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: REPRODUCTIVE SUCCESS OF WHISKERED TERN CHLIDONIAS HYBRIDA IN EASTERN SPAIN IN RELATION TO WATER LEVEL VARIATION
Review round: 2
Reviewer: 2

Output:
Basic reporting: -	I still feel that the work would benefit if the manuscript was put in a much broader context (i.e. not just about terns). For example, you could refer to nest flooding studies on saltmarsh sparrows (e.g., Bayard and Elphick 2011), laughing gulls (e.g., Burger and Shisler 1980) or a large scale study on multiple shorebirds (van de Pol et al. 2010). See below for full references. By putting your work in this broader context you could greatly improve the impact of your work, potentially outside of just those people interested in whiskered terns.
-	Line 132 – 138: I think it’s only relevant to discuss the fauna of the area if it is the predator or prey of the terns.
-	There is a large amount of data that you present in your results that you don’t provide any figures for. Most importantly, your ANOVA analysis, but also your general reproductive results (Lines 265 – 280).
-	Make sure that you reference to your figures in order. For example, figure 2 should be the second figure you refer to in the text. At the moment, this is not consistent.
-	Fig. 4: x-axis is not clear. I think it would be better to use something like ‘water level change (cm)’.
-	Fig. 5: does not seem necessary. I would remove it.
-	Fig. 7: This is more appropriate for an introduction.
-	Table 1: You need to provide a more informative title for the table. The title you provide is specific R-code and may not be informative for all readers. Provide a title that gives a better idea of what was actually tested.
-	Table 1: You should also present the residual degrees of freedom in your ANOVA table so we have an idea of the amount of statistical power you have for your test.
-	It would also be good to include the ANOVA tables of the Fledgling and Hatching success analysis, or at least refer to the supplementary figures in the text (e.g. line 254).
-	I think there could still be some improvements to the written English. It is not a huge issue (it is all mostly easy to understand), but it could help you convey your points more clearly. However, I feel the paper still has to go through some major changes, so I'll make more comments on this when it comes back for further review.

Bayard, Trina S., and Chris S. Elphick. "Planning for sea-level rise: quantifying patterns of Saltmarsh Sparrow (Ammodramus caudacutus) nest flooding under current sea-level conditions." The Auk 128.2 (2011): 393-403.

Burger, Joanna, and Joseph Shisler. "Colony and nest site selection in Laughing Gulls in response to tidal flooding." Condor (1980): 251-258.

van De Pol, Martijn, et al. "Do changes in the frequency, magnitude and timing of extreme climatic events threaten the population viability of coastal birds?." Journal of Applied Ecology 47.4 (2010): 720-730.
Experimental design: You have taken into account the general comments of the reviewers to include statistical analysis; however, your statistics are quite badly flawed. This is a serious issue that needs fixing. I’ve included separate comments on the stats first and then more general comments on the methods section.

Statistics
-	Line 199 – 201: I think the aim of your statistics should be to look at the relationship between water heights/water height change and hatching/fledgling/breeding success. For this to have any meaning, we also need to know what success rates are like when there is no change in water height. Therefore, you should consider ALL your data, not just the data when an event occurred (if you have it).
-	Line 217 – 218: You said you conducted a quadratic transformation on your hatching data, but in the supplementary material it is a square root transformation. Which one did you use?
-	Line 220 – 225: I don’t understand why you have categorised your water height data, why can’t you treat it as a continuous variable as you do in Figure 4? Additionally, the way you have categorised your data is badly flawed. You are testing the effect of water height change on success, but you also based your groupings on nest success (e.g. Light events were 0-6 cm OR events that didn’t cause high nest loss). With this definition you will definitely find an effect of water height change because you have adjusted your groupings based on their success!! If you feel that you need to include some measure of the duration or speed of water change, perhaps you should make your predictor variable rate of change instead (e.g., cm/day). The way you currently structure you data is unusable and needs a serious overhaul.
-	Line 226 – 229: Kruskal-Wallis is a test that we employ if the assumptions of normality aren’t met within our data. If this is the case, you need to say so. If it is not, you can simply carry out the analysis with an ANOVA. Also, you can do Kruskal-Wallis in R, so it might be easier to use all the same analysis software.
-	Line 239 – 242: If you want to discuss this result you should analyse it statistically. You can do this easily with a linear model in R (e.g. lm(Success ~ Depth)).
-	Line 310 - 311: You didn’t mention anywhere how you accounted for predation in your statistical analyses.
-	Line 375 – 377: I guess you mean there is a large variability in how breeding success changes with water levels? The standard deviation of breeding success shouldn’t be more than the mean, otherwise there could be negative breeding success.

General comments
-	Line 120 - 121: Why haven’t you presented mean annual precipitation for the full time series (i.e. 1961 – 2015)? You must have the data if you are able to determine the rainfall during your study period.
-	Line 180: You only include fledglings that remain by the original nest. What about chicks those fledge but leave the area, why are these not considered?
-	Line 185: Previous studies consider all chicks that weren’t found dead as fledged. If you are going to mention this you need to point out why you didn’t use this method (i.e. why is this assumption flawed?).
-	Line 217 and Line 358: If the assumptions of the test were not met, this is called heteroscedastic (i.e. there is a relationship between the variability in the data and the response, in this case water height).
-	You need to point out that your predictor variable, water fluctuation, is a relative measure based on the water height in that year. You currently don’t say this anywhere.
Validity of the findings: I don’t feel that I can comment on the validity of the findings until the statistical analysis has been adjusted (see above).
Additional comments: I think you have taken some steps to improving the manuscript since my last review. A major change from the previous work is your inclusion of statistical analysis (ANOVA) and more in depth figures; however your analysis structure has a number of major flaws (documented in more detail in the comments). I also think that your choice of figures could be improved. I still feel like this work can become a good paper, but very major revisions are still required. Make sure you think more carefully about how you will analyse your data. If in doubt, it may be worthwhile getting some professional statistical advice.


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: INTEGRATED ECONOMIC AND ENVIRONMENTAL ANALYSIS OF AGRICULTURAL STRAW REUSE IN EDIBLE FUNGI INDUSTRY
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript is clearly written in professional language, and the structure, figures and tables are professional. However, many grammar issues still exist, the English language should be improved by professional institute if necessary.
In Line 45, CH4, CO2, Nox, SO2, such chemical formulas should be standardized with subscript like CH4.
Experimental design: Line 99-118, this paragrapgh contains too many words, the aim of this study should be emphasized with a single paragraph.

There is a weakness in the statistical analysis, a lack of descriptive introduction of the sample, which is useful to future readers. It should be improved upon before Acceptance.

Line 144-147, the author said there are four ways…, but in Figure 1, the fourth path (dried out into biofuels) was not displayed, which should be improved upon before acceptance.
Validity of the findings: I commend the author for his/her extensive and excellent work, they compiled the survey data and annual/seasonal reports of the enterprise, the data is robust, statistically sound.

line 323, "......is feasible for technology, economy and environment".  I can not find any related information about "feasible for technology" in the text, please supplement explanation for it, or remove the word "technology,".
Additional comments: The authors seem to have done much work on disposal of or reuse of agricultural straw, it has environmental and economic benefits. And also a bio-economic model –“straw resource utilizaiton for fungi in China” was introduced, which is described with sufficient detail and information. So this work is interesting and is of important significance. However, some typographic errors and discrepancies are found needed to correct in the paper. In addition, some part of the sentences need more clarification for easy understanding therefore the following are some of the corrections recommended for enhancement.
For more information, pls refer to the original manuscript PDF document.


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: INTEGRATED ECONOMIC AND ENVIRONMENTAL ANALYSIS OF AGRICULTURAL STRAW REUSE IN EDIBLE FUNGI INDUSTRY
Review round: 1
Reviewer: 2

Output:
Basic reporting: The article is overall well written, though the writing can be improved. There are places throughout the paper with some grammar mistakes.
Experimental design: The method is overall adequate. However, I think more clarifications are needed for the optimization model. For instance, what type of production function did you use in the model? What are the baseline model parameters?
Validity of the findings: The results make sense. I have a few comments regarding the interpretation of the results. See my general comments to the authors.
Additional comments: 1.	It would be helpful to provide a table of the baseline data used in the optimization model. For instance, what are the prices assumed in the model? What is the production function?

2.	What is the “Material balance approach”?

3.	One thing the authors want to consider is to include the cost of capital in the profit function. Based on my reading, the objective function in the optimization model does not include the cost of capital (opportunity cost of liquid capital). Given the scale of the production considered in your analysis, the capital cost may turn out to be rather large.

4.	In scenario 1, when you relax the production capacity constraint, do you also revise your capital constraint, and potentially other parameters used in the model?

5.	Table 1 scenario 3, why does the water usage go up when the price of fungi goes down by 10%?

6.	Based on table 2, fungi price fluctuations appear to have the largest impact on the net profit, followed by scale, wage, and others. However, in table 3 however, you show that the production scale has the largest effect on the net benefit. Am I missing something?


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: INTEGRATED ECONOMIC AND ENVIRONMENTAL ANALYSIS OF AGRICULTURAL STRAW REUSE IN EDIBLE FUNGI INDUSTRY
Review round: 2
Reviewer: 1

Output:
Basic reporting: The revised manuscript is clearly written in professional logic and structure, the English text is well-improved compared to the last version. Moreover, the revised figure and tables are professional. Apparently, the authors have checked the manuscript thoroughly, and revised every comment carefully.
Experimental design: The model (or method) used in this work is overall adequate, as the other reviewer has pointed out. I think the research design is reasonable and fit for this case study.
Validity of the findings: I noticed that the authors have added several new findings in the revised manuscript. In my point of view, these new findings are closely related to the topic.
Additional comments: The authors have done much work on disposal of or reuse of agricultural straw, it has environmental and economic benefits. And also a bio-economic model –“straw resource utilizaiton for fungi in China” was introduced, which is described with sufficient detail and information. So this work is interesting and is of important significance.


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: INTEGRATED ECONOMIC AND ENVIRONMENTAL ANALYSIS OF AGRICULTURAL STRAW REUSE IN EDIBLE FUNGI INDUSTRY
Review round: 2
Reviewer: 2

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


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

Input:
Title: A NEW SPECIES OF GULO FROM THE EARLY PLIOCENE GRAY FOSSIL SITE (EASTERN UNITED STATES); RETHINKING THE EVOLUTION OF WOLVERINES
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Minor comments:
1) Line 61: 2012, not “2011”.
2) Line 73: “Koufos, 1914”? Should it be Koufos 1982? The latter is included in the References section but nowhere cited.
3) Lines 73–74, 138 and 871: Gidley & Gazin, not “Gazin & Gidley”.
4) Lines 160–161: “Shunk, Driese, & Clark, 2006; Shunk, Driese, & Dunbar, 2009”, not “Shunk, Driese, & Clark, 2006; 2009”.
5) Lines 226 and 578: Bowdich, not “Bowditch”.
6) Lines 227 and 610: Fischer, not “Fischer von Waldheim”.
7) Line 401: “in” is missing between “1.25” and “all other taxa”.
8) Line 482: Kalmykov, not “Kalmykova”.
9) Line 500: Biogeographic analyses of Sato et al. 2012 restrict this area to Asia.
10) The References section lacks Dalquest 1978 (cited in line 217), Eshelman & Whitmore 2008 and Marx & Fordyce 2015 (both cited in line 211), Farlow et al. 2001 (cited in line 195), Gustafson 2012 (cited in lines 184 and 191), Madden & Dahlquest 1990 (cited in line 185), Stehlin 1931 (cited in line 419), Valenciano et al. 2016, 2017 (both cited in line 451), Voorhies 1990 and Janis & Manning 1998 (both cited in line 209), Webb et al. 2008 (cited in line 194) and Wolsan & Sato 2010 (cited in line 88).
11) Burmeister 1850, Eizirik et al. 2010, Gray 1865, Hilzheimer 1936, Kalmykov 2015, Mckelvey et al. 2014, Nadachowski et al. 2011, Orlov 1941, Repenning 1987, Sato et al. 2009, Woodburne 2004 and Yu et al. 2011 are included in the References section but nowhere cited.


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

Input:
Title: A NEW SPECIES OF GULO FROM THE EARLY PLIOCENE GRAY FOSSIL SITE (EASTERN UNITED STATES); RETHINKING THE EVOLUTION OF WOLVERINES
Review round: 1
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: Two points require clarification and additional detail:

1. The interpretation that Gulo and Plesiogulo are morphologically convergent is supported by geochronologic and dental morphological evidence, but no cladistic framework is used. As such, the claim of evolutionary convergence (the concept itself which is defined within a phylogenetic context) is not supported by mapped character distributions over the tree. If no cladistic framework will be used and the authors wish to suggest convergence in those two taxa, I recommend explicitly identifying this interpretation as a speculation.

2. The diagnosis of G. sudorus in the systematic paleontology section provides differentiation between Gulo species, but not between this new species and other non-Gulo gulonines. The differential diagnosis could be improved by citing characters that exclude the new species from membership in other genera.

Please see general comments for specific sections in the manuscript where the two comments above apply.
Additional comments: In this study the authors describe a new fossil species of Gulo, present evidence that early Gulo lived in warmer and wetter environments than indicated by the genus' present range, and suggest that Gulo and Plesiogulo may be convergent in their adaptation for opportunistic hypercarnivory. Overall, the study presents interesting and important new data in understanding wolverine evolution, and also in a re-assessment of the likely geologic age of a very important fossil locality for understanding pre-Pleistocene mammal evolution in North America. As I mentioned in Section 3 ("validity of the findings") above, I recommend making changes to two important aspects of the paper before it is accepted for publication.

Below I include detailed comments on sections of the manuscript:
-Abstract: diagnosis of convergence is contingent upon a cladistic framework, but because no such framework including Gulo and Plesiogulo is presented in this study, I would recommend the authors present this last sentence as a speculation rather than an interpretation supported by phylogenetic evidence.
-L51: Supp. Table 1 is a very useful compilation of Gulo localities.
-L132: any particular reason these two species of Martes were not examined?
-L142: Within Supp. Table 2, the locality name for Plesiogulo crassa ("Paote") should be consistent with the locality for some of the Pekania palaeosinensis specimens ("Baode"). The two names refer to the same locality. "Baode" is the modern Pinyin spelling, whereas "Paote" is the traditional Wade-Giles spelling. Only one system should be used, for consistency.
-L151: Are ETMNH specimens extant and ETVP specimens fossils? Please clarify the distinction between these two collection acronyms.
-L155: should add "(Smithsonian Institution)" after "National Museum of Natural History".
-L196-221: This entire section is a critical reworking of the biostratigraphic evidence supporting a revised estimate for the age range of the Gray Fossil Site. The reasoning and evidence cited herein would be useful for future studies related to the Gray Fossil Site biota as well. Therefore, I recommend the authors include a summary biostratigraphic range chart to accompany this section, to further visualize the evidence for their interpretation of the age of the locality.
-L235: Figure 2 is cited in text before Figure 1. Please consider re-ordering the figures, or cite Fig. 1 in introduction.
-L235 Table 1: please see previous comment regarding the localities "Baode" and "Paote".
-L239: are there characteristics that unite this new species with other Gulo species, and distinguish them from other gulonines? As written, the diagnosis differentiates species of Gulo, but does not address differentiation of the new species from (thus eliminating it from membership in) other genera? From the comparison section below, the lack of the additional median rootlet on P4 may qualify as a diagnostic character between Gulo and Pekania (or more broadly, Pekania with all other gulonines).
-L854 Fig. 4. The placement of the new species described in this study was not based on a cladistic framework, and thus should be indicated as such. The authors should include justification for the grouping of Gulo species shown in this figure; what are the characteristics supporting G. sudorus as the most basal Gulo? Otherwise, it appears as if the phylogenetic relatinoships in this group mainly reflect their chronological order of appearance in the fossil record.


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: COMPARISON OF CLINICAL OUTCOMES AFTER DRUG-ELUTING BALLOON AND DRUG-ELUTING STENT USE FOR IN-STENT RESTENOSIS RELATED ACUTE MYOCARDIAL INFARCTION: A RETROSPECTIVE STUDY
Review round: 1
Reviewer: 1

Output:
Basic reporting: The MS should be checked carefully and some grammar errors need to be corrected, eg. line 73-74, Compared with DES, DEB__an alternative strategy …
Experimental design: No comment.
Validity of the findings: Does the gender difference account for the results?
Additional comments: Please describe the patients' classification in detail. Were the patients divided randomly?


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: COMPARISON OF CLINICAL OUTCOMES AFTER DRUG-ELUTING BALLOON AND DRUG-ELUTING STENT USE FOR IN-STENT RESTENOSIS RELATED ACUTE MYOCARDIAL INFARCTION: A RETROSPECTIVE STUDY
Review round: 1
Reviewer: 2

Output:
Basic reporting: Major comments:
1.	The language of the manuscript should be polished, improve the expression and reorganize some of the paragraphs. For example, “however” in line 116-119, 223-225, should be used carefully.

Minor points:
1.	Format all the literature references, the citation should be inside the hallmarks;
2.	Acute MI could be shortened as AMI;
3.	Figure part, not well labeled and described. Figure 1C legend, line 373, two “at”; Remove the label of "Percent survival" in Figure 1A, 1B and 1C. Remove number at risk in Figure 1.
Experimental design: In this study, Fang et al get the conclusion that DEB is a reasonable strategy for AMI based on a non-randomize single center clinical study by comparing the short-term outcomes with DES. Especially, the average conditions of the AMI patients are worse in DEB group, the 1 year outcome indicators are better than the DES group. The project is meaningful due to high risk of ISR after DES treatment and limited direct evidence of advantages of DEB so far.
Validity of the findings: no comment
Additional comments: no comment


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

Input:
Title: COMPARISON OF CLINICAL OUTCOMES AFTER DRUG-ELUTING BALLOON AND DRUG-ELUTING STENT USE FOR IN-STENT RESTENOSIS RELATED ACUTE MYOCARDIAL INFARCTION: A RETROSPECTIVE STUDY
Review round: 1
Reviewer: 3

Output:
Basic reporting: This is a well-written manuscript that reports the finding of sound and an interesting study revealing new information where the authors have evaluated the efficacy of drug-eluting balloon for acute Myocardial Infarction (MI) with in-stent restenosis (ISR) lesions for the treatment of acute myocardial infarction. There are different guidelines and recommendations for the use of DEB in Europe and America which leaves the surgeons ambiguous about the treatment regimen to be followed. In dearth of studies on the usage of DEB in acute myocardial infarction, the results presented in this study would be helpful to come to a validated conclusion. The authors have compared the differences in clinical outcome between the use of DES and DEB for acute myocardial Infarction with ISR and showed that DEB had good clinical results. The writing quality, clarity of thoughts and knowledge of the subject under study has been demonstrated.  The study is presented well and the results are properly interpreted and correlated with the published literature had no major scientific issues, so I straight away forwarded it for acceptance with minor corrections in English at few places.
Experimental design: The experimental designs are acceptable with a considerable number of patients enrolled in DEB and DES groups.
Validity of the findings: The authors have done a robust study analyzing the wide number of sample and over a long period of time. The clinical outcomes chosen including target lesion revascularization, target vessel revascularization, resurrect MI, cardiovascular mortality etc. are taken into consideration and well supported by statistical analysis.
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: COMPARISON OF CLINICAL OUTCOMES AFTER DRUG-ELUTING BALLOON AND DRUG-ELUTING STENT USE FOR IN-STENT RESTENOSIS RELATED ACUTE MYOCARDIAL INFARCTION: A RETROSPECTIVE STUDY
Review round: 1
Reviewer: 4

Output:
Basic reporting: Fang et al conducted a retrospective analysis to compare the clinical outcomes of DEB and DES in treatment of acute myocardial infraction due to ISR. The authors reported that DEB treatment alone had similar clinical outcomes with DES alone after one-year follow up.  The use of DEB is attractive in clinical setting as it potentially reduces the late-developed stent malapposition and stent thrombosis. The question raised in this study is important and the results are interesting.
Experimental design: This is a retrospective study and the design is sound.
Validity of the findings: The study is limited in this area and the data can support the main conclusion.
Additional comments: Fang et al conducted a retrospective analysis to compare the clinical outcomes of DEB and DES in treatment of acute myocardial infraction due to ISR.  The authors reported that DEB treatment alone had similar clinical outcomes with DES alone after one-year follow up.  The use of DEB is attractive in clinical setting as it potentially reduces the late-developed stent malapposition and stent thrombosis. The question raised in this study is important and the results are interesting.  However there are some major concerns:
1) Currently, It is unclear the role of DEB alone in treating patients with acute myocardial infraction. During this study period, 64% (75/117) patients received DEB treatment while only 36% (42/117) patients received DES treatments. DEB use is pretty high given that this is a retrospective analysis.  What criteria did physician use in clinic to choose the DEB or DES to treat these patients? How could physicians ensure these patients benefit most from the treatments as the basic characteristics are similar between DEB and DES group?
2) The Laboratory examination is limited, with only creatinine was listed in the Table 1. The authors need to show and compare more biomarkers, especially those related with cardiac injury and function, such as TNT, BNP
3) Although there is no difference between DEB and DES in terms of clinical outcome during a short -term follow up, both post-PCI minimal luminal diameter and post-PCI reference diameter are significantly lower in DEB group than those in DES group. How do the authors explain it? Does DEB worsen other cardiac function?  Did these patients receive echocardiography before and after PCI? This is important and needs to be analysis more. These results should also be described in Abstract.
4) The language is poor and confusing throughout.  It needs to be reviewed and edited by a native English speaker.


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: COMPARISON OF CLINICAL OUTCOMES AFTER DRUG-ELUTING BALLOON AND DRUG-ELUTING STENT USE FOR IN-STENT RESTENOSIS RELATED ACUTE MYOCARDIAL INFARCTION: A RETROSPECTIVE STUDY
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: This manuscript has been revised and answered the concern.


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: COMPARISON OF CLINICAL OUTCOMES AFTER DRUG-ELUTING BALLOON AND DRUG-ELUTING STENT USE FOR IN-STENT RESTENOSIS RELATED ACUTE MYOCARDIAL INFARCTION: A RETROSPECTIVE STUDY
Review round: 2
Reviewer: 2

Output:
Basic reporting: The authors have addressed my questions. I recommend acceptance of the manuscript.
Experimental design: The authors have addressed my questions. I recommend acceptance of the manuscript.
Validity of the findings: The authors have addressed my questions. I recommend acceptance of the manuscript.
Additional comments: No additional comments


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

Input:
Title: THREE-DIMENSIONAL ARCHITECTURE OF THE WHOLE HUMAN SOLEUS MUSCLE IN VIVO
Review round: 1
Reviewer: 1

Output:
Basic reporting: The authors have submitted a very clearly written and presented manuscript. The article is well structured and results are relevant to the posed research questions and the figures are of high quality.
Links are provided to data files, which appear complete and are clearly documented with appropriate 'Read me' files.

The references cover the majority of relevant literature, although there do seem to be a couple of omissions:
1. Rana et al., (2013) J. Applied Physiology (115(1): 116-125) have reported ultrasound derived 3D fascicle orientations in the triceps surae, including soleus muscle. This should be mentioned in the literature review of the introduction and it would also be useful to include in the comparison of results described in the discussion section;

2. The authors suggestion of different roles for the anterior and posterior compartments of the muscle is supported by their data, and such partitioning of functional roles within muscle is not new. Again for completeness there should be some reference to previous work that has outlined similar ideas - for example: English et al., (1993) Physical Therapy 73: 857-867 - which will help readers interested in this topic access additional evidence for such ideas;

3. leading on from the comment above, it would also help strengthen the discussion if the manuscript indicated how different functions of the compartments could be controlled by the nervous system. As such reference to work that has shown 3d network of nerve branches through soleus and how they seem to parallel the architecural partitions would be valuable, eg. Loh et al., (2003) Clinical Anatomy 16: 378-382
Experimental design: The manuscript fits the aims and scope of the journal.
The manuscript clearly  articulates how the work fills an identified gap in current knowledge and the methods used are innovative and performed to high technical and ethical standards.

The methods are in the most part described with sufficient detail, there are however a couple of areas where more information would be valuable:
1. methods L124 readers are referred to another publication for the scan setting details. For completeness it seems as though details should also be provided within this manuscript, to ensure that it stands alone as a self-contained piece of work with sufficient detail for replication;

2. There is no reference to the ethical approval number or associated documentation for the cadaver data;

3. Lines 165-167 describes the settings for the fibre tracking. It would be useful to know whether these were established using some form of standardised optimisation approach (and if so what was the protocol?); whether they are based on past experience of working with images of other muscles and/or whether they are specific to the soleus images analysed here.

4. As part of the fixing process for the cadaveric muscles, were they pinned or stretched to a certain length at all? I was left wondering whether the cadaver material could be equated to one or other of the ankle joint angles studied in the live participants? It could help in relating these two aspects of the study it were possible to make some indication on this point, maybe in the methods or discussion.
Validity of the findings: The data appear to be robust with sound statistical analysis. The conclusions are well stated and link to the original aims of the manuscript. There were a couple of areas for consideration:

1. L238 in results, states curvatures were 4 degrees larger in the posterior compartment. If this is curvature should it not be reported as /m or does this point refer to pennation angle?

2. Lines 242-244, reports that for every cm of MTU lengthening there were given changes in fascicle lengths, pennation angles and curvatures. However, this does assume a linear or constant change, which may well not be the case as the muscle transitions from shorter to longer lengths (e.g. Herbert et al., 2011 J. Physiol), this could be noted in a relevant place within the manuscript.

My final comment here is related to those made in the first section of the review, where reference to previous work suggesting partitioning of roles within muscles should be made; and links to possible pathways open to the nervous system to indepedently control different regions of the could muscles also be made.
Additional comments: Overall, this was a very enjoyable and interesting manuscript to read. It is good to see new information regarding in vivo muscle anatomy being presented.

The only additonal thought I had with regard the presented work was the potential for differential sensory feedback from structures, such as muscle spindles, from across the different muscle compartments. There could be potential of interplay between different intramuscular regions for the nervous system to 'understand' changes in soleus lengths and also possibility to have regional patterns of activation with sensory feedback from 'quieter' portions of the muscle. This may be something the authors wish to consider within the discussion as to the potential value of having such compartmentalised muscles, although I appreciate it would be speculation rather than facts these data support. I present this comment really as a point I thought the authors may find interesting to consider.


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: THREE-DIMENSIONAL ARCHITECTURE OF THE WHOLE HUMAN SOLEUS MUSCLE IN VIVO
Review round: 1
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: We thank the authors for this interesting work, which have reported in-vivo the architectural properties of the soleus. Here are my comments/suggestions.
line 19: I suggest to add the words dorsiflexion and plantarflexion for a better understanding of the ankle joint position
line 69: ‘With ultrasound, measurements can usually only be obtained from the most superficial (posterior and distal) compartment of the muscle’ This is a quite strong statement. Could you provide more information to support such statement or alternatively make this sentence more soft by saying that it depends on the US system used.
Line 112: how is the ankle passively dorsiflexed during the acquisition? Did you use any device to keep the joint in such position?
Line114-116. This part is not clear for me. I don’t understand how you achieved slack length of the medial gastrocnemius in dorsiflexion. I assume you mean ‘plantarflexion’ instead of dorsiflexion. Then you mentioned 108 deg in dorsiflexion: this I think is in plantarflexion. Please clarify this part.
Line 132. I think it is an useful information to mention (on average) the number of images outlined.
Line 138. This is a critical part. I understand that the DTI data were also used to support the segmentation but it is still unclear how you merged the two information (segmentation using MRI data and using DTI). As you mentioned, the muscle border is not always clear. Therefore, is it possible to provide some reliability data for the relevant outcomes (volume , fascicle lengths, pennation angle and curvature)?
I think it is important to discuss this limitation and eventually new reliability data in the discussion. This is useful for the reader in order to interpret correctly your relevant dataset .
Line 272. Could you explain the differences in terms of volume among your study, Ward and Hodgson?


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: THREE-DIMENSIONAL ARCHITECTURE OF THE WHOLE HUMAN SOLEUS MUSCLE IN VIVO
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors have satisfactorily addressed all my previous comments. I consider that the manuscript now meets all PeerJ criteria in terms of basic reporting.
Experimental design: Again the authors have addressed all the comments I previously made and I consider that the manuscript reaches the standards required for publication.
Validity of the findings: All my comments have been met, with the conclusions being well stated, linked to the original research question and well described in the context of previous work.
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: THREE-DIMENSIONAL ARCHITECTURE OF THE WHOLE HUMAN SOLEUS MUSCLE IN VIVO
Review round: 2
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: Regarding my previous comments on the images outlined, could you add which was the rationale of choosing the number of images to be outlined? For example, did you make the segmentation every 5 mm?

To me, it is not entirely clear how you ended up with 6.3% (root mean square difference between volumes). I guess this number is an average among the different parts of the soleus, but how it is currently written in the result section seems related to the whole muscle volume. I suggest to rewrite that part.

In addition, since you mentioned that discrepancies larger than 2% mean errors in the segmentation, in the discussion I would add a sentence saying that the value of 6.3% obtained suggests possible errors in the volume extraction. Also acknowledge in the discussion that this reliability analysis is missing for the other variables.

I understand that the DTI was helpful for the segmentation but it is still unclear how the relevance for its contribution. I think it would be interesting to know how worse the reliability without the DTI data is. Anyway, I am not asking another investigation, but to just mention this point as possible future analysis
Validity of the findings: no comment
Additional comments: I thank the reviewer for the detailed revision. I just added few minor 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: CAN PHOSPHORUS APPLICATION AND COVER CROPPING ALTER ARBUSCULAR MYCORRHIZAL FUNGAL COMMUNITIES AND SOYBEAN PERFORMANCE AFTER A FIVE-YEAR PHOSPHORUS-UNFERTILIZED CROP ROTATIONAL SYSTEM?
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript by Higo et al give an investigation concerning AMF community diversity and phosphorus application in soybean roots with different rotation systems. The authors found that P application and crop rotational systems changed the diversity and community composition of AMF and AMF diversity influenced positively plant biomass, plant P uptake and grain. Experimental settings have a certain degree of rationality, the author did a lot of work and the data is also very abundant. Literature references, sufficient field background/context were provided. I suggest that the data of 2014 can be placed in the supplementary information.
Experimental design: Original primary research within Aims and Scope of the journal. Research question well defined, relevant & meaningful. However, the Methods for describing Statistical analysis  were not very detailed, it should be written more substantial.
Validity of the findings: The discussion is badly organized and is not real discussion. So much redundant information presented in the Result and Discussion. I am not convinced the data and statistics support the authors' hypotheses in the current version.
Additional comments: The manuscript by Higo et al give an investigation concerning AMF community diversity and phosphorus application in soybean roots with different rotation systems. The authors found that P application and crop rotational systems changed the diversity and community composition of AMF and AMF diversity influenced positively plant biomass, plant P uptake and grain. Experimental settings have a certain degree of rationality, the author did a lot of work and the data is also very abundant. However, this is not very novel. The impact of P on AMF community diversity and composition has been studied too much and the technological means of PCR-DGGE is relatively backward in microbial community research. I consider that there are many more advanced technical methods to do it. The Methods for Statistical analysis part was not very detailed, it should be written more substantial. In addition, the pictures are too hasty to publish, it would require repaint them better especially the last figure for network analysis.
This MS have two years of data in the text section so that it is difficult to catch the main idea. I suggest that the data of 2014 can be placed in the supplementary information and the author can discuss the data for 2015 in more detail, so the article will be more purposeful and convincing. The discussion is badly organized and is not real discussion. So much redundant information presented in the Result and Discussion. The discussion seems too superficial. I am not convinced the data and statistics support the authors' hypotheses.
All of the tables were hard to comprehend, it is better to changes these tables to figures.

It’s not necessary to present the data of 2014 in the body text, or you can consider showing it in the supplementary part.

Table 2: how do you link the aboveground plant biomass or other growth performance at R2 with the grain yield? It will be more scientific to characterize the differences of these growth performance from R2 to maturity stage, and analyze how the AMF root colonization affect P absorption and utilization during this stage.

Line 194:  All test for tables were not provided. Please describe in detail.

Line 199 - 201: Please provide more details of RDA analysis and how did you define the all the environmental factors in Figure 1.

Line 280 – 286: How did identify these species of AMF? Please describe in detail.

Line 290: The legend describes of Figure 1, please change the “between” to “among”.

Line 290 - 293: The Monte-Carlo permutation test is used for whether the environmental factors explain the distribution of the community is significant. Please use PERMANOVA to test the AMF communities in different treatments.

Line 306 – 331: Different correlation lines should be represented by different types of segments and please provide more clear pictures.

Line 325 - 326: The Figure 3 was too hasty and should be repainted.

Line 352 - 357: You did not detect any functional traits, so, the discussion is a little bit desultory. Do these discussions make any sense to any of the conclusions?

Line 404: Remove “molecular”.


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: CAN PHOSPHORUS APPLICATION AND COVER CROPPING ALTER ARBUSCULAR MYCORRHIZAL FUNGAL COMMUNITIES AND SOYBEAN PERFORMANCE AFTER A FIVE-YEAR PHOSPHORUS-UNFERTILIZED CROP ROTATIONAL SYSTEM?
Review round: 1
Reviewer: 2

Output:
Basic reporting: Overall, I think that the manuscript could benefit from additional polishing to tighten the language and avoid redundancy, to ensure that the message being conveyed is clear and consistent throughout. Below are some examples I’ve highlighted throughout reading the manuscript:

The introduction does need to be expanded a little bit:
1)	Lines 39-43: It would be good to mention the economic cost of fertilizer application over time. Do you have a reference that states that growers are applying less b/c of the cost?  Also this first sentence does not clearly convey what your point: That the increasing costs is deterring growers from applying required levels of P containing fert. In these first few introductory sentences, it would also be good to get an idea of the environmental impact of P-containing fertilizer and why this necessitates a green revolution.
2)	Lines 43-51: Can you give a couple examples of key AMF species and their benefits?
3)	Lines 48-51: Redundant with the previous sentence.
4)	Paragraph starting on line 53- at first pass, it is not clear that you are trying to give examples of management examples. Maybe re-work the first sentence?
5)	Line 63-64: You need a citation that shows some stats / why Japanese growers are decreasing use of winter cover crops.
6)	Line 67 and line 70: Please define what is meant by AMF composition and AMF diversity. It is not clear in how it is presented throughout the paper.
7)	Paragraph starting on line 76: The first sentence is not clear- “In contrast, it is well known that a decrease occurs in AMF root colonization…”  You can be clearer of what is intended by stating AMF root colonization is decreased following….
8)	Line 78: “Specifically, Brassicaceae crops are not ..” This sentence is awkwardly worded. It makes it sound that the crop cannot establish a symbiotic relationship with itself.
9)	Paragraph starting line 93: This paragraph is overall a bit redundant, consider revising. Also the stated hypothesis is a complicated in its wording.
Experimental design: In this section, the authors could further expand on the experimental set up. From what is written in lines 116-130. For example:
1)	It is not clear at first that the authors replicated their experiment in 3 plots per P treatment. Also, it is not clear until the reader makes it to lines 144-157 that 10 individual replicated plants were included in each plot .
2)	It would be good to know what accounts for the differences in P in the plots between the two sampled years. (If it can be explained).
3)	Line 161- 162: Provide a reference for the molybdenum yellow colorimetric method.
4)	Line 166-177:
a.	“The DNA samples from the roots were used for the PCR templates after a 10-fold dilution”- what concentration was achieved?
b.	Provide the primer sequences and thermocycler protocols for each set.
c.	Can you please tell the reader why you chose to amplify the 18S SSU rDNA, AM1, NS31?
5)	Lines 179-187: What DNA ladder was used?
6)	Lines 189-192: Please provide the reader with the specific primer sets and thermocycler protocol.

Statistical analysis:
1)	Lines 195-206:
a.	Please clarify what the Monte Carlo permutation test was aiming to do. From this section and from the Results section, it is implied that the permutation is testing the significance of the quadrants from the RDA output. If that is true, then that should be described in this section and reiterated in the results section as well.
b.	By looking at the tables reported within the manuscript, it appears that the statistics carried out were performed based on 3 replicates. Does this mean that the replicates within each plot (n=3), were averaged and this is what was used for the analysis described there?
c.	What correlation test was performed for the data reported in figure 2 and 3? Spearman/Pearson?
d.	How does the data from the two years correlate for plant measurements?
Validity of the findings: VALIDITY OF THE FINDINGS
1)	The network model nicely illustrated in a figure the observations they had made and reported throughout. The most notable finding from this is the role that AM colonization and AM abundance has on Plant biomass and their relationship with Plant P uptake and available Soil P.
Additional comments: RESULTS:

1)	Diversity of AMF communities and abundance:
a.	Line 259: Please provide a reference for the use of DGGE bands for species richness. How is this measure useful / different  or compare to just only using the Shannon index?
b.	Paragraph starting on line 277: I am assuming that the AMF taxa was identified via qPCR as described in materials and methods. It is not clear from how this paragraph is started out that these taxa were identified via that method. Can you also elaborate as to why this method is a relevant measure to indicate the abundance of these species? Can you mention in the materials and methods how the samples were normalized? It seems like this method could bias the representation of the AMF taxa if the preparation method did not standardize the quantity of the cDNA.

2)	Relatedness factors to AMF communities:
a.	Please see my comment in the statistical analysis.
b.	List the quadrants (I-IV).
c.	List each RDA plot as A and B.

DISCUSSION:
1)	Line 334: The stated hypothesis starting on line 93 does not match the reiterated hypothesis starting on this line.
2)	Line 339: “However, other more important factors can be involved”, like what??
3)	Line 366-369: Point is not clear here.
4)	Line 389-391: What is meant by a net cost?

COMMENTS ON FIGURE LEGENDS:
Figure 1: Please divide up each RDA into quadrants, this will make it easier to discuss in the results section where you report the associated p-values from the Monte Carlo.

Figure 2: What correlation test was done? State that in legend. Is each correlation significant? That should be stated in the results.

Figure 3: How was each correlation value derived? Spearman/Pearson? State it in the legend.

Figure S1 and S2: It would be good if the lanes could be better labeled with their target names and also if the DNA ladder could be annotated.

GENERAL COMMENTS
I think the authors should prepare the reader for the caveats of the benefits of P and AMF in the introduction, so that once the reader gets to Figure 3 and reads through the discussion, it doesn’t seem like the findings reported here contradict what was known previously. Also, it would be good to mention this finding in the abstract, as I think it is key to 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: CAN PHOSPHORUS APPLICATION AND COVER CROPPING ALTER ARBUSCULAR MYCORRHIZAL FUNGAL COMMUNITIES AND SOYBEAN PERFORMANCE AFTER A FIVE-YEAR PHOSPHORUS-UNFERTILIZED CROP ROTATIONAL SYSTEM?
Review round: 1
Reviewer: 3

Output:
Basic reporting: Revision of English language by a native is needed.
Manuscript should be condensed and guiding thread shoul be improved.
Introduction, discussion and conclusions are the weak points of the manuscript. They need a revision.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Abstract:
Only part of the results are mentioned. Discussion is poor.

Introduction need to be improved. Hypothesis should better support in introduction.
Guiding thread and connection with the rest of the document shoul be improved.

Material and methods: phases of the research shoul be better explained.

Results: they are interesting but the text is very repetitive, information is already shown in tables.

Discussion: main messages and guiding thread of each paragraph and, in general, of the whole discussion shoul be improved.
There are many and interesting results but some of them are poorly discussed or not discussed at all, i.e. the influence of cover cropping, and specifically the effect of the different species of cover crops (or fallow). In addition, the RDA analysis (Fig.1), or the impact on the abundance of different AMF taxa (and the meaning of that) (Table 4) are not discussed.  In contrast, there is a paragraph poorly connected with results (Lines 382-395).

Conclusions: Conclusions need to be improved to better link to original research question and be limited to supporting results.

References:
Gilbert et al, 2000 instead of 2009
Njeru, instead of Njel
Schernier and Koide 1993 does not appear in list of references.
Kowalchuk et al, 2002 instead of 2001
Hicks and Loynachan 1987; does not appear in list of references.
Treseder 2002 instead of 2008
Liu et al 2015 instead of 2005 in list of references.
Alguacil et 2010 does not appear in the text
Higo et al. 2010 does not appear in the text

See comments on 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: CAN PHOSPHORUS APPLICATION AND COVER CROPPING ALTER ARBUSCULAR MYCORRHIZAL FUNGAL COMMUNITIES AND SOYBEAN PERFORMANCE AFTER A FIVE-YEAR PHOSPHORUS-UNFERTILIZED CROP ROTATIONAL SYSTEM?
Review round: 2
Reviewer: 1

Output:
Basic reporting: Compared to the previous version, the latest manuscript has been greatly improved. The author earnestly answered all the questions that I had rasied. I do not think there is a big problem in the latest, except that the author should put all names of R software packages and functions into italics in the Statistical analysis section.
Experimental design: No problem.
Validity of the findings: No problem.
Additional comments: No problem.


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: CAN PHOSPHORUS APPLICATION AND COVER CROPPING ALTER ARBUSCULAR MYCORRHIZAL FUNGAL COMMUNITIES AND SOYBEAN PERFORMANCE AFTER A FIVE-YEAR PHOSPHORUS-UNFERTILIZED CROP ROTATIONAL SYSTEM?
Review round: 2
Reviewer: 2

Output:
Basic reporting: The manuscript still needs a fair bit of polishing. Please see commented manuscript attached.
Experimental design: The research phases are not well described. Please state why the experiment was broken into phases to better understand the flow.
Validity of the findings: no comment
Additional comments: Dear author,

Thank you for incorporating our suggestions. After careful reading, I think that the manuscript could still use a bit of polishing. In the next edits, redundancy can be further reduced and also pay attention to sentence and paragraph structure. I found some misspellings and typographical errors as well and have noted that in the track edits.


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: CAN PHOSPHORUS APPLICATION AND COVER CROPPING ALTER ARBUSCULAR MYCORRHIZAL FUNGAL COMMUNITIES AND SOYBEAN PERFORMANCE AFTER A FIVE-YEAR PHOSPHORUS-UNFERTILIZED CROP ROTATIONAL SYSTEM?
Review round: 2
Reviewer: 3

Output:
Basic reporting: The new version was greatly improved compared with the original one, but it still needs changes for publishing.
Manuscript is sometime redundant and may be condensed a little more. Try to be more concise.
Despite suggestion of one of the reviewers, it is better to keep both years data in the main results. It seems strange that most figures (2-6) correspond to 2015 data but the last two figures (7 and 8) correspond to both year data. If 2014 data are kept as complementary information, please, justify this decision and provide some comments (not as detailed as with 2015).
Still explain better the two phases of experiment. It seems to be a split-plot design.  The P fertilization is not clear in Phase 2.
Have you considered in the statistical analysis that it is a split-plot design?
Sometimes, results in the text are quite confusing and contradictory (mainly regarding figures 2-4). In some cases, the new text contradicts the original one. Text may be condensed in results.
Discussion is better in the new version but still needs some changes.
Indicate in figures that you used Tukey test.
Figures 5 and 7 are small and difficult to read.
Improve conclusions and remark the take-home message of the manuscript.
Revise references: Thonar et al, 2012 (2011) ; Wakelin et al 2012, Njeru et al 2014, Johnson et al, 1992, 2010a, 2010b.

Detailed comments in the manuscript.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: no comment


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

Input:
Title: CAN PHOSPHORUS APPLICATION AND COVER CROPPING ALTER ARBUSCULAR MYCORRHIZAL FUNGAL COMMUNITIES AND SOYBEAN PERFORMANCE AFTER A FIVE-YEAR PHOSPHORUS-UNFERTILIZED CROP ROTATIONAL SYSTEM?
Review round: 3
Reviewer: 1

Output:
Basic reporting: Basic reporting has improved since the last draft. Thank you for incorporating our suggestions. I did not find Figure descriptions for the supplemental figures. Also please indicate Marker sizes and also indicate which marker was used to compare amplicon sizes. Also, in each supplemental figure, there are 3 lanes per cover crop indication, however it is not clear whether each lane corresponds to a given AMF. Please have this indicated either in the figure or in the description.

In order to be clear to the audience, please remind your reader in the figure description that they are looking at data collected from 2 different P-application doses. It otherwise misleads the reader to think that the experiments carried out in the two years are fully repeated experiments.

I would also be interested in your interpretation of how a leguminous cover crop may impact soil nutrition and therefore your 2015 plant growth results. Did you perform any nutrient testing of the plots after each subsequent cover crop rotation?

I would like it if the author could label the quadrants of Figure 5 as they are described in text (i.e. quadrants I - IV).
Experimental design: Please state the developmental stage that the experiments were executed at. This information was provided in the results & figures descriptions, but not in the experimental design. Also, it should be stated why the researchers decided to apply a 3X Phosphorus application and also whether the researchers tested soil nutrition for 2015 as done in 2014 to account for differences in plant growth between the two years. Even the controls were larger in 2015. Was this increase hypothesis driven? Why was this not included as an experimental factor in the experimental design prior to initiating the studies?
Validity of the findings: Overall it seems like the authors did not find similar trends in the AMF population due to P application as was reported in previous literature. This is a point that is discussed, but I think that it would be good to get an understanding of how previous studies differ from the current one (i.e. growth chamber, greenhouse field experiments?) I raised this question in the discussion.
Additional comments: Overall, the manuscript has improved. There are some sentences that could benefit from clarification and help guide the reader as to why certain experiments/tests were performed. I made explicit comments/suggestions where further clarification is needed.


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: CAN PHOSPHORUS APPLICATION AND COVER CROPPING ALTER ARBUSCULAR MYCORRHIZAL FUNGAL COMMUNITIES AND SOYBEAN PERFORMANCE AFTER A FIVE-YEAR PHOSPHORUS-UNFERTILIZED CROP ROTATIONAL SYSTEM?
Review round: 3
Reviewer: 2

Output:
Basic reporting: The new version was greatly improved. However, after so many punctual changes, the manuscript needs a global revision in order to be more concise and improve the style and readability of the text.

Please, see manuscript with comments.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: no comment


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

Input:
Title: CAN PHOSPHORUS APPLICATION AND COVER CROPPING ALTER ARBUSCULAR MYCORRHIZAL FUNGAL COMMUNITIES AND SOYBEAN PERFORMANCE AFTER A FIVE-YEAR PHOSPHORUS-UNFERTILIZED CROP ROTATIONAL SYSTEM?
Review round: 4
Reviewer: 1

Output:
Basic reporting: Improved basic reporting, addressed all concerns in previous revision.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: Dear author,

Thank you for addressing the suggestions. The manuscript has improved greatly.

Best wishes!


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

Input:
Title: CAN PHOSPHORUS APPLICATION AND COVER CROPPING ALTER ARBUSCULAR MYCORRHIZAL FUNGAL COMMUNITIES AND SOYBEAN PERFORMANCE AFTER A FIVE-YEAR PHOSPHORUS-UNFERTILIZED CROP ROTATIONAL SYSTEM?
Review round: 4
Reviewer: 2

Output:
Basic reporting: The manuscript has been improved but still needs further improvements. It could be more condensed. Main messages should be clearly presented.
Experimental design: No comments
Validity of the findings: No comments
Additional comments: Please see comments in the document attached.
As I suggest to remove some studies, references were not checked.


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: STABILITY OF AN OPHTHALMIC FORMULATION OF POLYHEXAMETHYLENE BIGUANIDE IN GAMMA-STERILIZED AND ETHYLENE OXIDE STERILIZED LOW DENSITY POLYETHYLENE MULTIDOSE EYEDROPPERS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript is written clearly and in proper English. The Introduction provides a large amount of background information which is cited appropriately. Figures and tables are appropriate and the raw data is supplied.
Experimental design: The research question is well defined and relevant. However I believe another measure of stability should have been performed. As a microbiologist, I believe that a bioassay demonstrating antimicrobial activity against a number of bacteria or Acanthamoeba isolates should have been performed to demonstrate antimicrobial similar activity at the various time points.
Validity of the findings: I believe the data is valid, but lacking antimicrobial biological activity data.
Additional comments: I commend the authors for a well-written manuscript describing the stability of PHMB eye drops over three months and contained in bottles sterilized using different methods and at different storage temperatures. A number of assays were used to analyze the PHMB concentrations over time, osmolality, pH, and breakdown products over time. The concentration of PHMB was determined using LC. While I believe that determining the PHMB concentrations and breakdown products over time is very important to demonstrated chemical stability, the authors do not demonstrate that the biological activity of PHMB was not affected. Bioassays, such as MIC testing or time-kills against standard bacterial isolates or the use of an Acanthamoeba complete-kill assay (Kowalski RP, Abdel Aziz S, Romanowski EG, Shanks RMQ, Raju LV. Development of a Practical Complete-Kill assay to Evaluate Anti-Acanthamoeba Drugs. JAMA Ophthalmol 2013;131(11):1459.) to determine bioactivity would have provided important supplemental data for this study. I believe that stability testing of all antimicrobials should be tested against susceptible and resistant organisms to determine whether there is any degradation of biological activity. If the authors do not have this data to include in this manuscript , then this point should be discussed as a limitation of the study in the manuscript and the reason why it was not done also included.

Minor Points
Line 73: It is stated that Acanthamoeba trophozoites are “sensitive” to antibiotics. Microorganisms are not “sensitive” to antibiotics, they are “susceptible”.

Line 88: The Gram in Gram-positive and Gram-negative should be capitalized as Gram is a proper name.

Lines 109 - 112: It is stated on lines 109-112 “The objective of this study was to assess the physicochemical and microbiological stability of a PHMB 0.2 mg/mL (0.02%) ophthalmic solution in two different low-density polyethylene multidose eyedropper, at two conservation conditions (5 °C and 25°C) for three months in unopened eyedroppers and during 10 hours of simulated patient use. It is stated that the “microbiological stability” of PHMB was assessed. Reading this, I am expecting to see microbiological data such as MICs, and not sterility data of the solutions. This statement should be reworded as the readers do not misinterpret the intent of the statement, so as to expect antimicrobial data rather than sterility of the solutions over time.


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: STABILITY OF AN OPHTHALMIC FORMULATION OF POLYHEXAMETHYLENE BIGUANIDE IN GAMMA-STERILIZED AND ETHYLENE OXIDE STERILIZED LOW DENSITY POLYETHYLENE MULTIDOSE EYEDROPPERS
Review round: 1
Reviewer: 2

Output:
Basic reporting: See uploaded PDF file
Experimental design: See uploaded PDF file
Validity of the findings: See uploaded PDF file
Additional comments: See uploaded PDF file


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: VOLUNTARILY CONTROLLED BUT NOT MERELY OBSERVED VISUAL FEEDBACK AFFECTS POSTURAL SWAY
Review round: 1
Reviewer: 1

Output:
Basic reporting: Overall this manuscript is clear and the topics is worth investigating, and the hypotheses are supported by previous literature. My only suggestion would be to have an native English speaker proofread the manuscript before re-submission. Further comments are addressed in the attached pdf.
Experimental design: Overall the experimental protocol is well-described and adequate to test the hypotheses. My major concern relates to the use and interpretation of DFA. My detailed comments can be found in the attached pdf, but I want to highlight the principal comment here: the authors suggest that the lower DFA values observed in the voluntary-control group reflect 'more' self-similarity, which is not the case (deviations toward 0.5 reflect less persistence).

While the rest of the study is very clear and rigorous, it seems that the application of DFA is lacking rigor and a clear rationale. As mentioned in the attached pdf, I suggest the authors to either remove completely DFA analyses (which may be necessary due to the very low sampling rate, 30 Hz; see Rhea et al., 2015), or to dig deeper in the analysis and interpretation of the results (e.g., DFA of CoP velocity, taking into account the cross-overs, etc.).
Validity of the findings: With the exception of DFA results, the results seems valid and tend to support the hypotheses.
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: VOLUNTARILY CONTROLLED BUT NOT MERELY OBSERVED VISUAL FEEDBACK AFFECTS POSTURAL SWAY
Review round: 1
Reviewer: 2

Output:
Basic reporting: Imaizumi and colleagues investigated how the intentional control of visual feedback of postural sway influences the balance control of healthy adult participants, during quiet standing. They found that visual feedback increased the postural sway of individuals who voluntarily controlled the visual feedback. They suggested that the visual system is integrated into the postural control system by the closed visuo-postural loop mechanism.
The study is clearly and adequately written. It contains a nice historical review of studies of visual feedback and its effect on postural sway. While the study provides new knowledge about the effect of visual sensory information in control of posture during quiet standing, there are some issues that require the authors' attention.

Lines 65-66: be more specific in this sentence “…effectiveness and feasibility for patients”. What kind of patients you referee to?
Experimental design: The authors should state more clearly the possible contribution, implications or relevance of the present study to the field of research.

Line 142: the authors state that the participants had normal visual acuity. Did you make any test? How was it verified?

Besides the Wii balance board has been considered to be “…a valid and reliable measurement of postural sway….” as stated in the text, it is known that this device has some limitations (inconsistent sample rate, COP signal error and calibration method). Did the authors calibrate the equipment? What calibration method was used? How did you solve the question regarding to sample rate? Maybe re-sampling the raw data to ensure a consistent sample rate might help with this issue.
I suggest that such questions and limitations should be clearly presented in the text, the methods section needs some improvement.
Validity of the findings: The results are clearly described and alternative interpretations are discussed.

Lines 380-383: I suggest revising this sentence. The larger postural sway does not necessarily can be interpreted as a postural instability. It should take in account that central, peripheral and mechanical factors lead to spontaneous changes in the body reference configuration, the individuals make constant postural corrections during quiet upright standing posture.

Lines 472-473: the authors should be cautious when using a specific interpretation: “….sway area, which reflects how widely CoP fluctuates, originates from vestibular functions.” The amplitude of COP displacement is not necessarily originated from vestibular function, but also may reflect the mechanical properties of the body required for postural stability during upright standing.
Additional comments: The manuscript was carefully written and I appreciate the effort to collect such a data.

The study provides novel results about the effect of visual sensory information in control of posture during quiet standing, however there are some issues that require the authors' attention.


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: VOLUNTARILY CONTROLLED BUT NOT MERELY OBSERVED VISUAL FEEDBACK AFFECTS POSTURAL SWAY
Review round: 1
Reviewer: 3

Output:
Basic reporting: The present manuscript has clear and professional English, achieving the journal standards regarding structure, figure quality and raw data supplied.

Concerning the INSTRODUCTION, it is clear and well-structured. The introduction is full of references about all it has been done in postural control and the effect of visual feedback. However, I miss an explanation about the relevance of the main aim of the study. In addition, I have some questions that are indicated in the reviewed PDF (please, check the comments). The main problem of this experiment is in the EXPERIMENTAL DESIGN, please, check the specific comments in the experimental design section and the comments in the reviewed PDF. The RESULTS and DISCUSSION are influenced by the design so I will wait to review them when the issues will be addressed, although, the authors can see some specific comments in the reviewed PDF.
Experimental design: In my humble opinion, the design of the experiment is not the most appropriate to address the goal of the study, it has some scarcities. The manipulation of the level of intention to control the visual feedback through the given instruction has some issues:

1. The answer of the participants to the question "to what extend did you feel that you were controlling the moving square? could be influenced by the instruction the authors gave to the participants. In other words, if the researcher said to the participant: do not pay attention to the moving square, and 30 s later the researcher asked him/her: did you pay attention to the moving square?... What do you think the answer is going to be? That could have happened or not but it is something out of the control of the researchers.

2. Despite the previous issue, the "sense of control" is a subjective variable that has been used in previous studies to assess the feel of controlling the movement. However, those studies, it has been used to compare the level of intention within one only group. It is said, they compared the level of controlling the movement of the participants in one situation with the level of controlling the movement of the same participants in another different situation. However, in this study, the authors have compared the rating of this variable between different groups giving different instructions. How could the authors know that the differences between groups are caused by the instruction if they do not know if both groups exhibit differences under the same situation with the same instruction?

3. The same problem exist with the rest of the variables, not just the sense of control. How do we know that the differences found are caused by the manipulation of the introduction, gain or flipped condition?

From my point of view, this big problem needs to be addressed. I suggest the following idea: using the same 2 groups, assess their postural control (all the variables used in the study) and the sense of control under the same exact situation, with the same instruction. You could use the situation where you ask them to pay attention to the moving square or the one where they should not pay attention to it, even both.
In that way, the authors will be able to check if the groups are or not different in all the used variables in the study. Thus, if they are not different the results of the study can be related to the given instruction, the gain or the horizontal flipped condition.

In addition, a better explanation about why the gain and the flipped condition are included in the study is needed.

Regarding the description of the method, the ethical standard and so on, I believe the authors did a great job. However, a better definition of the research question and to fix the big problem in the design of the protocol need to be addressed.
Validity of the findings: The design of the experiment needs to be improved to be able to evaluate the validity of the findings.
Additional comments: The main idea of the paper is interesting and the authors could find relevant discoveries for postural control research but several aspects of the paper need to be improved, mainly the design of the protocol.

Apart from these comments, please, check the specific comments in the reviewed PDF. I hope you find my suggestions 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: VOLUNTARILY CONTROLLED BUT NOT MERELY OBSERVED VISUAL FEEDBACK AFFECTS POSTURAL SWAY
Review round: 2
Reviewer: 1

Output:
Basic reporting: The manuscript quality has improved, in particular the English.
Experimental design: The research design is thoroughly described and seems very rigorous.
Validity of the findings: The findings supports the conclusions. Limitations are identified, and future perspectives and proposed.
Additional comments: The authors have made significant efforts to improve the quality of their manuscript. I believe they addressed each and every comments from all reviewers.


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: VOLUNTARILY CONTROLLED BUT NOT MERELY OBSERVED VISUAL FEEDBACK AFFECTS POSTURAL SWAY
Review round: 2
Reviewer: 2

Output:
Basic reporting: 1.	The authors have addressed the issues in the introduction.

2.	L 113 and L312. Personally, I think the use of the DFA as an index of intentionality could have made the paper stronger. As I specified in the previous revision, it has been used in several studies to report the level of attention or intentionality the participants have (Stins et al. (2009) Gait Posture; Donker et al. (2007) Exp Brain Res). I hope you take it into account for future studies. The variable you use to talk about the voluntary control of the movement is subjective and it could have been supported by the DFA results.

3.	L 136. I am so sorry but I still do not found the reference you made in the Procedure section regarding the pseudo-randomly assignment of the groups. Please, could you point it out? I do not think is a very relevant information to report but if you refer to it in the method it should be there.
Experimental design: 1.	Regarding the bias of the way the authors assessed the sense of control, the fact that the voluntary-control group scored approximately 4–6 on the sense of control rating scale across four feedback conditions, while the observation group scored approximately 2–4 can be caused precisely by the question you asked and the given instruction. Even if the groups were not biased toward an extreme response, as you say, this variable has its limitations so I would suggest adding it in the Limitation section.

2.	I agree on the use of a between-participants design and the reasons the authors gave to support their decision. However, that does not avoid the issue with the “sense of control” variable that has been used. Since the authors talk about several studies which have measured the effects of between-participants factors by employing a similar index to assess the sense of control I would suggest referring some of them? Note: Asai & Tanno, (2007). The Relationship Between the Sense of Self-Agency and Schizotypal Personality Traits. Journal of Motor Behavior, 39, 3; used within-participant multivariate analysis of variance.
Validity of the findings: No comments
Additional comments: Thank you very much for addressed all the comments I made in the previous review. I hope you found them 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: INDUCIBLE NITRIC OXIDE SYNTHASE (NOS2) KNOCKOUT MICE AS A MODEL OF TRICHOTILLOMANIA
Review round: 1
Reviewer: 1

Output:
Basic reporting: In this paper, the authors reported the phenotype of a inducible nitric oxide synthase (NOS2) knockout mice. They found that this mutant mouse exhibited barbering behavior (BB) which might be used as a model of trichotillomania (TTM). Furthermore, they showed that two drugs, clomipramine and memantine, could partially rescue the BB phenotype of NOS2 knockout mice. They also found  a reduction of MAP2 in the NOS2 knockdown PC12 cells during activity-dependent differentiation. This study is interesting in regard to a novel model of TTM. However, lacking of proper controls and evidences make me having a hard time to evaluate this work.
1. Chen SK et al. Cell, 2010 and Greer JM et al. Neuron, 2001 showed that Hoxb8 mutant mice exhibited compulsive grooming and hair removal which were similar to TTM. They also found this behavior disorder was associated with mutant microglia. The authors should cite, discuss and learn from those two papers.
2. The authors mentioned in line 84-86 (Introduction) that some mice display excessive grooming without BB. Could the authors explain the differences between BB and excessive grooming? Are there any literatures that describe the differences?
3. Since the authors used the NOS2 knockout mice from Jackson Lab, they should introduce the phenotypes that were identified by previous studies. Actually, NOS2 mutant mice have a series of phenotypes, including abnormal inflammatory responses and have been widely used in several fields. How could the authors rule out the possibility that the BB phenotype was just a side effect of other defects? It is possible the BB phenotype in this study was not induced by the change in the nervous system.
4. Without any evidences to indicate the efficiency of NOS2 knockdown in PC12 cells, it is hard to evaluate the MAP2 data. Even if it's true, could the authors explain the relationship between the MAP2 data with the BB phenotype? I think it is inappropriate to use the indirect and preliminary evidence in this study to draw such a conclusion in line 288-290.  The reduction of MAP2 and BB could be two parallel phenotypes without any interaction. Meanwhile, the authors should culture the primary neurons of NOS2 knockout mice and analyze the phenotype in vitro.
5. Figure 2: In 2A, the value of KO is about 2000. Meanwhile, in 2C, the vehicle (also KO) is over 3000. Could the author explain this huge difference. Moreover, the authors should include wt mice (with or without drug treatment) in the 2C and 2D.
Experimental design: no comments
Validity of the findings: no comments
Additional comments: no comments


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

Input:
Title: INDUCIBLE NITRIC OXIDE SYNTHASE (NOS2) KNOCKOUT MICE AS A MODEL OF TRICHOTILLOMANIA
Review round: 1
Reviewer: 2

Output:
Basic reporting: The authors describe the NO knockout mouse as a potential mouse model of trichotillomania. In general, the manuscript is well written, the rational for the study is described well, the methods are described adequately, the results are presented well, and the interpretation of results is well supported and presented in a context that is supported by publications in the field.
Experimental design: The experimental design is appropriate that answers a well defined question, which is relevant and meaningful. The number of animals per group was as low as 5, which is minimal as generally 12 animals per experimental group is a minimum in my research laboratory to have enough statistical power. Nevertheless, most of the results appeared to have robust statistical results.
Validity of the findings: The data is generally robust, although sample sizes are sometimes very small. The female and male data needs to be reanalyzed as described in the comments to the authors. Appropriate control groups were used. The interpretation of results are conclusions are appropriate for the results obtained. I especially like the authors cautious interpretation of their results without overstating their significance.
Additional comments: The authors describe the NO knockout mouse as a potential mouse model of trichotillomania. In general, the manuscript is well written, the rational for the study is described well, the methods are described adequately, the results are presented well, and the interpretation of results is well supported and presented in a context that is supported by publications in the field.

I would like to suggest just a few changes:

The barbering behavior is not well defined. The phenotype of the mice as shown in Fig. 1a could be due to selfbarbering or barbering by conspecifics in the home cage. Although the authors mention that some of the barbering on the back may be due to allobarbering, I would expect to see some evidence that the hair loss is due to selfbarbering. Whisker pulling and fur pulling on the snout, around the eyes and on the forehead can be due to allobarbering alone, as I have witnessed in my own mouse colony. Therefore, the authors cannot be sure that the barbering is due to selfbarbering unless they have observed the animals closely. Allobarbering could be due to expression of dominance by a conspecific. Do the authors have videos of animals pulling out their own whiskers or fur, or have they observed this? If the barbering is predominantly due to allobarbering, a link with compulsive-like behavior and trichotillomania would be more difficult to make as the phenotype could be due to expression of dominance.

For the statistical analyses with females and males, the authors should include an effect of sex and appropriate interaction effects in their ANOVAs, instead of testing females and males in separate ANOVAs or t tests. This will reveal whether the females and males responded similarly, or whether there were sex or interaction effects. Please include the true p value, instead of stating p<0.05 for every statistical analysis. This will provide more confidence in the overall results as some sample sizes are pretty small.

In the rescue of BB results section pups were used, but this was not described in the methods section. Please add a section for pups in the methods section and described at what ages they were tested.

For those results for which only females were used, for clarity I would like the authors to indicate that the results were obtained with females. For example, in the repetitive behaviors results section, the authors could write in the first sentence “NOS2.KO females” instead of just “NOS2.KO”.

Also, where there is a significant interaction effect, please describe the results that explain the interaction effect. This could result in novel insights that would otherwise get lost.

I would like to commend the authors on a thorough discussion that did not overstate the interpretation of their results.


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: KILL TWO BIRDS WITH ONE STONE: MAKING MULTI-TRANSGENIC PRE-DIABETES MOUSE MODELS THROUGH INSULIN RESISTANCE AND PANCREATIC APOPTOSIS PATHOGENESIS
Review round: 1
Reviewer: 1

Output:
Basic reporting: See below
Experimental design: See below
Validity of the findings: See below
Additional comments: In this paper, the authors construct a mouse model able to replicate, simultaneously, the major pathogenetic mechanisms of T2DM: insulin resistance and beta cell defect. The paper is susceptible for publication, but I have some comments that need to be addressed by the authors:

1.	Gene acronims employed in the abstract must be explained
2.	Introduction lacks of the main findings originated by previous, and pioneristic works with the most relevant single-gene engineered diabetic mice (generalized and tissue-specific insulin receptor KO,  HMGA1 KO, etc). These studies should be cited (at line 106), and briefly commented. On the other hand, from line 115, the text anticipates (in too much details!) what will be shown in the Results. This part should be omitted.
3.	Please, fix the following references: “Association” and “Statements”, in the text and in the reference list.
4.	Please, split the first chapter of the Results section: one for figure 1 and one for figure 2
5.	In panels 2A and 2B, the dual transgenic mouse is lacking. In panels 2C and 2D, the single transgenic mouse is lacking. Please, complete the panels and adopt always the same colours.
6.	Lane 250. It is not clear why the authors choose to employ the triple TG mice for next experiments.
7.	Discussion section is too long and must be drastically reduced.
8.	The manuscript needs an extensive revision of English.


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: KILL TWO BIRDS WITH ONE STONE: MAKING MULTI-TRANSGENIC PRE-DIABETES MOUSE MODELS THROUGH INSULIN RESISTANCE AND PANCREATIC APOPTOSIS PATHOGENESIS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript is clearly written. References to previous work using a porcine model of metabolic syndrome/diabetes are provided. Raw data supporting the figures are provided.
Experimental design: The experimental design is within the scope of Peer J. There is a clear need to develop a model of diabetes that fully recapitulates the end organ manifestations of type 2 diabetes. The authors compare hypothesize that transgenic animals for CHOP (single transgene), CHOP and hIAPP (dual transgene; both coupled to the porcine insulin promoter), and CHOP-hIAPP and 11-beta-hydroxysteroid dehydrogenase type 1 (linked to the porcine apoE promoter). Their hypothesis is that the triple transgene, by targeting various aspects of islet function/cell survival and insulin resistance, provide a more robust model of metabolic syndrome/diabetes than do the single transgenic animals. The methods, combined with this group's previously published methods on the porcine model, are sufficient to understand how the studies were conducted.
Validity of the findings: The authors do find that the triple transgenic mice have slightly higher blood glucose levels in the IPGTT test, and that administration of a high fat-high sucrose diet led to higher glucose levels than the double transgenic animals. Body weights and adipose tissue accumulation were also higher in the high fat triple transgenic animals. There appears to be a modest increase in hepatic lipid deposition in the triple transgenic animal fed a high fat diet. However, the normal diet control mice also had significant hepatic steatosis. The transgene apparently increases microvesicular steatosis, whereas the high fat diet increases the size of the lipid vacuoles. In general, the high fat diet appeared to increase islet area, whereas the transgene decreased islet size. There do not appear to be statistically significant differences in caspase 3 activity among the 4 groups studied.
Additional comments: The authors clearly show that the triple transgene, combined with high fat diet, produces heavier animals with increased fat deposition, hepatic lipid deposition, and insulin resistance than the single transgenic animals. However, the conclusion that the triple transgenic animal provides a better model of diabetes is premature. The mice were studied for 190 days, which would be a long time to use this model for future studies on pathogenesis or interventions. There are two issues that should be addressed in the discussion--first, there are other models of type 2 diabetes (such as the leptin-deficient db/db mouse or the ob/ob mouse). How does the triple transgenic animal compare with these models? If the triple transgenic animal is a better model than other type 2 diabetes models, this should be discussed. Second, one of the leading problems in diabetes research is the lack of an animal model that recapitulates the end organ manifestations of diabetes, i.e. cardiovascular disease, renal disease, retinal disease, and neuropathy. It was mentioned that the heart and kidney weights of the triple transgenic animals were higher than that of normal mice--were these normalized to body weight? Is there any evidence of cardiovascular or renal disease in this model? This should also be discussed.


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: KILL TWO BIRDS WITH ONE STONE: MAKING MULTI-TRANSGENIC PRE-DIABETES MOUSE MODELS THROUGH INSULIN RESISTANCE AND PANCREATIC APOPTOSIS PATHOGENESIS
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: The authors have conceptually improved their manuscript, however there are still some issues that deserve to be well addressed.
1. There is still no mention of the IR knock-out mice, which were the first genetically engineered mouse models for diabetes.
2. English still needs improvement in the newly added parts – these sections should be revised.
3. References need to be double-checked, especially if the authors used an automatic system. Line 51, Association?, line 60, HH? – this is not correct. Line 87, the reference is wrong.  Authors should check their cited references according to the context. These are just a couple of examples to take into account.


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: KILL TWO BIRDS WITH ONE STONE: MAKING MULTI-TRANSGENIC PRE-DIABETES MOUSE MODELS THROUGH INSULIN RESISTANCE AND PANCREATIC APOPTOSIS PATHOGENESIS
Review round: 2
Reviewer: 2

Output:
Basic reporting: The revised manuscript has been edited for grammar. Additional references have been added. Data tables are complete.
Experimental design: No comment.
Validity of the findings: No comment
Additional comments: In this revised manuscript, the authors provide several important clarifications. In the revised discussion (lines 575-600) the authors emphasize that the triple transgenic model is employed to study metabolic syndrome and early manifestations of diabetes--insulin resistance, islet cell dysfunction, and hyperinsulinemia. Important comparisons with other commonly used models of diabetes (the ob/ob and db/db mouse) have been added.


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: SYMBIOTIC IMMUNO-SUPPRESSION: IS DISEASE SUSCEPTIBILITY THE PRICE OF BLEACHING RESISTANCE?
Review round: 1
Reviewer: 1

Output:
Basic reporting: meets all standards
Experimental design: Experimental design is solid just a few small suggestions.

Was there error associated with observer variability? Did the same observer assess bleaching and disease across all time periods? If so it should be mentioned in the methodology.

12.5% showed signs of bleaching and 18.4% of disease. This is a small percentage of the total sample size. The authors recognize the benefit of increasing the sample size on lines 180-181 but do not give details of what sample size would be appropriate. A power analysis of the data should give the suitable sample size.
Validity of the findings: Fig. 2 shows a number of fragments that appear intertwined and touching each other. Was a spatial analysis conducted on whether or not disease increased with decreased distance from a diseased fragment? There is no mention as to how they were oriented within the nursery or whether or not direct contact can infect a white band-like white syndrome.
In lines 54-60 there is minimal discussion of transmission. A more thorough discussion of vectors and transmission in the introduction would be helpful that also includes how you are defining “disease”. You refer to the correlation between bleaching and “disease” but is this white band-like white syndrome really a disease or is it a syndrome or other condition? This should be made clear in the beginning and in the methodology. Your terminology is very important.
Additional comments: Overall the paper is well written and in-depth. I believe this research significantly contributes to the larger field of climate change research.
The authors include plausible explanations with detailed support of symbiont immune suppression to back their findings of a negative correlation between bleaching and disease.
Tracking individuals with a known prior history over time helps determine the link between bleaching and disease. The authors make a good case for the limitations of other field studies that omit this.