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: LIVER SLICE CULTURE AS A MODEL FOR LIPID METABOLISM IN FISH
Review round: 1
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: Methods:
•	It is stated (line 68) that the study was treated according to the Norwegian Animal Research Authority in accordance with the animal welfare act of June 2009.

The experiment should be in compliance with the “newer” national (FOR-2015-06-18-761) regulation for use of experimental animals (which is in agreement with EU regulation (Directive 2010/63/EU), it is also recommended that the authors include a reference to their FOTS approval of the experiment.

•	The authors compare gene expression between whole liver, liver slice and hepatocyte culture by using pooled data from each source to give an overall expression phenotype.

Livers are sampled from fish in different life stages freshwater and saltwater and fed different diets, these are all factors that will have major impact on the expression of metabolic gene. The samples to be compared should ideally come from fish fed the same diets, from same life stages in order to be able to make a sound comparison. The authors need to give more information to justify that their comparisons are sound.

•	Lipid analyses:
The authors state that they used 13:0 as an internal standard for fatty acid composition analyses.
 It is not very common to use this short chain fatty acid, when there is specific emphasis on determining the level of the longer chain fatty acids. Why have the authors used 13:0 and not the more relevant longer chain 23:0? Further in their GC analyses, no effect on the relative proportions of EPA and DHA with increasing ALA inclusion in the media was found but instead a tendency to reduced EPA + DHA. This reduction is most likely due to a dilution effect when ALA increase. Although 13:0 is maybe not the best std to calculate the quantitative levels of EPA and DHA, the authors are recommended to give these quantitative values for the fatty acids in addition to the relative (to see if the actual quantity of fatty acids change when ALA increase)..

•	Hepatocyte culture.
•	 It is stated that the cells were grown at 200K density, the authors need to give the density per area. Further the authors are recommended to include the fatty acid composition of the livers used in the study for isolation of hepatocytes in addition to the life stage, since these factors will influence the gene expression in the cells.
.
•	Isolated primary hepatocytes in culture are normally used for metabolic studies within the first 4 days after isolation and cultivation, thereafter the cells will start to lose their “hepatocyte” characteristics/nature/function and become more and more fibroblast like cells. The authors need to explain why they have chosen to compare the expression of metabolic genes between day 5 to day 9, at these time points the cells are not normally suitable for such comparisons. While the gene expression in liver slice culture stabilize after 4 days and the authors consider them suitable for metabolic studies between day 4 and 9, this is normally not the case for cultivated hepatocytes.
Validity of the findings: Viability measurements

•	It is only measured dead and alive cells as test of viability, ideally it should be included a measurement of the viability of live cells, for instance by measuring mitochondrial function MTT, or LDH leakage, since live cells do not necessarily need to be “healthy”. It is stated that the liver slices were highly viable in all experiments with a mean viability of 90%.  When looking at supplementary figure S1., there is a major increase in expression of genes related to autophagy, mitophagy, proteasome and lysosome in cells supplemented with insulin and the two highest doses of ALA. Autophagy can be seen as an response to cellular stress, which can promote cell death or in extreme cases, the breakdown of cellular components promotes cellular survival by maintaining cellular energy levels showing the need to include more thorough viability evaluations of the cells.
The combination of insulin and ALA led to downregulation of many metabolic genes that normally are upregulated by insulin and ALA, the authors need to evaluate if this is caused by a potential toxic effect by the high doses of ALA and insulin.  Stress in cells may lead to downregulation of a huge number of genes.

•	Viability measurements of hepatocytes in culture also needs to be included, also a test showing the viability from day 1 after isolation to day 9 at the end of the experiment, It is further recommended to include a microscopy image of the hepatocytes in culture (in supplement), to visualize that the cells actually have formed bridges (mimicking) liver structure, which healthy salmon liver cells do in culture

De novo lipogenesis
•	Line 259, it is stated that there was a large difference (doubling) in proportion of 18:0 between fresh liver and liver slices after 4 days of incubation. It is further discussed in line 357 that these fatty acids are synthesized de novo. However, it is believed that the capacity to produce fatty acids de novo in salmon is relatively limited and it should be more thoroughly discussed why the authors believe this?

Discussion of liver slice culture versus primary cell culture

•	It is concluded that liver slice culture outperforms 2D hepatocyte culture in terms of gene expression and similarity to whole liver.  However, the authors are recommended to modify their conclusion since the experimental conditions do not justify a comparison of the two model systems. Further there is a huge amount of studies on 2D hepatocyte culture that show their suitability to study metabolism of fatty acids and conversion to all metabolic products in the omega-3 pathway, whereas in the liver slice culture in this study, only 20:3n-3 could be found.
Additional comments: The manuscript “Liver slice culture as a model for lipid metabolism in fish (#34550)” present some new and interesting data on how liver slice culture could be used as a model for studies on lipid metabolism in fish. However, some of the conclusions drawn could not be thoroughly justified.


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: LIVER SLICE CULTURE AS A MODEL FOR LIPID METABOLISM IN FISH
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: Comments to steroid biosynthesis results:
 Fig 3, shows co-expression correlation between mean whole liver expression and gene expression in liver slice from different days. The steroid biosynthesis pathway expression appears to be significantly reduced in liver slice (from day 3-9) compared to intact liver. In primary hepatocytes, many genes in the steroid biosynthesis pathway was lower than both that in both liver slice and whole liver.
Based on these results, the authors conclude that the liver slices were closer to whole liver expression relative to primary hepatocytes.
However, the authors need to consider the potential influence of the use of methyl-β-cyclodextrin (MβCD) in their model. MβCD is an effective agent for the removal of plasma membrane and mitochondrial membrane cholesterol. Several studies have shown that MβCD dose-dependently increase the cholesterol level in the culture medium and the intracellular level of free cholesterol, possibly through removal of cholesterol from the plasma membrane (even when a non-toxic concentration of MβCD is used). In this study it was used 0,09% MβCD in the incubation over 9 days.  Even though less than 0,1% MβCD was used, which  is considered safe dose for cells in short term cultures,  detrimental effects may still occur during longer term incubations (as 9 days in this study). It has also been proposed that the variability of the toxic effects of MβCD observed in different cell system studied is correlated with the concentration of cholesterol in the membrane. For instance, 0.2% MβCD toxicity in fibroblasts cell lines (Pfitzner et al., 2000) exhibit lactate dehydrogenase activity in media culture comparable to control. However, 1% concentrations of MβCD triggered a significant induction of cell death and apoptosis in human keratinocytes cell lines (Schonfelder et al., 2006). Cancer cells are also shown to be more sensitive to cholesterol depleting agents because their membranes are more enriched with cholesterol. Salmon cells are known to be particularly rich in cholesterol, which may suggest a high sensitivity in this species for MβCD.  Further, MβCD is a well‐known lipid microdomain disrupting agent and cholesterol chelator and it is shown to disrupt mitochondrial raft‐like microdomains by cholesterol efflux and impair mitochondrial bioenergetics.
Thus, the authors need to discuss how sensitive the salmon liver cells are towards MβCD in longer term exposure? If cholesterol is released from plasma membranes and mitochondrial membranes, it may explain the downregulation of genes in the sterol biosynthesis.
.
Previous reviewer comment to De novo lipogenesis results
Line 259, it is stated that there was a large difference (doubling) in proportion of 18:0 between fresh liver and liver slices after 4 days of incubation. It is further discussed in line 357 that these fatty acids are synthesized de novo. However, it is believed that the capacity to produce fatty acids de novo in salmon is relatively limited and it should be more thoroughly discussed why the authors believe this?
Authors comments
While it is true that de novo lipogenesis (DNL) is thought to be active but limited in salmon, our data suggests a large increase in DNL one day after slicing. Expression of fasa and fasb more than doubled (log2FC 1.08 and 1.02 respectively) between whole liver (D0) and day 1. Additionally, L15 is high in D+ galactose (5mM) and sodium pyruvate (5mM) providing ample supply of acetate precursor. It is also possible that the 18:0 originates from FBS added to the media, however previous studies have found that FBS also contains high levels of 18:1n9 and we find that this decreases in liver slices.
We have added this to the discussion on lines 353-360.

New comment reviewer:
The major products from de novo lipogenesis are known to be 16:0 and 18:0. Since an increase in these saturated fatty acids are known to be very toxic for cells, the hepatocytes have a huge capacity to desaturate these fatty acids further to 16:1n-7 and 18:1n-9, since MUFA prevent toxic effects. However, when looking at the quantitative levels mg/100 gram of these FAs, the levels of both 16:0, 16:1n-7 and 18:1n-9 are reduced, which do not point in direction of increased de novo lipogenesis, since it is only the level of the saturated fatty acid 18:0 that increases. Further data is therefore needed if in order to conclude that increased de novo lipogenesis is the cause of the increased 18:0 level.
The authors point to that fasa and fasb more than doubled (log2FC 1.08 and 1.02 respectively) between whole liver (D0) and day 1, indicating increased lipid synthesis. However then one would expect increase in total liver slice lipid content (which is the opposite of what is shown in Table S2). However, FAS gene expression may also increase during stress, for instance FAS induction in stressed myocardium represents a compensatory response to protect cardiomyocytes from pathological calcium flux. Also, data suggest that FAS fine-tunes the cell's response to stress and injury by remodeling cellular O-GlcNAcylation.
Table S2 shows that the supplementation of ALA leads to a major reduction in the total fatty acid level in liver slice cells. The level is reduced from 3.20-gram fatty acid per 100-gram biomass (in the 0 ALA group) to 1.83 fatty acids per 100-gram biomass in the 140 ALA group, even though this group has taken up ALA FAs. Why has there been an approximately 50% loss of cellular fatty acids when increasing dose of ALA is given to the cells? Can this loss of fatty acids may also indicate increased lipolysis due to toxic effects or increased dose of MβCD resulting in leaky membranes?
Further, disruption of microdomains by cholesterol extraction with methyl-β-cyclodextrin may inhibit tyrosine phosphorylation and insulin-induced glucose transport activation. It is shown that the cholesterol-lowering agent methyl-β-cyclodextrin promotes glucose uptake and reduces insulin resistance in obese mice. The authors need to discuss if MβCD in the culture media may be one factor influencing the confounding effects of ALA and insulin in their study.
Additional comments: The Authors state that liver slices were highly viable in all Experiments. However, there are some concerns concerning the validity of their findings that the Authors needs to address/discuss


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: SEASONAL AND INTER-ANNUAL COMMUNITY STRUCTURE CHARACTERISTICS OF ZOOPLANKTON DRIVEN BY WATER ENVIRONMENT FACTORS IN A SUB-LAKE OF LAKE POYANG, CHINA
Review round: 1
Reviewer: 1

Output:
Basic reporting: The article has high quality figures and tables, but the language still need some improvement. Besides, I would recommend the authors add the relevant references to the methods which have used in the article.
Experimental design: The research question has well defined on a meaningful topic. However, I have worried about the method for rotifer collection. The 64 um plankton net could be too large to loss a high mount of rotifer species, density as well as biomass for the zooplankton community.
Validity of the findings: There is a sufficient data base. However, the topic mentioned "different hydrological years", while I didn't find sufficient description on this part. I would suggest either change the topic or add related information to support the hydrological differences and influences.
Additional comments: 1, Change "shallow lake" to "sub-lake" in the abstract. and explain "shallow lake" in the introduction when first using it. Maybe you can add "linking" or "surrounding" to identify the shallow lake. Otherwise readers will get confused when first look at it.
2, Line 65: delete "water".
3, line 71: "biological" change to "biotic".
4, line 72: "small algae" is not professional expression.
5, line 77: top-down "control"?
6, line 85: delete "characteristics of".
7, line 86: "repeated water changes" looks strange. Maybe you mean "fluctuation of water level"?
8, line 97: "remain rarely reported" has grammar mistake.
9, line 101-103: "zooplankton" is a collective noun following with plural form.
10, line 103: "water" change to "aquatic".
11, line 104: better divided into two sentences.
12, line 150: As I mentioned above, each method should link to a reference.
13, line 282-287: There are actually your results. In this part, you made too many duplication of your results, but lack of powerful and meaningful discussion to extend your results. I would suggest you think about the dominant species, and the species who can survive in the winter. How about they biological traits? Are there any relative reports of them in other place? Moreover, the diversity patterns are also lack of discussions.
14, line 435-437: This conclusion neither with results to support nor discussion on it.


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: SEASONAL AND INTER-ANNUAL COMMUNITY STRUCTURE CHARACTERISTICS OF ZOOPLANKTON DRIVEN BY WATER ENVIRONMENT FACTORS IN A SUB-LAKE OF LAKE POYANG, CHINA
Review round: 1
Reviewer: 2

Output:
Basic reporting: The article in English  use clear, unambiguous, technically correct. The article professional standards of courtesy and expression.
Experimental design: All variables were ln (x+1) transformed prior to analysis？

Does this have any references?

Is it reasonable?
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: SEASONAL AND INTER-ANNUAL COMMUNITY STRUCTURE CHARACTERISTICS OF ZOOPLANKTON DRIVEN BY WATER ENVIRONMENT FACTORS IN A SUB-LAKE OF LAKE POYANG, CHINA
Review round: 1
Reviewer: 3

Output:
Basic reporting: The authors used the correct scientific definitions however, the linguistic quality of the manuscript is very low.  The manuscript needs a revision by an English native speaker since, in many parts, it is not clear what do authors want to say.
The title is not very relevant to the study due to the inclusion of the phrase “different hydrological years”. Since the aim of the study is the investigation of the seasonal and annual changes in zooplankton community structure and no hydrological analyses are included in the manuscript I strongly recommend that the above phrase is removed from the title.
Literature and background information: In my opinion, literature and background information is satisfactory. The literature is relevant to the study area and the content of the study in general. However, I have a comment about the introduction since it needs to be more focused on seasonal changes of species presence and abundance as well as community structure, rather than on the effects of eutrophication since water quality parameters were not measured in the present study.
Structure for their manuscript: The authors followed the required structure for their manuscript. They have provided good quality figures, Tables and raw data. However, I have a comment about one of the figures provided. Particularly, Figure 1 caption is incomplete “Location of Shahu Lake and the zooplankton sampling points (water depth map based on the water level of October 2012)”. The authors should name each one of the individual maps shown in Fig. 1 (i.e. a, b, c, d) and include information about each one of them to the caption. It would be also important to give numbers to the sampling points.
References: I have noticed that some of the references in the text are not included in the Reference section i.e. Hu, 2015; Lin, 2013; Yang & Huang, 1994. I strongly recommend careful checking of the references provided.
Experimental design: The scientific gap is well documented and research questions are stated clearly. However, the last paragraph of the introduction includes some points which need improvement and clarification, i.e.
-	The authors stated in line 109: “This study has carried a preliminary research into seasonal variations in zooplankton communities in Shahu Lake, a sub-lake of Lake Poyang.” What do the authors mean by the term preliminary? Why the results are preliminary?
-	My major objection concerns research question 2 Line 112: “(2) identify the dominant environmental factors that affect the variation in zooplankton communities.” the term “environmental factors” is very generic, and definitely it includes more factors that are known to affect freshwater biota i.e. depth and more importantly nutrients concentration. And this is my major concern about this study. I recommend that the authors reconsider their research question 2 and if they can answer this question by only testing water temperature, conductivity, DO, pH and turbidity.
Sampling design of zooplankton is described adequately.
In my opinion, the authors should clarify the criteria for selecting the three points. They mentioned in the text that “With the water level declining, the water only remained in the deepest area, so three sampling points were set in the more than 1.4 m area in winter (Fig. 1).” So, what I understood is that all sampling points are located in areas with a water level being at 1.4m depth at least. However, according to Fig 1 this is not true. 2. Also, Fig. 1 caption needs more elaboration (see paragraph 1).
Data analysis
Subtitles in the Data analysis section is necessary in order to be easier for the reader to follow your statistical analysis. i.e Zooplankton community structure
 I also believe that density and biomass estimation should be moved in this section since is also part of community structure analysis. Their density was calculated by dividing the individual numbers of zooplankton gathered in each sample by the sample volume and expressed by ind./L. The biomass of zooplankton (wet weight) was evaluated according to the method of Zhang and Huang (1991). The weight of each nauplii was estimated to be about 0.003 mg (Xie & Li, 1998).
Validity of the findings: I have a major objection about the conclusion that the authors ended up and it is also stated in the abstract “Water environmental factors, water level fluctuations, wintering migratory bird activities and human disturbances have a direct or indirect impact on zooplankton community structure” since, it is not a conclusion derived from the data analysis and results from the current study, rather being a general assumption and thus, I suggest that the authors consider deleting it from the abstract. They can use it to support their results.

Results:
I am not convinced, or at least it is not clearly explained in the manuscript why “The interannual differences of the communities were not found indicating that the seasonal variation in zooplankton community structure in Shahu Lake was much greater than the interannual variation” (lines 265-267). I encourage the authors to provide more details of how they ended up with this very important result.
Also, a table showing the results from one-way ANOVA for biomass and species richness changes among seasons is missing. I believe that the results from lines 202-203: “Zooplankton species richness showed significant seasonal differences (P=0.041)” and line 229 “of zooplankton was significantly lower in winter than in other seasons (P<0.05)” need to be shown in a Table.
The authors have to ensure that the results are presented in a Table and the number of the Table is also included in the text. i.e. line 225: Rotifers density showed no significant seasonal difference (P = 0.123) (Table +++++); The interannual variation in zooplankton density was significant (P = 0.012).
I suggest using either April, July, October, January or spring, summer, autumn, winter, both text, and figures.

Discussion:  I believe that the discussion is very weak. The repetition of the results in many parts of the discussion is redundant. There are many linguistic mistakes so in many cases it is unclear what the authors want to point out. The authors are extensively using in their discussion the “Water level fluctuation” as one of the most important factors affecting zooplankton community structure (i.e. Line 381-403) in order to explain the seasonal changes of zooplankton communities in their study. However, they have no data on water level changes in their study in order to use it as an explanatory environmental factor for their findings. This is my major concern, I believe that the authors need to enrich their dataset with more environmental data, and especially water depth, maybe seasonal fluctuations e.c.t.  in order to be able to answer their research question 2. I strongly recommend the enrichment of the environmental dataset.

Conclusions
Water environmental factors, water level fluctuations, wintering migratory bird activities, and human disturbances have a direct or indirect impact on zooplankton community structure. This is definitely not a conclusion of the current study since water level fluctuations, wintering migratory bird activities and human disturbances were not tested.
Additional comments: The paper entitled " Seasonal and inter-annual community structure characteristics of zooplankton driven by water environment factors during different hydrological years in a sub-lake of Lake Poyang, China" is interesting and could contribute to a better understanding of the responses of hydrological and water environmental factors to zooplankton community in lakes. I believe, however, that the authors partly answered their second research question since important environmental factors affecting zooplankton community were not included in the study. The authors could also analyzed their dataset by strengthening seasonal and interannual variability examination. Some suggestions would be to estimate species turn-over or estimation of the coefficient of similarity among years/seasons. I strongly recommend a revision by an English native speaker since the linguistic quality of the manuscript is very low and, in many parts, it is not clear what do authors want to say.
Therefore, major revisions are needed so that the manuscript could be considered for publication.


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

Input:
Title: NOMOGRAM FOR PREDICTING CANCER SPECIFIC SURVIVAL IN INFLAMMATORY BREAST CARCINOMA: A SEER POPULATION-BASED STUDY
Review round: 1
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: - There is a lot of time series, why did the authors select data from 2010 to 2015?
- The authors have to compare their performance with the previous works on the same dataset.
- Quality of figures needs to be improved. Now it is hard to see.
- The authors reported C-index values. It is good, however, there is necessary for reporting the other metrics, such as an important one is the ROC Curve.
- In their tables (1 vs 2), what is the "1[Reference]"?
- Why there are missing p-values in the multivariate analysis?
- It is important to discuss the characteristics with high p-value (not significant)
- It is necessary to test the prediction model with an independent dataset.
- There are some grammatical errors and typos. The authors should re-check and revise carefully.


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: NOMOGRAM FOR PREDICTING CANCER SPECIFIC SURVIVAL IN INFLAMMATORY BREAST CARCINOMA: A SEER POPULATION-BASED STUDY
Review round: 1
Reviewer: 2

Output:
Basic reporting: Clear.
Background not sufficient, should have more introduction about similar studies using SEER database.
Experimental design: Well done.
Validity of the findings: The majority of the findings is valid.
Additional comments: The authors used the SEER database and analyzed the prognostic factors of inflammatory breast cancer patients. They used univariate and multivariate analysis to screen for significant prognostic factors and develop a survival nomogram that might help to provide prognostic information of IBC patients. I have several comments.

1, The authors stated in the discussion that “To our knowledge, this is the first study to analyze the survival of a large 163 cohort of patients with IBC based on the SEER database and” This is definitely not true. There are numerous published papers using the SEER database to analyzed the prognosis and prognostic factors of IBC patients.

2, The generation of the nomogram has a potential mistake. All of the variables, e.g. ER, PR, Tumor size, etc, has the same increase of points when different values were selected. (Namely, for ER, positive to unknown is equal to negative to positive). This is not correct as the HR between pos and unknown should not be 1/2 of the HR between negative and unknown. To solve this problem , the authors could set the variables as factor in R, using the as.factor codes.

3, the comparison between MRM and non-MRM is confusing. What do you mean by non-MRM? Do you mean breast conserving surgery? BCS is almost contraindicated in IBC patients. Do you mean radical mastectomy or extended mastectomy? They removed more tissues than MRM, why inferior to MRM?

4, I think the reason that LN is not significant is possibly due to the co-existence of M stage in the multivariate analysis. The authors could check this.

5, there are many others studies using SEER database to investigate the IBC patients. The authors should not avoid them, and should present the novelty of the current studies, when compared with previous studies.


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: NOMOGRAM FOR PREDICTING CANCER SPECIFIC SURVIVAL IN INFLAMMATORY BREAST CARCINOMA: A SEER POPULATION-BASED STUDY
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: My previous comments have been addressed.


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

Input:
Title: LAND USE MANAGEMENT BASED ON MULTI-SCENARIO ALLOCATION AND TRADE-OFFS OF ECOSYSTEM SERVICES IN WAFANGDIAN COUNTY, LIAONING PROVINCE, CHINA
Review round: 1
Reviewer: 1

Output:
Basic reporting: I am not familiar enough with the many methods used in this paper to provide a substantial review. It is my sense that this study used data from only two years (2010 and 2014) to determine changes to ecosystem services that are sensitive to rainfall. NPP was determined to grow in this time span and is described has having a 1.7% increase despite lower rainfall in 2014. The Food Supply (FS) ecosystem service increased over this time period primarily (as far as I understood) through increases in aquacultural activity. Food supply was reported in Yuan per hm. I saw no rationale for reporting food supply in monetary units which are subject to many market forces that have nothing to do with ecosystem services. I am also not familiar with hm as an areal unit (Hectameter ?).

The discussion of trade-offs and synergies between ecosystem services was particularly confusing. It seemed to be explained solely by correlations between changes in ES using only 2010 and 2014 as temporal observations with sample size needs coming from doing this on a  per pixel basis? In addition - changing prices of grain were used to explain changes in ecosystem services. I do not understand that. A simple example (ginned up for simplicity): A yield of 1 ton per hectare brings $1,000 yuan in 2010 while a 0.5 ton per hectare brings in $10,000 yuan in 2014  is an INCREASE in FS? How does that make sense? I do not believe there is sufficient temporal data in this analysis to justify any conclusions whatsoever with respect to change or allocation strategies.
Experimental design: Not enough temporal data?
Validity of the findings: As I said in the beginning - there are many methods used here that I am not familiar with. However, I am concerned about the limited temporal resolution of this experimental design. I am also perplexed by the idea of grain price changes influencing changes to the food supply ecosystem service. I would be more comfortable with calories of food yielded. This would be confusing also if major changes were made to agriculture e.g. switching from grains to livestock or orchards. etc.
Additional comments: This paper needs a broad overview of Wafangdian County. Not necessarily a description of latitude and longitude but a description of the ecosystems that exist there, variability of weather and climate in this area, impacts of water availability and climate on these ecosystems, the economic activity going on in this area, and changes that have taken place to all of these from 2010 to 2014. I suggest placing your data and analysis in that context. The ESs evaluated were  FS (derived from NDVI alone?), NPP (derived from CASA in which you saw a 1.7% increase - what may have caused that? Land use management? What evidence is there for that? less rainfall?), WY (Using InVEST - what data changed from 2010 to 2014 that went into that other than differences in annual precipitation? Why do you believe the results of this model were valid when applied to your data?), and SC (using RUSLE - did anything other than rainfall change in the evaluation of SC for 2010 and 2014?). I am not familiar with the OWA analysis.


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

Input:
Title: LAND USE MANAGEMENT BASED ON MULTI-SCENARIO ALLOCATION AND TRADE-OFFS OF ECOSYSTEM SERVICES IN WAFANGDIAN COUNTY, LIAONING PROVINCE, CHINA
Review round: 1
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Study the effects of land use management on the trade-offs of ecosystem services is meaningful to investigate the key factors and process of ES trade-offs change. This study applied GIS, ecological models and n ordered weighted averaging model to examine spatial and temporal changes of four ES (food supply, net primary productivity, water yield, and soil conservation), and identify the effects of land use management on the ES trade-offs based on multi-scenario allocation. It’s meaningful, and I suggest revise several key issues before the acceptance as the following:

1. L66-68, the gaps on studying the effects of land use management on the trade-offs of ecosystem services need to be justified. This section mainly listed the studies on the impact of land use change and management on ecosystem services and trade-offs, but the main problems in the current studies are not clearly concluded, which need to be addressed clearly, to demonstrate the significance of your study.

2. L89-97, the ecological and environmental problems in the study area (Wafangdian) are not explained clearly, which needs to be added to enhance the representativeness of the study area.

3. I don’t understand why there are food supply for the forest and grassland? Please justify it and give a clear definition in the sub-section of Quantifying ecosystem services.

4. In this study, the CASA, InVEST and RUSLE models were used to estimate NPP, WY and SC services. There was no any modifications and calibrations of the models, and the default parameters were straightly used. So it is not necessary to introduce these models at detail. I suggest to explain each model with only one equation and cited related references is enough. Now, it’s too redundant for the explanation of these models.

5. L217-260 of Scenario analysis based on OWA-GIS is also suggested to simplify, and Fig.2 is not necessary.

6. The sub-titles of “Spatiotemporal distribution of ecosystem services” and “Spatiotemporal differences in ecosystem services with different land use types” in the RESUKTS are suggested to revised as “Overall change of ecosystem services” and “Spatial change of ecosystem services”, respectively, and reorganize the related contents.

7. There are too many figures and tables. Some figures/tables are redundant and can be removed, such as Figure 2 and Table 1, etc. Also, the captions of the figures are usually removed from the figures, please have a check for the requirement of the figures for PeerJ. Some figures can be put into the Appendix.

8. The conclusion needs to be further enhanced to a higher level, for example, by addressing the future direction or significance for ecosystem services study.

9. The English and context need to be improved, especially for the sections of Results and Discussions

10. The format of references need to be double-checked and consistent.


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: LAND USE MANAGEMENT BASED ON MULTI-SCENARIO ALLOCATION AND TRADE-OFFS OF ECOSYSTEM SERVICES IN WAFANGDIAN COUNTY, LIAONING PROVINCE, CHINA
Review round: 1
Reviewer: 3

Output:
Basic reporting: The four ES are not all using abbreviations in Lines 37,38,45.  I recommend to use abbreviations like Line 139.
Experimental design: The scenario analysis based on OWA-GIS should be described with more details.
Validity of the findings: The conclusion should be better written.
Additional comments: Very interesting to see investigated complex interactions among ecosystem services.This study selected four ES that were representative of the study area and applied OMA model to optimize allocation .The result may provide scientific methods for land use management.
A few questions are list below.
1 How to determine risk coefficients?
2 Please provide more details on fuzzy quantification model (Table 2).


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: LAND USE MANAGEMENT BASED ON MULTI-SCENARIO ALLOCATION AND TRADE-OFFS OF ECOSYSTEM SERVICES IN WAFANGDIAN COUNTY, LIAONING PROVINCE, CHINA
Review round: 2
Reviewer: 1

Output:
Basic reporting: The paper has been significantly revised as a result of the first review. These revisions are acceptable and it is particularly useful that a third temporal dataset (2007) has been added to demonstrate the confounding impact of weather / climate variability on this analysis.
Experimental design: Adding the 2007 dataset was quite useful. I did notice that ‘preserving ecoystem’ diversity was an ‘objective’ in the scenario development. This seems to be a ‘tradeoff’ With respect to optimizing ecosystem services. I think a greater discussion of how ‘optimization’ in terms of efficiency is almost always a tradeoff with another often referred to and desired objective of ‘resilience’. This appeared to be focused on optimizing ES but what happens to the resilience of the system as a result of this optimization. I think a full of analysis of this is beyond the scope of this paper but a few sentences describing this ‘tradeoff’ is warranted.
Validity of the findings: This is a relatively sophisticated analysis of a very complex problem. It is very difficult to assess ‘validity’ in this respect. Assessing the validity of Explorations of tradeoffs and interactions amongst ES using models and datasets that have myriad shortcomings and inaccuracies is virtually impossible. I think the best we can do is publish the findings, and see how they hold up over time. Those that seem to correspond with reality in the future deserve greater attention then. Just as many General Circulation Models of global climate get presented, assessed, and reevaluated.
Additional comments: Thank you for you attention and response to the 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: LAND USE MANAGEMENT BASED ON MULTI-SCENARIO ALLOCATION AND TRADE-OFFS OF ECOSYSTEM SERVICES IN WAFANGDIAN COUNTY, LIAONING PROVINCE, CHINA
Review round: 2
Reviewer: 2

Output:
Basic reporting: Clear English is used!
Experimental design: Research question is well defined.
Validity of the findings: Conclusions are well stated.
Additional comments: The authors have answeres all my concerns. It's suitable to be accepted for publication. Thanks for your responses!


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: WHY THE LONG FACE? COMPARATIVE SHAPE ANALYSIS OF MINIATURE, PONY, AND OTHER HORSE SKULLS REVEALS CHANGES IN ONTOGENETIC GROWTH
Review round: 1
Reviewer: 1

Output:
Basic reporting: Overall the manuscript is written well, clear and concise. The literature cited is appropriate and the hypotheses are clearly stated.

My only concern on the reporting is that the introduction does not follow the usual format of broad to narrow and as such is difficult to follow. Suggest some rearrangement, and move the final horse paragraph up to after the first paragraph, since the breed sizes should be introduced before they are discussed in terms of hypotheses of allometry.

I would like to see some clarifications in the manuscript regarding horses, ponies and miniature ponies, because the terms are not always referred to consistently (and I believe the authors use pony to refer to specifically the miniature breeds at times, e.g. Line 326). The authors mention in the introduction that ponies are defined as horses of a particular height, and miniature ponies are a height below this. In the caption of Figure 1, they use a “Welsh” pony as an example of a “regular sized horse”, which is confusing since it is not clear if ponies and horses are distinct in morphology or just size? Furthermore, on lines 273-278, the authors discuss ponies and regular-sized horses in relation to the CREA hypothesis. Finally, caption for fig.4 simply states small and large breeds. Please clarify and make consistent.
Experimental design: The authors amassed a very commendable dataset of skulls from museums for their study. The methods applied to test for allometry and consider paedomorphosis are appropriate.

Pooling the data for all non-miniature breeds of horses and ponies assumes a single allometric slope for these breeds. As such, I suggest below that the authors plot the regression residuals and not simply the regression predicted values, to show whether this is a valid assumption.

Only some R functions mentioned explicitly in the methods section, please be consistent.

Rstudio is simply a graphical user interface (GUI) for R and doesn’t really need mentioning.

The outlier test implemented in geomorph is simply a data inspection tool and is not necessarily identifying statistical outliers, but simply specimens than fall far from the average shape. In this case, it is clear the juvenile forms are more different, but they are not actual statistical outliers. Omit figure S2 and discussion of this from manuscript.
Validity of the findings: I have a concern about the shape data, which I’m alerted to based upon two lines of evidence. First, on line 224 the reported R-squared value is extremely high; higher than I’ve seen for shape allometry studies (which are normally lower due to the high dimensionality of the data). Secondly, the values on the y-axis of figure 4 are orders of magnitude higher than normally seen for predicted values of Procrustes residuals (I’d expect 0.2 rather than 2000). The R code provided with the text does not show the analyses for the coordinate data provided so I cannot check what was done. But seeing these values I’m concerned the Procrustes residuals are not calculated correctly or are not being used in this analysis? These values seem like they are in the original pre-GPA coordinates. Please check and confirm.

The authors should give versions for the R packages used. I am not sure what version of geomorph was used, but I am aware of a known bug in version 3.0.7 on CRAN regarding the procD.allometry HOS test (and was fixed on the version in GitHub). The bug was reading from the wrong column of the ANOVA table when it prints out whether to reject or support the null hypothesis. It is worth double-checking this if the authors were using v3.0.7 from CRAN.

Figure 4 – It would be helpful to the reader to see a ‘regression score’ (sensu Drake & Klingenberg 2010) version of this plot in order to see the regression residuals and thus variation in the data (to be able to confirm that the r-squared value of 0.94 is correct), in addition to the predicted lines.
Additional comments: This is an interesting paper and important for our understanding of how allometry contributes to morphological diversity.

Line 296-297 Perhaps I misunderstand wat the authors are saying here, but what about the extinct short-faced kangaroo subfamily Sthenurinae?

Figure 1 – Inconsistency in naming. Call all ‘XX pony’, or just give name without pony suffix.

Figure 3A – This is a wonderful graph! Can you make it bigger?

Figure 3B – I think that thin-plate spline (TPS) grids would work here to show the overall shape change from juve to adult, rather than the two configurations overlaid.

Following my comments above on horses, ponies and miniature ponies, it would be good to see another graph such as a PCA like fig. 3 showing miniature ponies, ponies and horses as three separate groups/trajectories, since there is not much dialogue about whether ponies are distinct from horses, or is it just miniature ponies that are distinct?


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: WHY THE LONG FACE? COMPARATIVE SHAPE ANALYSIS OF MINIATURE, PONY, AND OTHER HORSE SKULLS REVEALS CHANGES IN ONTOGENETIC GROWTH
Review round: 1
Reviewer: 2

Output:
Basic reporting: A few minor grammatical issues are noted in the appended pdf.
Experimental design: No comment
Validity of the findings: No comment
Additional comments: In general, I thought the paper was well written, well presented, and addressed an issue of some interest.  The findings were not what I would have anticipated, and I'll be glad to see these data and interpretations available.


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: WHY THE LONG FACE? COMPARATIVE SHAPE ANALYSIS OF MINIATURE, PONY, AND OTHER HORSE SKULLS REVEALS CHANGES IN ONTOGENETIC GROWTH
Review round: 2
Reviewer: 1

Output:
Basic reporting: Clear and unambiguous. Only minor concern: “Regular sized horses” – Since regular-sized horses (requires hyphen) are defined with a wither height greater than that of ponies, it would be clearer to just call them horses throughout after definition. Else it suggests there are horses of a size other than that which is defined. Regular-sized breeds compared to miniature breeds would be valid terminology. But then that would confuse whether you are talking about ponies or horses.
Experimental design: Methods described with sufficient detail & information to replicate; all code and data are presented in the supplementary materials.
Validity of the findings: The findings are novel and supported by the data. My only concern is that given the size-range sampling for horses is not as good as for ponies (with only 3 small specimens). As such, it may be that the observed allometric slope difference, which is relatively small, is artefactual due to the sampling. This caveat should be given in the text.
Additional comments: I have reviewed the revised manuscript. I am glad to see that the allometric analyses was a simple error that could be easily rectified. 42% of the variation is very reasonable. I apologise for missing the R markdown file in the original submission; this is done well and I have no comments to make. The changes made are great, particular the new graphs. I have only some small further comments on the manuscript, provided in each section and below:

The title doesn’t do the paper justice since there is no mention of the allometric hypotheses. Suggest changing to include the key words of allometry and miniature.

Lines 446-448 – Arguably all vertebrates show allometric growth in crania (as well as other body parts), not just domesticated animals. Perhaps instead here make the observation about generally common allometric changes among all of the breeds examined, as shown by the 42%.


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: EFFECTS OF LECANICILLIUM LECANII STRAIN JMC-01 ON THE PHYSIOLOGY, BIOCHEMISTRY, AND MORTALITY OF BEMISIA TABACI Q-BIOTYPE NYMPHS
Review round: 1
Reviewer: 1

Output:
Basic reporting: Even if the authors state that they have used an English grammar and style proof-reading service, the actual manuscript is hard to understand. Specially at the Material and Methods section, which in some parts lack of complete sense.
A part from this, I thought that the main objective was achieved, as they want to indicate the performance of a new fungus strain which could be used in biological control of B. tabaci. But the authors lack clarity, and they have promising results, that would benefit from a profesional writer to increase its impact.
Even if they have an appropriate number of references, they are missing one important point, that is the taxonomical position of the fungus species they were using. Some other references are missing at the introduction part, that could be also useful at the discussion.
The figure listing should be checked as in the pdf file the figures are listed from 1 to 11, whereas in the main text, only reach to fig. 6.
Experimental design: The authors have stated a research gap, but they have failed in describing the most important section at the Material & Methods.
I tried to re-write this section, but the exact protocols used with the corresponding references which are missing, some of these are indicated in the attached file.

My main concern is that the special focus that the authors state that have this manuscript is missing, ie. The authors focus that is of special importance the study of protective and detoxifying enzyme activities, but they don´t describe how this has been carried out. The authors state in lines 510-516 :
“Tomato leaves with 3rd instar B. tabaci nymphs were immersed in a conidia suspension of V. lecanii JMC-01(1×108conidia/mL). After this method was used, the same petri dish method as above was then used. The temperature was 20°C in the laboratory.
The protective enzyme activities of superoxide dismutase (SOD), catalase (CAT) and peroxidase (POD), and the detoxifying enzyme activities of carboxylesterase (CarE), glutathione-S transferase (GSTs) and acetylcholinesterase (AchE) from Jian Cheng Bioengineering Institute, Nanjing.”

To me, this last sentence is understandable. Where are the methods? how the activities performed by each of these enzymes were measured?
This is an example, the following sub-section on weight, water and fat content, also have many missing points.
Validity of the findings: The presented data seems robust and statistically sound, but the authors have not squeezed them in full.
I thought that the authors could find more on their results, as finding a relationship between conidia concentration and mortality index, not sure if they could find a linear or if they should use a more complicated method (like the GLM). The results they provide with this part, deserves this further step, I thought that the manuscript will be really improved, adding a point not presented by any other one.
The conclusions are clearly linked to the supporting results, I have just edited them to give a more appropriate style, but it's up to the authors if they would like to return to the original version.
Additional comments: The manuscript describes the biological control power of a new fungus strain against one of the major worldwide agricultural pests, the whitefly Bemisia tabaci.
It is a great job, but deserves more work on it, specially done by an English native speaker, to polish the written style. Apart from that, I found it really interesting, including the description of a new fungus strain that the authors or their institution could patent.


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: EFFECTS OF LECANICILLIUM LECANII STRAIN JMC-01 ON THE PHYSIOLOGY, BIOCHEMISTRY, AND MORTALITY OF BEMISIA TABACI Q-BIOTYPE NYMPHS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Recently, entomopathogenic fungi as myco-biocontrol resource offer an attractive alternative to the use of integrated pest management or chemical pesticides. In line with this, Ting Xie et al. attempted to investigate the eﬀects of Verticillium lecanii strain JMC-01 on the physiology, biochemistry, and mortality of Bemisia tabaci Q biotype nymphs. Overall, they provided some evidence showing host physiological reactions to infection with V. lecanii JMC-01. However, the manuscript should not only be thoroughly improved in writing with a revision by a native speaker, but the structure should also be modified,  and additional data should be provided before considering for publication.

In the introduction, the classification of Verticillium lecanii (Lecanicillium lecanii) should be clearly described. Also, it would be necessary to provide a more detailed description regarding a potential impact on biological control by its validated role of toxicity against insect host, for example, the results from a study of Ravindran et al. (2018) mentioned in this manuscript.

In the Materials and methods section, how did the authors select B. tabaci nymphs infected by V. lecanii JMC-01 for further analyses at 0 h, 12 h, 24 h, 36 h, 48 h, 60 h, and 72 h? Which method was used to determine water content in this study?

Because V. lecanii JMC-01 was isolated from the nymphs of B. tabaci and used as a novel isolate in this study, the results section should be included characteristics of the B. tabaci following infection with V. lecanii MC-01. MH312006 can be trackable, although the author and information were not exactly as shown in this manuscript. A more detailed and informative description representing obtained data should be added, for example, the statement in line 149-156 was largely uncomplemented. In addition, all figure legends should be revised with a brief description of methods. Figures should be precisely represented in the text, therefore figure 3-10 should be reconstructed. When comparison, the result for each time point should be used. For example, the statement in line 170-171 was incorrect (~2.7 fold for day 2 instead of 4.5 fold as mentioned in the manuscript).

The references contain many typos and are still in an inconsistent format. Moreover, all of the journals were lacking. Reference of Ravindran et al. (2018) was represented two times.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: No additional comments


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

Input:
Title: THE MINERALIZATION CHARACTERISTICS OF ORGANIC CARBON AND PARTICLE COMPOSITION ANALYSIS IN RECONSTRUCTED SOIL WITH DIFFERENT PROPORTIONS OF SOFT ROCK AND SAND
Review round: 1
Reviewer: 1

Output:
Basic reporting: The article from Guo et al. is an interesting piece of work which shows organic carbon mineralization rate difference according to the soft rock and sand mixture. From organic matter decomposition experiment, the results show that carbon accumulation effectively increases when the ratio of soft rock and sand volume was about 1/5-1/2. Overall, I think this is a very nice manuscript with several important findings about carbon cycling in the soil.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: *Does the amount of cumulative mineralization of soil organic carbon under different mixture differ only in mineralization rate? Or does the amount differ for long period experiment? Add to the discussion if there are something hypothesis in other papers discussion.

*According to Kemmitt et al. (2008), incubation for 30 days is only explained non-biologically available SOM. Discuss or Explain about this thing in discussion section or method section.

Specific comment
*Line 27: Replace the words “typical treatments” with such as “mixture of soft rock and sand”.
Line 77 and 149: What hm2 means?
Line 119 and 120: Which is correct for Fping or Fuping?
Line 220 C3?
Line 241: How to estimate the k?
L249: Define SOC.

Figures 1, 3, 4, and 6: After the decimal point is not necessary.
Figures 2 and 3: There are too many horizontal scale marks.


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

Input:
Title: THE MINERALIZATION CHARACTERISTICS OF ORGANIC CARBON AND PARTICLE COMPOSITION ANALYSIS IN RECONSTRUCTED SOIL WITH DIFFERENT PROPORTIONS OF SOFT ROCK AND SAND
Review round: 1
Reviewer: 2

Output:
Basic reporting: The English and the referencing needs to be improved (see general comments below)
Experimental design: The manuscript compares mineralization in 4 artificial soil plots, in triplicates. It does not offer an in-depth assessment of the factors responsible for the observed differences in mineralization rates (see general comments below)
Validity of the findings: no comment
Additional comments: The manuscript by Guo and colleagues reports on the mineralization of organic matter in soils composed of mixtures of 'soft rock' and sand. This is motivated by the importance of soil respiration under a changing climate. The soils were established in triplicate plots 2 m * 2m * 0.7 m plots (with the top 30 cm containing the mixture, overlying 40 cm of sandy soil) in 2009, and mineralization rates and soil characteristics were quantified in spring 2018.

The addition of soft rock (containing SiO2, Al2O3, Fe2O3 and CaO) increased soil carbon content, so that treatments with substantial soft rock addition (C3 (softrock/sand = 1:1), C2 (1:2), C1 (1:5)) are more enriched in organic carbon than those without (CK, softrock/sand = 0:1), albeit not in a linear fashion (Fig. 1). Treatments C1, C2 and C3 also exhibited higher rates of organic matter mineralization as measured over a 30 day period. However, the first order rate constants were largest for CK, where no soft rock was added.

Assessment: The manuscript addresses an important topic. However, it does not meet the bar required for publication. The introduction alludes to a theoretical basis, but the results presented are not meaningfully put into such a context. Curves are fitted through the data, but little rationale is given. The data mainly contains observations on organic carbon mineralization on 4 treatments over a time span of a month. It is not clear why the observational period over a month is the relevant time scale, and if/to what extent these results are relevant for longer timescales. The study lacks the data that allows one to link the observations to the underlying processes (e.g. measurements of sorption). It refers to microorganisms (line 284) or different organic matter compounds (line 295), but there is no data to back up such statements. Similarly, the discussion of extracellular processes and hydrolysis of organic matter seams reasonable, but there is no supporting evidence provided (line 303).

Clarity: The manuscript requires revision to clarify the language. For example, line 69 ff "... weathering and .. soil are erosion and texture...", line 76 "the technology ... has realized the resource utilization....", or line 87 "the scholars have carried on resource utilization and obtained the certain achievement" all need to be reworded.

Referencing: some broad statements lack references (e.g., end of line 62, or when referring to previous work (line 96/97,). Also, a significant fraction of the sources cited are journals in Chinese with English abstracts. This may be acceptable for very select sources that reflect local knowledge. However, it is also the case when citing methods, which prevents a significant portion of the readership from assessing the methodology (lye absorption method).

- The abstract contains references to treatments CK, C1, C2 and C3 that are not explained
- Throughout the manuscript, results are given with an accuracy that surely go beyond the significant digits (e.g. line 123 ff)
- Line 56 should be 'slightly changed'


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

Input:
Title: THE MINERALIZATION CHARACTERISTICS OF ORGANIC CARBON AND PARTICLE COMPOSITION ANALYSIS IN RECONSTRUCTED SOIL WITH DIFFERENT PROPORTIONS OF SOFT ROCK AND SAND
Review round: 2
Reviewer: 1

Output:
Basic reporting: see comments below. The writing has been improved in the revision
Experimental design: see comments below. I have some concerns on the lack of data that lead to a system understanding, and the meaningfulness of potential mineralization rates measured
Validity of the findings: see comments below
Additional comments: The revised manuscript by Guo et al. has been improved by revisiting the writing, and by expanding the references and the discussion

The editing indeed made the manuscript easier to read. However, it still suffers from numerous issues.  Most importantly, the scope is very limited: it reports on the amount of organic matter that can be mineralized in soils made from different mixtures of soft rock and sand. Ancillary measurements (granulometry, SEM) provide some limited context, but what is lacking is a data-supported analysis of the processes underlying the limited set of observations. The discussion is not or only loosely tied to data in this manuscript and hence is largely speculation. There seems to be some additional data that support some of the comments made, but I was unable to access or read them (e.g. paper by Jia et al, Zhang et al, Li et al). Thus, overall, the paper offers some novel data, but it does not provide much insight into the processes that cause the observations.

introduction
- when referring to 'culture', do you mean 'experiment' or 'incubation'?
- What does it mean that "the study of organic carbon mineralization... can provide technical support ... for soil organic reconstruction"?
- "tIn summary, when the ratio of soft rock to sand volume was 1:5-1:2, this can effectively increase the accumulation of soil organic carbon. " In fact, figure 1 shows that there is more OC in C1 than in C2; figure 2 shows that the rate betwee 11-30 days - which might be an indicator of the longer term behavior  is highest, not lowest in C3; C3 also has the highest cumulative mineralization (Fig 3, Fig4)
- "Then, the distribution of soil particles was more uniform, the soil structure was stable, and the mineralization level of unit organic carbon was lower." Where in the paper do you show soil stability? This is not the same as microstructure, so what data are you referring to?

Line 68: loose -> loss
Line 73: optimum proportion in what sense? what is your metric?
Line 83: "Many scholars have made use of the low-efficient resources like soft rock and sand and achieved some interesting results. " Delete or refer to actual studies.
Line 84-88: the role of soils in C storage/loss not only depends on the emission of CO2 but also the amount being fixed.
Line 90: adsorption potential
Line 94: "The texture was also improved to a certain extent" - improved in what sense?
"and the macroscopic mechanics showed a strain hardening phenomenon with non-linear characteristics" - what data is this based on?

methods:
- what is the motivation for having the sample "pre-cultured in the incubator at 25degC for 5 days"? How does that impact the soil and the subsequent results?
- "For uniformity of factors such as illumination and micro-topography, the test plot was arranged from south to north in a “one” shape". It is not quite clear how this was set up. Was there no random distribution of different plots?
- Mineralization rates quantified by an alkali absorption method over a short (30d) time horizon.
I am not quite following the rationale given, which refers to prior work by Dai et al. also "set the incubation time is 30 d), the results are satisfactory, and the test method can be repeated". How does this short timescale connect with the climate change issue referred to in the introduction? Also, how does the measurements of potential C mineralization carried out in this manuscript relates to actual fluxes (or rates) in the field?

data analysis:
cumulative mineralization (M, presumably in mg/kg, see Fig3, though y in table 1 is given in mg/kg/d) and the instantaneous mineralization rate (R, mgCO2/kg/d) are described by a logarithmic function:  M, R = a + b*ln(t). However, Table 2 and eq. 1 suggest a first order dependency of R on the organic matter concentration. How are these different fits reconciled in a conceptual kinetic model of organic matter breakdown?

discussion:
as mentioned above, there is no or little data presented that supports the model (non-biological vs. biological controls). It is also not clear to me how well the soils of this study compare to eg. those investigated by Kemmitt et al.
Line 370 ff also does not really add much new knowledge.
Line 417/8: the accumulation of SOC is larger fro C3 (1:1) than C2 (1:2) - see figure 1

references: fix title for She et al.


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: AURKB: A PROMISING BIOMARKER IN CLEAR CELL RENAL CELL CARCINOMA
Review round: 1
Reviewer: 1

Output:
Basic reporting: Introduction

I suggest writing a more detailed introduction; in particular you need to write more about what is known about AURKB. You mention that AURKB expression is related to tumorigenesis and tumor progression (lines 51 - 53) but you need to provide more details about these studies.

Introduction sounds more like an abstract than introduction. It is very short and it needs a lot of work.

Results

Results need to be better explained providing the reader with more details of what do you think the data means. Lines 96-101 – you need to explain in more details.  Similarly, lines 103-106. These are not fully explained.  How is AURKB correlated with gender, histological grade, pathological stage, T stage etc? This is not explained at all and is poorly written.

Tables
Please name Tables – Table not Tbale
Table 2 – Please put a space after Total (N)

Figures
Figure 2- Please enlarge its size a little.
Figures 3, 4 and 5 are very small to see. Please enlarge their size.
Experimental design: Methods need to be described in more details. Research question is well defined but the authors need to provide the reader with more details.
Validity of the findings: The data need to be better presented and explained. Some figures are too small (See the comments below). Conclusions are stated but very briefly.
Additional comments: I suggest the author to work on this article because Introduction and Results need a lot of work.


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

Input:
Title: AURKB: A PROMISING BIOMARKER IN CLEAR CELL RENAL CELL CARCINOMA
Review round: 1
Reviewer: 2

Output:
Basic reporting: English used throughout the manuscript is acceptable and within the scientific style.
Literature review and background information is  NOT sufficient enough to convince why the study was carried.
The study is NOT hypothesis driven.
The results could have been further elaborated.
Experimental design: The study was completely bioinformatics based, therefore analysis tool was satisfactory to meet the level of study. However, the study was not hypothesis driven. It was not clear why authors chose to study levels of Aurora B kinase in clear cell renal cell carcinoma. To me it seems it is very premature to conclude that Aurora Kinase B may be the promising biomarker for the treatment of ccRCC, esp. because Aurora Kinase B is a kinase and it has several downstream targets that may have direct effect on the proliferation of tumor cells. Therefore, without detail mechanistic studies, it can not be concluded Aurora B as a molecular marker.
Investigative and statistical tools used were  satisfactory.
Since this study is a purely bioinformatics based, the method provided is sufficient enough.
Validity of the findings: Authors examined the mRNA expression levels of Aurora Kinase B in clear cell Renal cell carcinoma. Furthermore, authors studied the correlation between expression levels of Aurora Kinase B and disease progression. Depending on the scope of the journal and reader group, the data presented can be sufficient enough to be considered to be published in a cancer focussed journal with few revisions. However, this study is not suitable for the journals and readers who are focussed on understanding the fundamental mechanism of Aurora B biology.
Authors had performed detailed bioinformatics based analysis to conclude that Aurora Kinase B may be a promising biomarker for the treatment of clear cell Renal Cell Carcinoma, however, this conclusion is too premature. Authors need to back up the data with some laboratory based findings in cell line or perform some orthogonal validation using cell line databases such as CCLE.
Additional comments: 1) Logical basis for studying expression levels of Aurora B kinase and its correlation with the disease prognosis in clear cell Renal Cell Carcinoma is missing. Authors need to do more literature reviews, not only the cancer studies, but also the basis science studies on Aurora B.
2) Overexpression or underexpression of Aurora kinase B is known to have effect on chromosome instability (CIN). What is the ploidy status of ccRCC? It is possible that increased Aurora B expression and positive correlation with poor prognosis could be due to aneuploid nature of the tumors. Please use an appropriate database to examine the CIN in these tumors and whether there is any correlation with Aurora B levels and prognosis.
3) For further detail understanding on effect of Aurora B levels in ccRCC and its prognosis, survival rate etc., it is important to study the drugs efficiency in these cancers? Any drug resistance correlates with Aurora B activity?
4) It is interesting to study the synthetic dosage lethality partners for Aurora B overexpression in ccRCC. This finding may predict the therapeutic target for ccRCC. The data from cancer database may be orthogonally validated with cell line database studies.


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: AURKB: A PROMISING BIOMARKER IN CLEAR CELL RENAL CELL CARCINOMA
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors have improved the paper. The use of english language is acceptable. Introduction is well written and details have been added. The figures, tables, data are shared. The results and discussion are well explained.
Experimental design: Research questions have been well defined. The authors state clearly how their findings fill an identified knowledge gap. The investigation has been well carried. Methods are described with sufficient details.
Validity of the findings: The literature is well written. All underlying data have been provided and explained in details. Conclusions are well stated, linked to the original question and clearly support the results.
Additional comments: This is a very interesting paper. It clearly explains how AURKB can be used as a promising biomarker in clear cell renal cell carcinoma.


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: AURKB: A PROMISING BIOMARKER IN CLEAR CELL RENAL CELL CARCINOMA
Review round: 2
Reviewer: 2

Output:
Basic reporting: In the rebuttal letter, authors explained that they examined the expression levels of Aurora B kinase in ccRCC because other studies had shown that Aurora B kinase levels are higher in gastric cancer, thyroid cancer etc. This is not a sufficient and logical explanation for studying Aurora B levels in ccRCC. Authors have included more information on Aurora B levels in different cancers and non-neoplastic diseases. However, these information is not relevant to what they are reporting in this study.
Experimental design: Experimental method section has been modified significantly.
Validity of the findings: 1) Authors added new results on the effects of drugs on ccRCC cell lines and showed that these cell lines are sensitive to Aurora B kinase targeting drugs, Genetech Cpd10. This result tells that inhibiting Aurora B kinase is lethal for ccRCC cells. Since Aurora B kinase is an important mitotic kinase, its function is important for cell viability and inhibiting Aurora B kinase causes global cell death. To rule this out authors should have examined the effects of Genetech Cpd10 on non-ccRCC cell lines as they did for the effects of Axitinib in non-ccRCC cell lines. Therefore, I am not convinced that Aurora B targeting drugs are sensitive to Aurora B high expressing cells only.
2) If authors want to make point that Aurora B targeting drugs are sensitive to ccRCC cell lines, they should back up this data by examining the OS of ccRCC patients who are on Aurora B targeting drugs and show that they have better OS compared to those on non-Aurora B targeting drugs.
3) I understand that the authors could not find the appropriate database to examine the ploidy status of ccRCC.
4) Synthetic dosage lethality (SDL) is not related to the drugs sensitivity. SDL genes are those that are always upregulated or downregulated/mutated with the Aurora B overexpression.
Additional comments: Overall, authors have revised the manuscript significantly, however I still think that there are several results that need validation.


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: GENOME SKIMMING IS A LOW-COST AND ROBUST STRATEGY TO ASSEMBLE COMPLETE MITOCHONDRIAL GENOMES FROM ETHANOL PRESERVED SPECIMENS IN BIODIVERSITY STUDIES
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: General comment:
The authors describe a method to efficiently sequence and annotate mitogenomes for non model taxa, using a variety of procedures and softwares. The pipeline they propose is an assemblage of known methods that are cleverly selected, and their methodology is clearly presented, however the authors’ claim for innovation is quite exaggerated and should be dropped as very close approaches have been used, including in similar groups, for a a couple of years.

Specific points:
- Title: “large scale data” is uninformative. Maybe “large scale molecular sequences” or something similar?

- The authors choose two examples, Rhinebothriidae and Streblidae (arguments for this “selection” are lacking, one can only suspect that these were the samples available at time of the study) but in any case do not treat them equally in many respects: discussion, literature etc… with the flies kept mostly on the side. Although references are (over?)abundant in general in the text, they become rare for Streblidae (see e.g. line 284, why not a couple of key references here?).

- The overall novelty of the proposed methods is certainly moot, see for example Brabec et al.(2016) IJP 46: 555-562 (for cestodes) among others who published very similar results for parasitic Platyhelminthes in the recent years. (Briscoe Par. Int. 2016, Digenea; Vanhove BMC Gen. 2018, Monogenea …).

- On the other hand the authors choose to mention e.g. Maldonado 2017 which is about genome not mtgenome.. The overall selection of literature should be filtered again with a better coverage and focus.
The claim of “taxon identification” (L78-80) is not correct if the taxon was not identified previously (name and reference sequence).

- Minimum coverage value should be included besides mean coverage value (L160-270 and table 2). This would allow for a better representation of the data quality.

- Also does the total number of sequences on L259  represent the number of  sequences or of *mapped* sequences??

- The statement on line 294 is incorrect. See Egger et al. 2017 BMC Genomics for the presence of ATP8 in some flatworms! It would be correct for Neodermata though.

- The claim of cost effectiveness needs to be substantiated with figures. The authors do not present any information allowing, e.g. to estimate the cost of a complete mtgenome or a cost per specimen and comparative values.

- Bibliography: Capitals for authors names and genera in references are essential

Summary:
The paper is interesting but lacks much of its claimed novelty. It could be shortened and more focused, literature coverage should be completed, balance between the 2 selected test groups should be improved, the points listed above should be taken into account. Provided these remarks are considered, it is acceptable for publication, with low to medium priority.

Typos and details: (obviously redaction of the final part of the manuscript has been bit hurried …)
L95: remove second right bracket
L106: for evolutionary… (not “of”)
L126: them not the
L127: add “or” (or remove “either”)
L143: this should have been done beforehand, in any case accession numbers should be available in the paper
L160: replace “and “by “or”
L250: define abbreviation PE (even if looking obvious)
L255: Fig or Figure, be consistent
L333: cestodes
L349: transposition
L350: remove “the”
L352: support?, confirm?…. instead of follow
L355: remove double word
L356: add “in” before “acetabulate”
L357: one instead of in (?)
L368: choose “the” or “their” and complete in accordance
L373: add “for”before cestode
L375: can
L383: change “that”
L403: add “it requires” after i., for consistency
L405: “and is not” instead of “or are”
L451: revise citation form
L627-32: twice the same reference


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: GENOME SKIMMING IS A LOW-COST AND ROBUST STRATEGY TO ASSEMBLE COMPLETE MITOCHONDRIAL GENOMES FROM ETHANOL PRESERVED SPECIMENS IN BIODIVERSITY STUDIES
Review round: 1
Reviewer: 2

Output:
Basic reporting: No comments
Experimental design: No comments
Validity of the findings: No comments
Additional comments: This is an interesting paper dealing with mitogenome assembly based on second-generation sequencing from low amount of invertebrate DNA. The manuscript is well written, methods are sound and discussion and conclusion well supported by the data. Although those mitogenomes will certainly be very useful for researchers working on related taxa in invertebrate systematics, since the manuscript is presented mostly as a methodological contribution my main criticism is related to how novel the findings really are. The main contributions seem to be related to (1) use of NGS to obtain mitogenomes at low cost based on (2) low amount of DNA of museum specimens in genomics of (3) non-model organisms. Certainly those are exciting points brought by NGS, but they have been extensively explored in many recent papers. In addition, much of that literature has not been mentioned in the paper, what makes the manuscript perhaps look more novel that it really is.

A few examples:

https://www.taylorfrancis.com/books/e/9781498729161/chapters/10.1201%2F9781315120454-9
https://books.google.com.br/books?hl=pt-BR&lr=&id=cMItDwAAQBAJ&oi=fnd&pg=PT316&ots=vUVKbbRifL&sig=2DIPlqS0vLj2TXbuqs2B78lXhmY&redir_esc=y#v=onepage&q&f=false
https://www.pnas.org/content/early/2013/09/04/1314445110.short
https://journals.plos.org/plosone/article?id=10.1371/journal.pone.0138446
https://onlinelibrary.wiley.com/doi/full/10.1111/1755-0998.12466

So my main question: what is really novel in this manuscript besides the assembled mitogenomes?  I understand that PeerJ focus on the on scientific validity and suitability to join the scholarly literature, but focusing on what is really novel will certainly make the paper more attractive to its intended audience.

A few minor points:

- Although I do agree that the biodiversity crisis is an important issue, it seems a bit disconnected to the rest of text. The intro could begin stronger dealing with topics that are closer to the paper main goals.
- Mitogenomes are very useful, but stating that "This set of attributes allows the mitogenome to be used for reliable taxon identification, which is the premise for any study involving biological organisms, specially in biodiversity." ignores all the issues that promoted the shift from mtDNA to nDNA in the last 15-20 years.
- In some points the text sounds a bit like coming from a thesis or dissertation, as in "Raw reads from each pair were pre-processed using a series of UNIX commands."
By the way, it would be fantastic to the readers to have those commands/scripts available as supplementary material, which does not seem to be the case in the current version.


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: ANALYSIS OF SMALL RNA CHANGES IN DIFFERENT BRASSICA NAPUS SYNTHETIC ALLOPOLYPLOIDS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript needs more careful editing. It is very poorly prepared. Literature references, significant background of the work are provided. Article structure, figures, tables and additional data are fine. However, reference list is very poorly prepared. Uniformity in format, complete details such as page numbers are missing. The manuscript is self contained with relevant results to hypotheses tested.
Experimental design: The research is original and fits with the aims and scope of the journal. Research question is defined well and meaningful. Role of small RNAs in polyploidization is less studied and hence the work fills a wll identified knowledge gap. Variations among the F2 lines analyzed are interesting. However, needs better discussion. The techical part of the work such as experments and ethical standards are high. Methods described are sufficient for replication. The field trails for observing the flowering time should be elaborated in materials and methods and discussed in detail in discussion section.
Validity of the findings: Some of the conclusions made are blunt statements. Authors have to discuss in detail about the molecular mechanism of flowering, role of small RNAs and the target transcription factors and other genes regulated by transcription factors.
Additional comments: The manuscript entitled 'Analysis of small RNA changes in different Brassica napus synthetic allopolyploids' is a good work overall but suffers from some serous issues and some minor issues detailed below. The manuscript needs careful editing and also elaborated discussion.

Major points:
1. The procedure followed to separate and confirm siRNA from other sRNA in the sequence reads. Is it the usual procedure? Any reference?
2. There are many blunt statements in results and discussion. It has to be elaborated with literature support.
Eg. Line 148. What is meant by method of comparision?
3. Lines 157-158. Polyploidization and hybridization caused changes in number of miRNA. Why it should change? Relate to gene regulation during the physiological process with reference.
4. Line 180. How could protein phosphorylation contribute to heterosis? Elaborate with cited references on what is happening to proteins during heterosis and to which proteins.
5. Line 190. What did Fu etal 2016a said? How you state it is consistent with that? Elaborate.
6. Lines 201-204. Number of up-regulated siRNA expression in F2 compared to number of down-regulated siRNA expression indicate what? Why should there be a difference in differential expression of siRNAs amoung F2 plants? This could have been discussed better.
7. Lines 211-221. Observation of flowering time in F2 plants in field trial is not enough to support the argument about role of transcription factors and their targeting miRNAs. A simple RT-PCR to confirm the suppression of AP2-like and AP2 transcription factors would have given a strong support.
8. Line 241. Inconsistent and consistent are not appropriate words. It can be used only when same samples are repeated and when we get different results compared to previous reports. It is obvious that when the subspecies used are different, the results are going to be different from previous reports. There is no surprise. There is no point in arguing consistent or inconsistent.
9. Lines 242-248. This should have been discussed in a much better way. Gene expression and regulation during initial stages of allopolyploid formation - needs referenes to support detailed arguments.
10. Line 252. miRNAs do not regulate sequence of target site. They complement and thus regulate the expression of target molecules (mRNA).
11. Lines 253-255. Unclear. miRNA gene undergoes mutation thereby the sequence changes and loses its complementarity to target mRNA. This can have an impact on the phenotype indirectly or may involve in evolution of new phenotype. Due to mutation in miRNA, its target site (mRNA) may not change or get lost.
12. Lines 265-268. Why there should be difference between different materials of same generation and different materials of different generation? Give a scientific argument or at least a speculation.
13. Lines 271-282.  A given miRNA may have many target mRNAs. Since one of the target is a transcription factor involved in regulating flowering time (as per literature / database), the flowering observed cant be just correlated with teh miRNA-mRNA combination. It needs validation. Include discussion on what are the genes regulated by this transcription factor and how many of them are involved in control of flowering time.
14. References are poorly prepared. Journal names are not given in full. Abbreviated journal names are not used in many references. Volume number or page numbers missing in most of the references. There are many typographical errors in reference list.

Other minor points:
1. Line 65-66. Avoid use of 'means of molecular biology'. Small RNA is a molecule and the approach is a molecular biological tool. Change the words appropriately.
2. Line 74. 'Stable synthesis B. napus'?
3. Line 77. Change 'are not been' to 'have not been'
4. Line 83. Remove the word 'polyploid'
5. Lines 88-89. Embryo rescue and in vitro hybridization. How this was performed. Elaborate the methodology so that it can be replicated by other researchers.
6. Line 93. Change to 'and flower size'
7. Line 99. Quit and Agilent 2100 should be within brackets? Include city and country name as well.
8. Line 110. Check spelling of the word 'sequences'.
9. Line 114. Change to 'miRNA'.
10.  Line 114. Instead of 'we got', use the words 'were obtained' at the end of the sentence.
11. Line 144. What is meant by different materials? plants or tissues?
12. Line 145. 'on average, average'
13. Line 155. Change to 'identified'
14. Line 156. Change to 'known'
15. Lines 162-165. What is bra-miRNA and bol-miRNA?
16. Line 173. 'cell cellular component'??
17. Lines 163-171. 'Non-additively activated'. Explain.
18. Line 188. Change to 'indicate'
19. Line 192. Change to 'followed by AACC6'
20. Line 192. 'number of parents' or 'number in parents'?
21. Lines 238, 239. Change to Fu et al. (2016a).
22. Line 255. A. thaliana... the statement has to be rephrased.
23. Line 257. Add year to Li et al.
24. Line 259. 'high propotion of miRNAs were non-additively expression' - poor English. Where found to be non-additively expressed?
25. Lines 260-261. Which genes? Examples?
26. Line 263. Add year to Fu et al.
27. Line 264. What is meant by non-expressively expressed??
28. Line 269. 'performance of field traits'??
29. Lines 273, 277, 278. 'non-additive expression' 'non-additively expressed'. Check.
30. Line 274. There are hundreds of field traits. What is again meant by consistent?
31. Line 297. 'Predecessors generally use..."??
32. Lines 283-300. Discuss in a better way.
33. Line 302. Check the spelling of author (auther). Contribution should have lower case c.
34. Line 304. 'contributed to the' is repeated appearing two times.
35. Line 318. Data Accessiblity Statement. Use lower case A and S for accessibility and statement.
36. Line 322. Journal name should be 'Proc Natl Acad Sci USA'
37. Line 325. Page numbers or DOI is missing for this reference.
38. Line 327. 'Trands' should be 'Trends'. Page numbers missing. Period after the article title is missing.
39. Line 329. Period after the article title is missing. 'U S A' should be 'USA'. Page numbers missing.
40. Line 330. Page numbers missing.
41. Line 344. Nucleic acids research should be 'Nucleic Acids Res'. Volume and page numbers missing.
42. Line 346. Give abbreviated journal name.
43. Line 355. Check the format in instructions to authors or recent issue of Peer J. Page numbers missing.
44. Line 359. Journal name is given in full. USA is missing. Volume and page numbers missing.
45. Line 362. Page numbers missing.
46. Line 364. Page numbers missing.
47. Line 368. Page numbers missing.
48. Line 371. Page numbers missing.
49. Lines 371 and 374. In all other references, title of the papers are given in lower case. In these two references it is given in title case!
50. Line 379. Give full details of page numbers. If it is a open access journal without volume or page numbers, give DOI.
51. Line 381. 'The plant cell'???
52. Lines 383-384. Title of paper is incomplete. 'genes in trans.....'??. Page numbers missing.
53. Line 395. Full name of journal is given. USA is missing. End page number is missing.
54. Line 397. Page numbers missing.
55. Line 407. Check Peer J format. Delete symbols like %, @ etc.
56. Line 413. Change to 'MicroRNA'
57. Line 416. Change 'U S A' to 'USA'
58. Line 421. Page numbers missing.
59. Fig. 2 Title: Small RNA sequencing quality analysis... carrys no meaning. Introduce hyphen "-" between 'sequencing' and 'quality'.
60. Fig. 3. Remove "Change of". Remove period at the end of figure title.
61. Fig. 3. "When alignmenting'..??? Change to 'when aligning with' and change it in all the three places in the figure legend.
62. Fig. 5. Remove 'difference'. Make the words ' analysis of' as first two words of the figure title. Do appropriate modifications in the legend.


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: ANALYSIS OF SMALL RNA CHANGES IN DIFFERENT BRASSICA NAPUS SYNTHETIC ALLOPOLYPLOIDS
Review round: 1
Reviewer: 2

Output:
Basic reporting: In general MS is clear and written in standard language. The background information on introduction, clearly indicated the importance of the study, well strengthen by updated relevant references. However, if authors can improve the significance of the study by focusing their results to emphasize the validity of their results would be more attractive to the readers. Specifically line number 76-83.
Experimental design: The study is original and novel. Methods describe with sufficient details. Standard protocols were used. Thorough experiments performed in a scientifically standard level. Research problem well defined, applicable & expressive. It address the importance of this research to fill the identified knowledge gap.
Validity of the findings: No indication of field experimental layout and replications. But, have solid and statistically stable data with novel findings. However, the meaning of the explained results particularly in lines of 139-145 ambiguous and need improvements.
Additional comments: I appreciate the authors for their solid data set, assembled over F1 to F2 generations of detailed fieldwork. In general, the manuscript is clearly written in proficient, unambiguous language. However, there are certain poorly written places as previously indicated, which should be improved .


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

Input:
Title: ANALYSIS OF SMALL RNA CHANGES IN DIFFERENT BRASSICA NAPUS SYNTHETIC ALLOPOLYPLOIDS
Review round: 1
Reviewer: 3

Output:
Basic reporting: The submitted article is clear and understandable to the reader. The language is good. Literature review is good and the references are appropriate. This manuscript contains suitable Figures, tables, data and relevant results.
Experimental design: The submitted work comes under the scope of the journal. The research question is well defined and the research investigations are performed with good standard. The methodology used in this research and the experimental design are appropriate.
Validity of the findings: This article contains original, novel and interesting results. The data provided in the experiments are robust and statistically sound.
Additional comments: The submitted manuscript contains some original and useful information. The submitted work has studied the sRNA changes and regulatory patterns of allopolyploids with reference to the flowering trait. The experimental design is good and the results are reliable.  The manuscript is clearly written. Hence this work is suitable for Publication with following minor corrections.

Abstract: Abstract is comprehensive and informative.
Introduction : Introduction is clear enough to introduce the reader. The aim and objective of the study are clear. However the authors failed to write why they select the sRNA changes and regulatory patterns of flowering trait and it's importance.

Materials and Methods : The research methodology are clearly written and appropriate.

Results : Results are clear with supporting evidences. The presentations of Figures are with good quality. However the Legends for Fig.3c and 3d are looks same. Please check the legends.
Line No: 218 Write the full form for 'FT"

Discussion : Discussions are sound and enough.

Minor concern :
Spelling mistakes
Line No: 156 the word Known is misspelled.
Line No : 188 the word indicate is misspelled


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: ANALYSIS OF SMALL RNA CHANGES IN DIFFERENT BRASSICA NAPUS SYNTHETIC ALLOPOLYPLOIDS
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 revised the manuscript and it reads acceptable.


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: SEARCHING FOR PHYLOGENETIC PATTERNS OF SYMBIODINIACEAE COMMUNITY STRUCTURE AMONG INDO-PACIFIC MERULINIDAE CORALS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The paper is generally well written, although there are some additional relevant papers that should be incorporated in the Discussion. I have noted these in the annotated pdf review. The figures present sequencing count data, however this is biased by the different numbers of sequences obtained for each sample, and should be presented (and analysed) as proportional abundance. Additionally symbiont data are presented at the genus level only and the type level data are missing. Furthermore, summary and/or raw sequencing data have not been shared. Consequently, I cannot evaluate the validity of the study findings.
Experimental design: The research is original and the study question is well defined. The methods are mostly sufficient but additional details are required for the reader to fully understand the analysis of sequencing data. Please see comments in the annotated pdf review.
Validity of the findings: Based on limitations with the current data analysis and presentation I cannot evaluate the validity of the findings.
Additional comments: Potentially you have a very interesting data set. However this is not obvious to the reader as key elements are not presented in the paper. For this study to be publishable, the sequencing data need to be reanalysed and the symbiont type data need to be presented. I also strongly encourage you to see how your results look using the symportal analytical framework (http://symportal.org/).