands of digital images available online.

I find the methods for the most part strong and well thought out. One question that is not addressed, and I don’t really think it’s functionally important, is whether Ospreys are “right-“ or “left-footed” when they’re carrying prey. It is well known that Ospreys will maneuver fish once they’re airborne with their prey so that the fish’s body is aligned with the Osprey’s body to turn the fish’s hydrodynamic design into an aerodynamic advantage as they carry the prey away from the capture location. I get asked this all the time. My guess is that in most cases it is just a function of whether the fish was going from right to left when the Osprey caught it. Whichever foot is closest to the head will be the one that the Osprey puts in front. Just an observation for future analysis perhaps.

One bit of data that is certainly available in some images is what was the toe arrangement before the Osprey hit the water? Kris Rowe has amazing images of Ospreys about to strike the water and they all seem to have the toes fully splayed in the zygodactylous arrangement. Are there enough images like these to offer any insight here? The authors must have included many of Rowe's photos from the Connecticut River Ospreys.
Validity of the findings: I will have to defer to other reviewers on the statistical analyses. I’m not familiar with the procedures that the authors used, but they seem relatively straightforward, and the results make sense, so I will move to the discussion and general comments.

Lines 59-62. I don’t follow the logic here. Sure, we see Ospreys using a zygodactyl toe arrangement doing non-predatory behavior, but wouldn’t that just be expected given that the outer toe can go either way? Why does seeing an Osprey perched zygodactyly make arguments about the advantages of zygodactyly in prey capture speculative? Logic dictates that the selective forces on a raptor’s foot will be related to prey capture. I demonstrated this in my Ph.D. thesis—foot structure (specifically toe length) across the Falconiformes and Accipitriformes is tightly linked to the type of prey commonly taken by different species.

Lines 199-200. The authors state that Semi-zygodactyly has “apparently evolved only three times (Ospreys, turacos, and the common ancestor of owls and mousebirds),…” but on line 51 they state that Black-shouldered Kites are also facultatively zygodactylous. If the Kites have the trait, then the statement on lines 199-200 cannot be true.

Lines 211-214. I disagree with the statement about the similarity of owls and Ospreys relating to their feeding on prey that is difficult to capture driving some sort of convergent evolution. No doubt about Ospreys needing every advantage they can get holding on to slippery fish, but the same is certainly not relevant to owls. Most owls that are hunting at night are not capturing fast moving prey. Most are catching prey that are almost certainly unaware of what is about to happen to them. I would argue that diurnal raptors are much more likely to encounter fast moving prey than are most owls. The authors need to make a much stronger case for this point.

Lines 226-229. The authors question how the rotation of the outer toe is accomplished, suggesting an alternative that the arrangement is “passively enabled by contact.” It took me a while to see the point here, I think because of the use of “enabled.” An Osprey about to grab a fish has set the toes in whatever arrangement it chooses before the moment of impact. I can attest to the same situation with Barred Owls. In my studies of this species, I have been hit by owls and can see, looking at the punctures in my arms, that they were in fully zygodactyl foot arrangement when they sunk their talons into me. As evidenced by the photos I’ve seen and mentioned above, Ospreys have their talons fully splayed at the moment of moment of impact. I can see how the movement of a fish just before impact could RESULT IN (rather than "enable") an alternate toe position, or perhaps more likely, this could happen as an Osprey, after leaving the water, regrasps its prey to manipulate it into the head-first orientation. This possibility should be discussed.

It would be interesting to work with a dead Osprey and manipulate the legs in the full “jack-knife” position that they assume before hitting the water to see if the toes splay out automatically, the way toes automatically clench around a perch when the taro-metatarsal joint is flexed.

In Table 1, right column in Grasping Effects, “To test how overall grasping behavior effects toe configuration,” change “effects” to “affects.”
Additional comments: I've gone through a Word version of the file and made some comments via TrackChanges. Most are minor points of grammar or style. Most of my more significant comments are above. I'm going to insert a couple of pictures of Ospreys immediately pre-water contact to illustrate the point about toe arrangement being determined will before contact with prey.


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: BEHAVIORAL CORRELATES OF SEMI-ZYGODACTYLY IN OSPREYS (PANDION HALIAETUS) BASED ON ANALYSIS OF INTERNET IMAGES
Review round: 1
Reviewer: 3

Output:
Basic reporting: No comments
Experimental design: No comments
Validity of the findings: no comments
Additional comments: The authors recollected photos of osprey from the internet and scored the position of digit four in relation to the observed behavior. The conclusion is not surprising, but this work quantifies, for the first time, something others have notice before, namely that ospreys fish with zygodactyl feet, but perch in anisodactyl position.
The manuscript is well written, the introduction is especially clear.
The results section, on the other hand, is hard to read, and it would be improved if the authors could soften it reducing the amount of raw data in the text.
The methodology is unusual, but very welcome, and it is actually what I like most in the paper. There is a huge amount of data on natural history to be explored by scientists in the web. They have shown an example of  how  to do it.
The discussion points to adaptative implications for the origin of semi- and full zygodactyly. There are many counter examples that could be discussed to make the discussion more balanced. Semi-zygodactyl Turacos are not carnivorous, and some of the best fishing eagle are anisodactyl. The are some important new papers on zygodactyl and semi-zygodactyl fossil birds that could be included in the discussion (see works from Daniel Ksepka, and Gerald Mayr).

Minor comments:

1	"Despite the common knowledge of Osprey semi-zygodactyly" This could be supported by some citations, it would be good to see what previous authors have said.
2	The sentence starting in lines 64-68 could be split in two for the sake of clarity.
3	194 “nested well within the predominantly anisodactylous Accipitriformes”. Actually Ospreys are the sister groups of all other Accipitriformes.


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: LOW-CARBOHYDRATE DIETS DIFFERING IN CARBOHYDRATE RESTRICTION IMPROVE CARDIOMETABOLIC AND ANTHROPOMETRIC MARKERS IN HEALTHY ADULTS: A RANDOMISED CLINICAL TRIAL
Review round: 1
Reviewer: 1

Output:
Basic reporting: The basic language throughout is clear, professional and easy to understand. The figures and tables are reported well.
Experimental design: The experimental design was well done. Some of the reporting however is not clear. The statistical analysis is not appropriate.
Validity of the findings: The hypothesis of the researchers was that moderate carbohydrate restriction may be easier to maintain than severe carbohydrate restriction. However, this hypothesis was not objectively measured nor was it reported in an objective manner. The statistical analysis was not done correctly--since there are multiple diet groups, interaction effects, as well as main effects need to be tested and reported. I can't recommend this paper be considered for publication until the statistical analysis is revised and with two way ANOVAs and interaction effects as well as treatment (main effects) are reported clearly.
Additional comments: I believe this is a good study and a great research question. I believe overall, the study was well executed. However, significant modification needs to be made in regards to the statistical analysis and reporting aspect of the paper.


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: LOW-CARBOHYDRATE DIETS DIFFERING IN CARBOHYDRATE RESTRICTION IMPROVE CARDIOMETABOLIC AND ANTHROPOMETRIC MARKERS IN HEALTHY ADULTS: A RANDOMISED CLINICAL TRIAL
Review round: 1
Reviewer: 2

Output:
Basic reporting: The language used throughout was appropriate. The cited literature was also appropriate with the main papers in the are having been referred to. The structure was appropriate.

I enjoyed reading the paper but felt the context was lost a little when discussing adherence. The issues with adherence with low carb diets generally come after 1 year so this would be difficult to detect in a 12-week study. The more interesting data, I feel would be from the clinical outcomes. I think you can keep the adherence data and discuss it but not really have this as a standalone/focal hypothesis because it isn’t really anything that your study could conclude on? Also, this objective/hypothesis isn’t mentioned in the title or the background in the abstract, so it feels a little misplaced.

I feel useful data to include would be the mean macronutrient breakdown of each of the groups at baseline and at week 12. Could you include this?
Experimental design: Well defined research question. Good explanation of blinding and how participants were assigned to groups. Could a little more information be given regarding the dietary instruction that participants were given? Lack of power/small sample size an issue but acknowledged in limitations to the study. Ethical approval acquired.

It may read better to have inclusion and exclusion criteria instead of “not diagnosed with diabetes” and “not previously following a keto diet” in inclusion, this could be exclusion criteria.
Validity of the findings: Conclusions seem sound but should say LCHF diets are easily adhered to “over a 12 week period”. It would be useful in the text and in the abstract to give the individual results of each of the 3 groups for each of the outcomes as opposed to the combined results as the combined results isn’t truly sharing the results of a RCT.

The study talks about adherence, but actually the adherence discussed is related to the adherence to calories, whereas the adherence should be discussed in relation to the carbohydrate as that is what we are discussing so the way in which this is reported needs changing.
Additional comments: I enjoyed reading the paper so thank you for the submission. I feel a few areas need to be addressed as per my comments but would make a good paper if these suggestions were actioned.


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: LOW-CARBOHYDRATE DIETS DIFFERING IN CARBOHYDRATE RESTRICTION IMPROVE CARDIOMETABOLIC AND ANTHROPOMETRIC MARKERS IN HEALTHY ADULTS: A RANDOMISED CLINICAL TRIAL
Review round: 2
Reviewer: 1

Output:
Basic reporting: Much better. I felt the authors listened to the comments provided. The objectives were much clearer and therefore the structure and flow of the paper felt much improved.
Experimental design: Again, much better. Thank you for adding this detail.
One small comment, in inclusion criteria to add the age of participants. e.g. > 18 years old.
Validity of the findings: No further comments. The conclusions are sound.
Additional comments: Well done to the authors, I feel the paper reads much better. Thank you for taking the time to make the amendments.


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: BLOOD PARASITES INFECTING THE HOATZIN (OPISTHOCOMUS HOAZIN), A UNIQUE NEOTROPICAL FOLIVOROUS BIRD
Review round: 1
Reviewer: 1

Output:
Basic reporting: The article offers the first information of haemosporidian parasites in the Hoatzin. Unfortunately the sample sizes are really small. The authors explain this by the rarity and difficulty to catch this species. There are a few other short-comings: The title of the paper is misleading as in the paper next to avian malaria other blood parasites are reported (but poorly identified, it is unclear what species). I suggest to change in the title Plasmodium to "Blood parasites" or, alternatively, leave out microfilaria and red blood cell data as this is limited information with regard to haemosporidian infection. If this would be my paper, I would concentrate on haemosporidian parasites. Maybe the blood parameter data is more suitable for another journal.
There are quite a few mistakes regarding the English language. This needs to be fixed.
Regarding references and background all is well. The article structure is also professional, only I would consider leaving out all tables and figures that do not relate to haemosporidian parasites. The haemosporidian tree is nice, but if at all possible it would be interesting to indicate hosts (at least for specialists).
So the article is not entirely self-contained and needs work (see above).
Experimental design: These points are all OK BUT a larger sample would really be important. Molecular work seems OK and also the analyses. See attached pdf for further comments.
Validity of the findings: See "basic reporting"
Additional comments: I hope you will be able to catch many more birds in Venezuela and check them for avian malaria. Your work is very good and 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: BLOOD PARASITES INFECTING THE HOATZIN (OPISTHOCOMUS HOAZIN), A UNIQUE NEOTROPICAL FOLIVOROUS BIRD
Review round: 1
Reviewer: 2

Output:
Basic reporting: Dear Editor,

This is a well-organized paper which provides a detailed analysis of parasites infecting Hoatzin birds, as a model organism. The Hoatzin is unique as a strictly folivorous bird species, although studies for this species are limited in various aspects, especially haemoparasites. The introduction and discussion are written with great clarity and objectivity. Considering the difficulties of catching these birds and the lack of studies for the floodplains of the Amazon, the sampling was reasonable to reach the aims of the study. The data analysis was well elaborated. The authors used different parasite detection and diagnostic methods such as blood film examination and molecular analysis. Discussion could be improved if the authors compare the level of parasites found in the floodplains to studies conducted in other biomes, such as Cerrado and Atlantic Forests, as found in publications by Miguel Ângelo Marini and Fabiane Sebaio. Other aspects that should be emphasized by the authors are the specific environmental vulnerabilities of the floodplains and how this could affect parasitism levels of  birds as well as other organisms.  The floodplains not only represent the second largest environment of the Amazon region (in territorial extension), but also shelter almost one-third of the bird species that inhabit the region. The avifauna of the floodplain presents a greater complexity. Several species are specialized in micro habitats of the floodplains (Remsen & Parker, 1983; Rossen, 1990) and it has been shown that avifauna of the floodplains of Amazonia are not homogeneously distributed (Cohn-Haft et al., 2007).  Cohn-Haft et al., 2007 also show that, while birds in Varzea are specialized in microhabitats, they still present in environments modified by human habitation, suggesting that these birds are relatively tolerant or have not yet had sufficient time to feel the impacts of human actions. How parasitism could affect the birds is a field that is not currently well explored. But I suggest that the authors add a paragraph discussing the conservation implications of their findings regarding the levels of bird parasites found in their study as compared to other studies conducted in other biomes. The authors should also provide more detailed information on the degree of conservation of the areas where the birds were sampled and how the level of parasitism could increase if the areas are affected by anthropic disturbances (citing other studies on these subject). With the inclusion of the above modifications, I recommend the publication of this article in the journal PeerJ.

CONH-HAFT, M. ; NAKA, L. N. ; FERNANDES, A. M. 2007 . Padrões de distribuição da avifauna da várzea do rio Solimões-Amazonas. Bases científica para a conservação da várzea: identificação e caracterização de regiões. 1ed.: Ibama/ProVárzea, v. , p. 287-323.
Experimental design: Considering the difficulties of catching these birds and the lack of studies for the floodplains of the Amazon, the sampling was reasonable to reach the aims of the study. The data analysis was well elaborated. The authors used different parasite detection and diagnostic methods such as blood film examination and molecular analysis.
Validity of the findings: No comment
Additional comments: Discussion could be improved if the authors compare the level of parasites found in the floodplains to studies conducted in other biomes, such as Cerrado and Atlantic Forests, as found in publications by Miguel Ângelo Marini and Fabiane Sebaio. Other aspects that should be emphasized by the authors are the specific environmental vulnerabilities of the floodplains and how this could affect parasitism levels of  birds as well as other organisms.  The floodplains not only represent the second largest environment of the Amazon region (in territorial extension), but also shelter almost one-third of the bird species that inhabit the region. The avifauna of the floodplain presents a greater complexity. Several species are specialized in micro habitats of the floodplains (Remsen & Parker, 1983; Rossen, 1990) and it has been shown that avifauna of the floodplains of Amazonia are not homogeneously distributed (Cohn-Haft et al., 2007).  Cohn-Haft et al., 2007 also show that, while birds in Varzea are specialized in microhabitats, they still present in environments modified by human habitation, suggesting that these birds are relatively tolerant or have not yet had sufficient time to feel the impacts of human actions. How parasitism could affect the birds is a field that is not currently well explored. But I suggest that the authors add a paragraph discussing the conservation implications of their findings regarding the levels of bird parasites found in their study as compared to other studies conducted in other biomes. The authors should also provide more detailed information on the degree of conservation of the areas where the birds were sampled and how the level of parasitism could increase if the areas are affected by anthropic disturbances (citing other studies on these subject). With the inclusion of the above modifications, I recommend the publication of this article in the journal PeerJ.

CONH-HAFT, M. ; NAKA, L. N. ; FERNANDES, A. M. 2007 . Padrões de distribuição da avifauna da várzea do rio Solimões-Amazonas. Bases científica para a conservação da várzea: identificação e caracterização de regiões. 1ed.: Ibama/ProVárzea, v. , p. 287-323.


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: BLOOD PARASITES INFECTING THE HOATZIN (OPISTHOCOMUS HOAZIN), A UNIQUE NEOTROPICAL FOLIVOROUS BIRD
Review round: 1
Reviewer: 3

Output:
Basic reporting: This manuscript reports on haemoparasite infections, apparently for the first time, on an Amazonian bird difficult to sample. The methods are consistent with current literature, but sample size is rather small, making this study very preliminary. The study also reports data on microfilaria and information on haematological parameters, both partially complimentary to haemoparasite infection, but mixed in the text. The manuscript could be improved by either (a) structuring it with three components (haemoparasite, microfilaria and haematological parameters) or (b) focusing even more on the haemoparasite infection and only appending at the end of the Results and Discussion sections the data on microfilaria and haematological parameters. Microfilaria is not mentioned in the title, but is cited first in the objective (line 63) and in the first paragraph of the Discussion (line 192). So, the manuscript could be re-structured, from the title, to incorporate microfilaria and haematological parameters also as its main objective, especially since the bird seems to be so difficult to capture and study.
Experimental design: No comment. See below.
Validity of the findings: No comment. See below.
Additional comments: Specific comments:
Lines 75-76. Describe shortly the vegetation characteristics and the conservation status of the sampling site since disturbance can affect parasitism. From a satellite image the study site seems very disturbed.
Lines 192-196. The Discussion starts with filarial infections, though it is secondary in the manuscript to haemosporidian infection. It should focus first on the most important main results.
Lines 204-205. This sentence needs references to support that “the ratio of one to the other (H:L) is commonly used as a stress indicator”. For example:
Gross and Siegel. 1983. Evaluation of the heterophil/lymphocyte ratio as a measure of stress in chickens. AVIAN DISEASES 27:972-979.
Maxwell 1993. Avian blood leukocyte responses to stress. WORLD’S POULTRY SCIENCE JOURNAL 49:34-43.

Line 221. Provide a reference for “has been only reported so far in Brazil”.
Lines 253-255. The statement “Overall, our results suggest that the parasite biodiversity in this species, and likely other birds inhabiting riparian ecosystems (e.g., Wood Stork and other species of Ciconiidae family), could be high” seems premature, especially considering the very small sample size. I recommend the following references to improve the discussion about malaria in Amazonian birds:

Belo et al. 2011. Host species and parasite lineage diversity of haemosporidians in three different environments with distinct levels of disturbance. Plos ONE 6: 17654.
Fecchio et al. 2017.  Avian malaria, ecological host traits and mosquito abundance in southeastern Amazonia. PARASITOLOGY 44:1-16.
Fecchio et al. 2018. Host community similarity and geography shape the diversity and distribution of haemosporidian parasites in Amazonian birds. ECOGRAPHY 41:505-515.
Fecchio et al. 2018. Diversification by host switching and dispersal shaped the diversity and distribution of avian malaria parasites in Amazonia. OIKOS 127:1233-1242.
Folegatti et al. 2017. A systematic review on malaria sero-epidemiology studies in the Brazilian Amazon: insights into immunological markers for exposure and protection. MALARIA JOURNAL 16:107.

Other minor corrections:
Line 23. Replace Opisthocomiforme by Opisthocomiformes.
Line 97. Remove the comma (,) after Lessler.
Line 100. 2009 should be (2009).
Line 176. Replace hemoparasites by haemoparasites. Correct also in the abstract.
Line 202. Replace “no” with “non-” at the end of the line.


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: BLOOD PARASITES INFECTING THE HOATZIN (OPISTHOCOMUS HOAZIN), A UNIQUE NEOTROPICAL FOLIVOROUS BIRD
Review round: 2
Reviewer: 1

Output:
Basic reporting: The manuscript which is not well known species the Hoatzin (Opisthocomus hoazin), is well designed and analyzed. The authors give us first results of blood parasites of the Hoatzin birds. Detail molecular analysis was done for identification the blood parasite of the birds. Although the manuscript improved according to previous reviewers’ suggestion and comment, still the main problem of the manuscript is sample size which is already mentioned previous reviewers.
Differential white blood cell counts are given Table 2 it is very interesting approach but microfilaria and microfilaria/Plasmodium results are given only one specimen. So, it is not useful any critics
Line 216 -220 it is impossible to make any critics like decrease or increase using one specimen information. The sentence should be rewrite
Experimental design: Catching the Hoatzin birds seems to be difficult but more samples could have found from the other lab. Lab works are ok
Validity of the findings: No comment
Additional comments: No additional comments


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

Input:
Title: BLOOD PARASITES INFECTING THE HOATZIN (OPISTHOCOMUS HOAZIN), A UNIQUE NEOTROPICAL FOLIVOROUS BIRD
Review round: 2
Reviewer: 2

Output:
Basic reporting: Interesting findings and complex discussion, though I am not convinced about the value of microfilariae reporting. The statement, that other studies also do so is not real justification. On the other hand, if this few sentences remain it causes no harm.
Experimental design: Part on Plasmodium parasites uses robust methodology, the basic haematology and microfilariae reporting are by-products of limited value. To be honest, presenting the haematological parameters with some clinical relevance would require larger set of individuals, more defined conditions, age, sex etc., as the haematological parameters vary a lot.
Validity of the findings: see above
Additional comments: No additional comments


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

Input:
Title: MOLECULAR AND MORPHOLOGICAL CONGRUENCE OF THREE NEW CRYPTIC NEOPETROSIA SPP. IN THE CARIBBEAN
Review round: 1
Reviewer: 1

Output:
Basic reporting: The MS was well structured and followed normal standards for the discipline. The writing was of a good standard throughout, with only a few typos or minor grammatical errors, which I have detailed in the general comments line-by-line. However, there were instances of overuse of the passive voice (e.g. sequences being “retrieved” and “provided” when referring to amplification and sequencing work done in this study), which made it difficult to understand. I would encourage the use of active voice to enhance clarity here, but at the least, these words should be substituted for something more appropriate.

In line 185, the Genbank Accession numbers are not listed. 18S data for N. sigmafera is not present in the Fasta file. Please add these.

Figures were generally high quality, however Fig 2D is bad resolution and must be changed for publication. In Fig 3A the arrows are too small, and should be made a little larger. In figure 5, the words “28S rRNA” look squashed (very minor but would be good to change if possible).

The literature was well referenced and relevant. However, at line 614, please be specific about the name of the extension, as this is not referred to elsewhere as far as I could see, and cite it (presumably it is Erpenbeck’s I3-M11 partition that the authors mean?).  Please also give more details upon the previous work detailed in lines 82-84.
Experimental design: This MS represents good quality, original and meaningful research, tackling taxonomy in the difficult Haplosclerida group. The work carried out was extensive and rigorous, and suitable to address the research at hand. However, there are a few clarifications to the methodology I would like to see:

1) The paragraph starting line 147 describing the primers and PCR conditions is confused and would not be sufficient for replication. The specific use of the primers designed here is not clear – i.e. in what primer pair combinations they were used, given that three new primers are shown for COI and one new primer for 18S. The PCR conditions are not described in sufficient detail here, as a range of annealing temperatures is given for all reactions, rather than detailing the temperature used for each primer pair. This could go in S1 to avoid cluttering the main article.

2) I would like to see details of the quality scores and acceptable quality thresholds utilized for the sequence data; details on how the sequences were edited and assembled are scant.

3) At line 170, how was the value of 85% chosen?
Validity of the findings: I agree with the validity of these new species. However, I am not convinced by the authors’ reasons for rejecting a genus change for N. sigmafera given the molecular, morphological and reproduction data all indicate a divergence from the other members of the genus. The authors explain that neither the presence of sigmas or the viviparity can be used as a monophyletic character, but do not explain why they reject their genetic evidence. What more would be required to push N. sigmafera into a different genus if these things are not enough, and conversely what evidence ties N. sigmafera to the genus?
Additional comments: 1) It’s a great shame there is no in-situ photo of Neopetrosia cristata – is there any way for the authors to obtain one?

2) The last sentence of the abstract is confusing, please revise.

3) Line by line comments:

Line 51 – 52: Phrase “were confirmed” repeated
Line 61: “consist” should be “consists”. I also recommend putting a comma after the word “Petrosiidae” to enhance readability
Line 65: Is the citation of the web address necessary?
Line 68 – 73: Is there any reason to repeat the genus name throughout this sentence?
Line 74-76: This sentence is unclear, please clarify.
Line 75: Replace “has” with “have”
Line 81: “Rather widespread” is a little general – please be specific about the geographic range
Line 86: Why have you put “other Caribbean localities”? It seems the only other area sampled was Martinique? Sorry if I missed something.
Line 94: “in” should be “on”
Line 130-131: should be “50 spicules per specimen”?
Line 150: The use of the word “retrieved” here is not appropriate (I assume that you mean you amplified these genes using primers from the cited papers?)
Line 151: “Specific primers were then designed when sequence data was missing to complete the gene sequence region of interest. Primers were designed using

NetPrimer” This would read better as one sentence as the second sentence here is a bit repetitive.
Line 157 – 158: Please be consistent in abbreviations (s or sec).
Line 165: Excessive use of the passive voice here “Double sequence coverage was provided”, please revise.
Line 243: Please remove comma after “thickly” (or change “thickly” to “thick”?)
Line 257: Typo: consist → consists
Line 334: Typo (semi colon)
Line 346: “are influenced by” should be changed to “vary by”
Line 362: y → and?
Line 400: Is the color cream in ethanol throughout, or just the interior? Please confirm.
Line 411: Typo (“holotypewas”)
Line 426:  Typo – should be a space in “1mm”
Line 449: Panamá is with an accent here but not in other places in the article; please be consistent one way or the other
Line 497: “This sponge is
known to harbor a host specific community of Synechococcus spongiarum cyanobacteria”
– could you be more specific here please? I am confused with the terminology as it reads as if you are referring to one species of cyanobacteria as a community. Could you also clarify what you mean by host specific – i.e., is that species of cyanobacteria specific to that species of sponge?
Line 537: “Add your results here”
Line 588: “Throughout” I think implies something more geographically extensive than the sampling conducted here, please change this.
Line 619: Is there a double space here? Hard to tell on the PDF, sorry if not.
Line 627-639: Grammatical mistakes in sentence, please revise
Line 639-641: This last sentence is a little confusingly worded, please revise. I also believe the phrase “make more genomes available” is a bit too passive.
Line 655: “continue” should be “continues”

Table 1 – should this read “number of sigma measured”?

Table S1 does not have a title.

References: There are some inconsistencies and mistakes in your reference list – please go over this carefully and ensure that the style is uniform throughout and remove typos (possibly from referencing software?). E.g., in some references, you have put a space in between the volume and issue number and in some you have not. I have also noted some other mistakes here but it is not necessarily extensive as I only scanned over it:

Line 729: New line missing between references
Line 790: Typo Noth → North. Please also revise the capatilisation in this sentence to match with the rest of the style of your list.
Line 884: Errant comma
Line 891: Volume number is in italics
Sollas 1885 reference – there appears to be a few too many numbers here?
Wiedenmayer
1977 reference – something strange happened here

Acknowledgements
 The contribution numbers are missing here, please add or remove the sentence.


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

Input:
Title: MOLECULAR AND MORPHOLOGICAL CONGRUENCE OF THREE NEW CRYPTIC NEOPETROSIA SPP. IN THE CARIBBEAN
Review round: 1
Reviewer: 2

Output:
Basic reporting: Many suggestions were made for improvement of language, above all as far as punctuation goes. Genbank accession numbers were not included still, but the space for their inclusion is there.
Experimental design: No comments aside those presented in the PDF.
Validity of the findings: There is actually no speculation. But I did suggest some alternative lines of reasoning to be presented, so that the reader can have a more comprehensive view of scenarios other than "we found three new Neopetrosia"
Additional comments: I congratulate the authors on their achieved contribution. Integrative taxonomy is the way to move forward when it comes to cryptc species, and I think the results presented by Vicente et coll is quite convincing of hidden diversity being brought to light. On the other hand, I made a large series of suggestions to avoid ambiguities and inconsistencies as far as arguments go, and a very large series of suggested adjustments to the text. Notorious among the latter is a rather economic use of commas, which renders the text frequently difficult to read. In my opinion the utmost inconsistency lies in the fact that molecular results being presented subsequently in the MS, readers are obliged to accept the new species diagnosed on the basis of absolutely minute morphologic distinctions, even though the first species whose description is presented (N. proxima) is said to be quite variable in many aspects. This is only acceptable if cross-referenced to molecular results, for which reason I suggest to turn the MS "upside-down".


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: DISENTANGLING THE EFFECT OF HOST-GENOTYPE AND ENVIRONMENT ON THE MICROBIOME OF THE CORAL ACROPORA TENUIS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The study is interesting and a pleasant read. English is used throughout, the language is professional. The article structure is professional. The introduction is well referenced, and properly and evenly cited. The description of the figures is adequate. The BioProject on NCBI at which the raw seq data are deposited is accessible. The manuscript is self-contained and represents an appropriate unit of publication.

There reporting of basic sequencing results and presentation of bacterial community composition will benefit from adding more detail.

	Major comments:
1. I am missing basic reporting of sequencing data, such as total numbers of seqs or reads before and after QC/removal of chimeric seqs and other unwanted seqs (like mitochondria, eukaryotes, lab contaminants), average amplicon length, etc. In addition, it would be informative both from the viewpoint of a reviewer and a reader to have an ASV abundance table (like an OTU abundance table) provided. This could e.g. be a .csv or .txt table provided in the supplement.
2. Dealing with kit contaminants, and reporting thereof. Lines 180-181: The Qiagen kits are often contaminated with bacterial DNA/amplicons, which may affect/distort bacterial community datasets (cf. Salter et al. 2014 BMC Biology). The best way to deal with this is to include ‘negative control’ mock samples (DNA extractions without template, using only kit reagents) and mock PCRs (PCR products without template, using only master mix reagents) and sequence them along with your samples. I strongly encourage the authors to add brief details in whether and how they’ve dealt with potential lab/kit contamination. I am a bit concerned about the proportion of Actinobacteria shown in the alluvial diagram (Fig. 4).
3. Lines 266 and following: Endozoicomonas may be the most abundant bacterial genus present in your sequence data, but associated seqs make up only about half of the microbiome (48 % on average). It would be informative to add some numbers for mean relative abundances of other bacterial groups (on the class and family or genus level) in the manuscript text, starting from line 272. Please also describe in the results section how many different Endozoicomonas ASVs were identified in the analysis, and what are their relative abundances (information can be drawn from figures, but it is a bit frustrating for the reader to not have it briefly compiled in the ms text).
4. in this context, it would be informative to provide a stack bar plot showing the microbiome composition (e.g., rel. abundances of xx most abundant ASVs + ‘others’) on the ASV or family level across coral genotypes in the manuscript to visualize the genotype-specific patterns.
5. It is good practice to provide basic information (e.g., a table) showing diversity and richness indices of total bacterial communities over samples or treatments.
6. Line 347: ‘some bacteria were significantly more abundant in treatments’ – the results state that the microbiome composition did not differ between treatments. Please provide information for significantly differentially abundant data in results section if you tested individual variants/families etc. If this is referring to indicator taxa, please correct statement – indicator taxa are significantly associated with a condition, environment, etc. This is not necessarily about abundance (rare members can be indicators), but persistent association.

Minor comments:
1.Lines 182-183: It would be helpful to provide more detail on PCR conditions along with sequences for F and R primer including illumina overhangs rather than only provide a reference.
2. Lines 201-202: Please mention that the bioproject uploaded in the SRA is available on NCBI.
3. The authors keep switching between the terms ‘effective quantum yield’ and ‘photochemical efficiency’. I strongly encourage the authors to consistently use one term only (Quantum yield – effective or maximum, whichever applies – see comment below in experimental design) throughout the manuscript so as not to confuse readers who are not familiar with this kind of measurement.
4. Lines 290-293: It would be great to add a sentence here on which of these bacterial groups are significantly associated with which experimental conditions. It is a bit frustrating for the reader to have to go get it from the supplement.
5. Line 325: the authors argue that Endozoicomonas ASV1 might be a stable and persistent member of the A. tenuis they are working on. The authors can easily get information on the core microbiome out of their data. They could even run the analysis together with sequences from field control corals (which seem to be available) and add this detail to the manuscript. This should not be considered as a requirement to have the manuscript accepted, but since this is a calculation that doesn’t take up much time and is discussed by the authors anyways, they might as well include core microbiome data.
6. Figure 6: the color gradient used for the indicator taxa in the plot is a bit hard to distinguish, in particular the greens and the blues. I encourage the authors to modify the color scheme to help the reader.
Experimental design: The research presented here is within the Aims and Scope of PeerJ.

The research goal is defined (effect of host genotype-by-environment interactions on the microbiome of Acropora tenuis), relevant, and meaningful. It clearly addresses an existing knowledge gap (combined influence of host-genotype and environmental stress on the microbial community composition of corals). The experiment has been developed and executed with rigor, to a high technical standard. I cannot identify any obvious flaws. The methods described contain sufficient detail and information to replicate the experiment.

There are a couple points I would like to get clarification on:

1.	PAM measurements. The authors state they have measured effective quantum yield Fv/Fm from light adapted corals. As described by Chakravati et al. 2017 GCB, Fv/Fm is the maximum, i.e. dark-adapted quantum yield – the light-adapted or effective quantum yield of PSII is delta Fv/F’m. Please correct the measures accordingly to what it is you measured.
2.	coral surface area quantification - Line 150-151: the authors used a single wax coating. Previous studies have shown that two wax coatings (as described in Naumann et al. 2009) are more precise. Please explain why you decided to use a single wax coating instead.
Validity of the findings: Replication is meaningful. Data is statistically sound and controlled, but I have one comment (see below)

Absence of bacterial community responses (‘stable’ or ‘inflexible’ bacterial microbiomes) under stress have previously been observed in different corals under different stress scenarios. The authors found that bacterial communities however differ significantly between coral genotypes. This is not necessarily surprising – as the authors correctly state in the introduction, genotype-specific physiological responses have been known for corals for a good long time. There is one point that I would like the author to consider to test (if they haven't done so yet).

1.Lines 251 and following: ‘stable’ bacterial communities. Have you tested for differences in the bacterial community after omitting the most abundant bacteria (Endozoicomonas ASV1, plus potentially others) from analysis to see whether any changes occur in bacteria with lower abundance? Rare microbes might matter – and sometimes less abundant bacterial taxa can exhibit changes under stress while the most abundant taxa remain ‘stable’, but this response can sometimes be statistically masked by high abundances of dominant taxa.

conclusions are well stated and linked to the original research goal.
Additional comments: Overall, the manuscript is well written. The data support the conclusion presented by the authors (but I encourage the authors to check if bacterial communities show patterns once Endos are omitted from analysis). The language of the manuscript is professional and standard English. There are some sections in methods and results where it is not entirely clear whether measurements encompass the holobiont or symbiont only, and whether statistically significant effects where identified between all time points or not, which I have detailed below.

This study fits well in the scope of PeerJ.

Abstract:
‘Planctomytaceae’ – do the authors mean ‘Planctomycetes’ instead?

Line 120: wouldn’t it be acclimation rather than acclimatization if the corals have to get used to new conditions in a new environment (I understand they were moved to a different environment, the experimental tank?)

Line 145: add ‘amplicon’ to 16S rRNA gene sequencing

Line 154: ‘Host physiological measurements’ is not a good way to describe the following section, as three of the four measurements (photochemical efficiency, zoox cell counts, and chl a content) are specific measurements of the Symbiodiniaceae and the fourth (total protein content) is on the holobiont level. If zoox and host cells/matter would have been separated into fraction and the host fraction would have been assessed separately, that would be a measure of host physiology. I suggest to rephrase (e.g., Physiology of Symbiodiniaceae and the holobiont). This also applies to the use of ‘host health parameters’ in lines 215 and 259 (and a couple of other locations in the manuscript).

Lines 236 and following: please detail between which time points the significant effects occurred. If there were statistically significant differences between each time point, please state this clearly.

Lines 351-354: ‘Therefore, unless host-genotype independent microbial indicators can be identified and validated, the efficacy of integrating microbial community data into coral health monitoring initiatives appears unfeasible…’ – I strongly agree with the authors' assessment, and I appreciate them being upfront.


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: DISENTANGLING THE EFFECT OF HOST-GENOTYPE AND ENVIRONMENT ON THE MICROBIOME OF THE CORAL ACROPORA TENUIS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript is well written, clear and well supported by the cited literature. However, justification of the various environmental stressors and the comparison of a single versus cumulative stress are not introduced in the introduction. Please provide some justification. These can be brief, with one or two references providing evidence that each is a relevant stressor. Also, a brief introduction to single versus cumulative stress should be included. The raw data is available in the SRA of NCBI, and the figures and tables are well set out. There are several minor issues with fine editing:
Abstract
- line 45 This sentence is unclear. Instead something like: The A. tenuis microbiome was dominated by Endozoicomas with, on average, 48% of ASVs assigned to this genus, with ASVs significantly different between host individuals.
Introduction
- line 46 Should this be coral hosts?
Introduction
- line 89/90 the semi colon should be after the references
- justification/reasoning behind choice of stressors is missing
Methods/Results
- be consistent with spacing between numbers and units (e.g. 24h should be 24 h, and in other places with other units).
Experimental design: - The experimental design is robust, however the authors have not accounted for tank effects. These can skew the interpretation of tank experiments, and the authors should address this either by testing for tank effects or by explaining why these were not accounted for in the statistical analysis.
- The description of the quantification of various measures from the airbrushed tissue: Was a consistent volume of PBS used? If not, could the cell counts be influenced by the volume used here? Also, Was the tissue allocated equally among the various subsequent analyses? If not, it would also influence the results of some of these measures.
- Line 198 were eukaryote and unknown sequences also removed?
Validity of the findings: - Lines 207 and following: please clarify the ANOVA factors, indicating where 1-way, 2-way or other models were applied, and give details of which factors are being tested. The design appears to be a 3 factor design with time, treatment and genotype as the 3 factors. However, the authors have elected to apply a variety of different types of ANOVAs and PERMANOVAs, which should be clearly justified throughout. In all cases, the interactions should also be reported. The main ANOVA and PERMANOVA tables should be included in the supplementary material, as well as the post-hoc and pairwise tests.
- The authors appear to have mastered the various analyses that have been applied to the data, however lack of clarity in the manipulation of the 3 factors within the experiment and the subsequent statistical analyses (outlined above) result in some uncertainty around the outputs and the interpretation of the results. This includes any tank effects that may be influencing the outcomes.
- Conclusions are well stated and linked to results, but the results need tightening up, as outlined above.
Additional comments: A nicely designed study with several interesting results. This paper is likely to be of broad interest to the field of coral/microbial ecology.


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: LIBINORM: AN HTSEQ-COUNT ANALOGUE WITH IMPROVED NORMALISATION OF SMART-SEQ2 DATA AND LIBRARY PREPARATION DIAGNOSTICS
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: This paper described software implementing bias correction methods proposed in the authors' earlier paper [1]. The method described in that paper (and summarized in the supplemental material) here is compelling and raises interesting questions, but the scope of this paper is to describe the tool LiBiNorm they devolved to make that methodology usable by investigators, so I'll similarly restrict the scope of the review to the tool without digging into the underlying model and findings in [1].

The paper does a good job of describing the background and how the tool works. It additionally shows a benchmark comparing bias corrected Smart-seq2 to TruSeq. There are different ways that estimates of relative expression can be compared, but the approach here isn't unreasonable. The results are somewhat surprising though, as they show bias correction with other methods often leading to diminished accuracy. However, I haven't seen this comparison made before (that is, Smart-seq2 vs TruSeq), so it doesn't necessarily contradict previous papers that show improvements in accuracy between bulk RNA-Seq and qPCR with bias correction.

I downloaded and compiled the software without issue. It's well documented on the website and includes a open source license (and the licenses of included libraries). To test the program I ran it on some BAM files from [2]. The program was quite efficient, e.g. processing 27 million alignments in less than a minute. I didn't attempt to independently benchmark the method, but did inspect the output files, which looked reasonable.

I have some minor concerns about the implementation. The models are fit "using non-overlapping, single isoform genes only". I ran the method on human data, using Ensembl gene annotations, which annotates multiple isoforms for most protein coding genes. It leaves me a little nervous that these are excluded, as the remaining genes may not be characteristic the sample as a whole (e.g. if it's mostly non-coding, or lincRNA). Still, this may not matter if, as the authors posit, the global bias is a function of length primarily.

This is a minor point of concern that I hope the authors will consider, but shouldn't hold up the manuscript. Overall, it's a well written paper, and well constructed tool, and I recommend accepting it for publication.

[1] Archer, Nathan, Mark D. Walsh, Vahid Shahrezaei, and Daniel Hebenstreit. 2016. “Modeling Enzyme Processivity Reveals That RNA-Seq Libraries Are Biased in Characteristic and Correctable Ways.” Cell Systems 3 (5): 467–79.e12.

[2] Tasic, Bosiljka, Vilas Menon, Thuc Nghi Nguyen, Tae Kyung Kim, Tim Jarsky, Zizhen Yao, Boaz Levi, et al. 2016. “Adult Mouse Cortical Cell Taxonomy Revealed by Single Cell Transcriptomics.” Nature Neuroscience 19 (January): 335.


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: LIBINORM: AN HTSEQ-COUNT ANALOGUE WITH IMPROVED NORMALISATION OF SMART-SEQ2 DATA AND LIBRARY PREPARATION DIAGNOSTICS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The authors present a well written and clear description of their software. However, the title and text are somewhat misleading when it comes to the strong focus on comparing LiBiNorm to HTSeq, since in fact LiBiNorm seems to be more akin to a specific tool implemented using the HTSeq library, i.e. the htseq-count script, and not a software library intended as a tool for building bioinformatics applications.

I have seen that the authors do make the correct comparison on their website and would encourage them to amend the article accordingly. It would seem that the authors dwell on this comparison maybe more than necessary, since LiBiNorm is first and foremost a modelling Software implementing a specific bias model and I would have expected that the authors would put a comparison of the successful bias modelling to the performance of other bias-removal strategies as shown in e.g. Figure 2c more into the foreground.

A few sections could benefit from clarification, e.g. on line 156 the authors state that LiBiNorm operates in strict mode by default, requiring each read to be fully contained within an annotated exon, this seems somewhat contradictory to the statement on lines 99-101 where a splice-aware aligner is required, which would imply that reads can span exons and would be considered in that case.

On Lines 184-186 the authors generally state that LiBiNorm is faster than HTSeq (I presume they talk about htseq-count) because it is compiled. Has this gain in performance been quantified? If so, it should be reported here, otherwise this part seems unnecessary since it is not clear if there is any tangible time benefit for people that build time-critical sequencing pipelines. A sufficiently more complex or not particularly well optimised compiled program might even be slower than the htseq-count script, or any other interpreted script for that matter.

The software is presented well on a dedicated webpage. I would suggest to use higher quality images in the section about Graphing results (https://warwick.ac.uk/fac/sci/lifesci/research/libinorm/graphs/), currently the plots have a very poor resolution. It might be worthwhile to consider moving/duplicating this information in a project-associated GitHub wiki to ensure it will be available even if the software is not actively developed anymore / the authors move on in their academic careers etc.
Experimental design: The methods are generally well described with some clarifications needed as specified in section 1 (Basic reporting).
Validity of the findings: As mentioned above the strong focus on comparing to HTSeq (or rather htseq-count) seems to take away focus from the comparison of the bias removal to other approaches, I would suggest to focus more on this aspect (although that might be already covered to a relatively large degree in the previous publication that describes the models themselves).
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: LIBINORM: AN HTSEQ-COUNT ANALOGUE WITH IMPROVED NORMALISATION OF SMART-SEQ2 DATA AND LIBRARY PREPARATION DIAGNOSTICS
Review round: 1
Reviewer: 3

Output:
Basic reporting: - English writing is clear and acceptable
- Structure of this paper needs to be improved. Example: some short paragraphs could be combined to a long paragraph with much information.
- Full set of output files (page 8) should be displayed as Table or the authors should use another way to display. Because it is not scientific now.
- Tables in the manuscript aren't displayed in a scientific way.
- It should be better if the authors provide the references for some tools they used, i.e., Tophat2, STAR, or Nelder-Mead …
Experimental design: How this work different with previous work (Archer et al. 2016), authors need to discuss more this issue?
Validity of the findings: - Can the authors test their method on a general dataset? Because now the methods only performed well on a specific dataset
- Where is the primary input data authors retrieved?
- How to choose the optimal parameters in this work?
- Why the authors used SRR1743160 data? Any specific reason?
- The authors should compare with other works more detail. For example, authors can use a paired t-test to test the significances among the works.
Additional comments: The authors should discuss more the differences between the current work and their previous work. They also need to discuss the detailed comparison with other works. It will help their work more strong and enough to meet the requirement of 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: LIBINORM: AN HTSEQ-COUNT ANALOGUE WITH IMPROVED NORMALISATION OF SMART-SEQ2 DATA AND LIBRARY PREPARATION DIAGNOSTICS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The manuscript is now more clear and I have no further comments.
Experimental design: I have no comments in this section.
Validity of the findings: I have no further comments.
Additional comments: No additional comments


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

Input:
Title: LIBINORM: AN HTSEQ-COUNT ANALOGUE WITH IMPROVED NORMALISATION OF SMART-SEQ2 DATA AND LIBRARY PREPARATION DIAGNOSTICS
Review round: 2
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: The authors have already addressed all of my comments, therefore, I think the manuscript now meets the requirement of PeerJ for publication.