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 INCONSISTENT REPORTING, REGULATION CHANGES AND MARKET DEMAND ON ABUNDANCE INDICES OF SHARKS CAUGHT BY PELAGIC LONGLINERS OFF SOUTHERN AFRICA
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: Regarding the use of random effects, a likelihood ratio test is not an appropriate way to choose between fixed and random effects – using random effects will always use fewer parameters and have lower BIC. There are various rules of thumb to decide which to use. E.g. see Gelman 2005. Also see https://stats.stackexchange.com/questions/4700/what-is-the-difference-between-fixed-effect-random-effect-and-mixed-effect-mode.
Monthly effects are not samples from a larger population, and they’re not random samples from a normal distribution, so would be better as fixed effects. The same applies to the region effects. Modelling vessel as a random effect is fine, but shouldn’t make much difference either way. Since you have most of the vessels I would probably use fixed effects, because then it is easier to explore the estimates which may be informative. If they are not normally distributed then normally distributed random effects is not the right approach.

There is a lot of data, so very little difference is expected between the fixed effect and random effect estimates, and the choice would hardly change the year effect outcomes at all.

The use of the large regions as the only area effects will affect the indices. The areas are very large compared to the usual practice in CPUE standardization. For example, the IOTC recommends using 5-degree squares when modelling large ocean areas. Data exploration indicates strong spatial patterns within regions, which are not adequately modelled.

In the delta model, the trend will be affected by the chosen mean probability level. How did you choose the baseline levels of the categorical variables? These often need to be adjusted so that the mean of the predicted values is close to the mean of the observed values.

It would be useful to model your data independently by ocean or region, since you discuss the trends of the Atlantic and Indian Ocean stocks by ocean.

Also, if you model by regioins, and find the same pattern in separate regions in which population trends are probably different, it reinforces the pattern it is due to reporting rather than population change.
Validity of the findings: I checked the results by running some analyses myself, for blue shark in the local fishery. I found a number of problems.
-	There were large differences in the month effects between the regions. Best to model the regions separately.
-	More importantly, there were also differences in the annual trends. This may undermine the conclusions of the paper.
-	The regions were not separated appropriately in the dataset. Plotting the ‘regions’ by lat and long shows many sets in the wrong region.
-	As above, there are strong spatial patterns within regions.

I recommend resubmission after rerunning the analysis to resolve these problems. I attach my data exploration code for interest.

The paragraph starting at line 378 compares ICCAT abundance trends with those observed here. The ICCAT data include South African data, which should be explicitly excluded from the comparisons.

Line 394, the issue is not if they are retained, but if they have been consistently retained.

Line 401, vessels can change their fishing strategy, so vessel is not a catch-all for targeting strategy. Has this been considered? The original dataset apparently contained information on set times and bait type, as well as number of hooks, which could be used to distinguish targeting strategy.

Line 435 states that local vessels landed far more sharks during the warmer season. But this is based on raw numbers, because there were no estimates of the covariates due to the use of fixed effects.

Line 451, sharp increases in blue shark catches were far less apparent when the data were analysed separately by region, with a model that accounted better for spatial variability. The same may be true for SMA.

# Exploration code
library(mgcv)
library(maps)
library(maps)

dat <- read.csv("peerj-21432-Raw_Data_Individual_Set_Data_GLMM.csv")

dat$lat1 <- floor(dat$LAT)
dat$lon1 <- floor(dat$LONG)
dat$vess <- factor(dat$VESSEL)
dat$yr <- factor(dat$YEAR)
dat$flt <- factor(dat$FLEET)
dat$ssn <- factor(dat$SEASON)
dat$ar <- factor(dat$REGION)

str(dat)

dat$N_BSH = dat$BSH * dat$EFFORT / 1000
dat$N_SMA = dat$SMA * dat$EFFORT / 1000
dat$HOOKS = dat$EFFORT

loc <- dat[dat$FLEET == "LOCAL",]

mod <- gam(log(N_BSH + 1) ~ yr + s(MONTH) + te(LONG, LAT, k = c(20, 20)) + HOOKS + vess, data = loc, family = gaussian)
windows()
par(mfrow = c(2,2))
gam.check(mod) #  this simplified model fits well enough for basic inference, though a delta model would be better
AIC(mod)
plot.gam(mod, pages = 1, all.terms = TRUE, scheme = 2)
table(dat$ar)
summary(mod)

windows(10,8)
plot.gam(mod, select = 2, ylim = c(-40, -25), scheme = 2, too.far = .01)
map(add=T, fill = T)
points(loc$LONG, loc$LAT, cex=0.2)

mod <- gam(log(N_BSH + 1) ~ yr + s(MONTH) + te(LONG, LAT, k = c(20, 20)) + HOOKS + vess, data = loc, family = gaussian)
windows()
par(mfrow = c(2,2))
gam.check(mod) # shows that this simplified model fits well enough
AIC(mod)
plot.gam(mod, pages = 1, all.terms = TRUE, scheme = 2)
table(dat$ar)
summary(mod)

windows(10,8)
plot.gam(mod, select = 2, ylim = c(-40, -25), scheme = 2, too.far = .01)
map(add=T, fill = T)
points(loc$LONG, loc$LAT, cex=0.2)

mod <- gam(log(N_BSH + 1) ~ yr + ssn + te(LONG, LAT, k = c(10, 10)) + HOOKS + vess, data = loc, family = gaussian)
summary(mod)

mod_w <- gam(log(N_BSH + 1) ~ yr + s(MONTH) + te(LONG, LAT, k = c(10, 10)) + HOOKS + vess, data = loc[loc$ar %in% c("W"),], family = gaussian)
mod_sw <- gam(log(N_BSH + 1) ~ yr + s(MONTH) + te(LONG, LAT, k = c(10, 10)) + HOOKS + vess, data = loc[loc$ar %in% c("SW"),], family = gaussian)
mod_s <- gam(log(N_BSH + 1) ~ yr + s(MONTH) + te(LONG, LAT, k = c(10, 10)) + HOOKS + vess, data = loc[loc$ar %in% c("S"),], family = gaussian)
mod_e <- gam(log(N_BSH + 1) ~ yr + s(MONTH) + te(LONG, LAT, k = c(10, 10)) + HOOKS + vess, data = loc[loc$ar %in% c("E"),], family = gaussian)

summary(mod_w)
summary(mod_s)
summary(mod_sw)
summary(mod_e)

windows(12,10); plot.gam(mod_w, pages = 1, all.terms = TRUE, scheme = 2, main = "W", too.far = 0.01)
windows(12,10); plot.gam(mod_sw, pages = 1, all.terms = TRUE, scheme = 2, main = "SW", too.far = 0.01)
windows(12,10); plot.gam(mod_s, pages = 1, all.terms = TRUE, scheme = 2, main = "S", too.far = 0.01)
windows(12,10); plot.gam(mod_e, pages = 1, all.terms = TRUE, scheme = 2, main = "E", too.far = 0.01)
Additional comments: No additional comments


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

Input:
Title: VARIATIONS IN THE REPRODUCTIVE STRATEGIES OF THREE POPULATIONS OF PHRYNOCEPHALUS HELIOSCOPUS IN CHINA
Review round: 1
Reviewer: 1

Output:
Basic reporting: Below are a number of specific places I see that the authors could focus on to help improve the presentation of their work. (A few of these may be more of a language issue.)
-Climate data is not developed in the methods in any detail, nor in the results. It is discussed in generalities with causal implications given in the discussion. This needs to be changed. Temperature is a very important factor in ectotherm life history and so should get some detailed attention.
- More natural history of the species would provide greater context for the results.
line 10: What is “fitness of a reproductive event?”
line 24: there is no real evidence provided for selective pressures. These data provide a description of geographic variation in reproductive traits and morphology but selection pressures implies a difference in fitness which is beyond the current study.
Line 25: correlated yes, “constrained by” I am not convinced.
Line 35-36: who has given them more attention? Need reference here
Line 36-38: Does this have to occur?
Line 41-42: always?
Line 77-87: format issues
Line 84: I do not understand point e. This needs to be clarified.
Line 173: always? This is a snake study reference. Here and throughout need to cite relevant lizard studies and indicate when a general pattern is being presented or something specific to this study system. There are many sweeping statements made in the discussion that may not be true or are specific to a given study system (eg line188-191). In a number of places studies of other organisms are cited as support for the current results but the connection is not clear.
Line 205-207: If size was adjusted for, then it is unclear what the role of body size is here.
Line 239: “some species” refers to?
Figure and Table legends need much more detail. For example, it is not clear what is being shown on Fig 3and 4, what are the lines? In the climate table no clear idea about time frame is given.
-Remove “s” from end of variation throughout.
Experimental design: While there may be some issues with the descriptive statistical analyses they may be fairly sound if assumptions of the models are met and more information is provided/clarified (see specific comments below). As they state early on, there is not much reproductive data for this species. This manuscript begins to take care of that, which is a good and necessary first step for understanding their life histories.
Line 91 - : These populations were sampled during different years. What is the year-to-year variation these reproductive traits within any one site? Did the weather vary over those years/sites?
Line 101- Were the cages checked 12 times per day?
Line 103- how were the measurements taken? Equipment?
Line 106:  What is POM?
Line 112: consider cutting the 1st sentence
Line 113-115: This is not clear. Were assumptions met for ANOVA, ANCOVA? These types of traits can show high collinearity which can be a problem for ANCOVA. Were Tukey’s done for ANCOVA and ANOVA?
Line 118: OLS regression – define
Line 119-121: What data were used, for what purpose, and how was it analyzed?
Line 121 how were means adjusted?
No weather/climate data provided in text of results.
Results general: don’t need to show p value cut off with each result.
Validity of the findings: Where the most work appears to be required is in the level of interpretation of the results. The discussion of the results goes well beyond what can be said with the data in hand.  Factors causing “life history trait” variation are many and often display complex interactions. The author’s should consider looking at Grant and Dunham (1990) for some ideas about complex interactions in causal agents to life history trait variation across populations of lizard species. Many lizard species also show year to year and time of season variation in these types of reproductive traits (eg clutch size). Therefore, to try to associate the patterns in the reproductive traits to any given causal agent or trade-off with only the descriptions of 1 set of samples from each site taken in different years may be premature.
Discussion:
Line 180-186:  All this needs to be developed in a rigorous manner in the methods and results.
These populations appear to be in vastly different habitats and there may be many, many different factors causing any of the patterns presented here. The authors need to step back and be very specific about what they can and cannot say with the data in hand.  For example, they discuss higher food availability in one of the locations as a cause of large SVL. There needs to be data to support this, both the level of food availability and causal relationship, as SVL can be impacted by other factors like temperature and activity time.
Line 195: How does hydration state impact egg size/mass? Eggs absorb water in moist soil and can expand after being laid. Could this confound the implications of egg size variation as measured and described?
Line 228- Correlation is not causality. Need to be cautious in interpretation of patterns.
Conclusions: There are many other reasons for variation in these traits. For example: Season length, daily temperature, food availability, daily activity times, social environment, predator environment… Again, caution needs to be used when interpreting the patterns being reported.
Additional comments: This is a potentially interesting description of geographic variation in reproductive traits and some female morphological traits in a wide spread species of lizard.
The authors make a good effort to collect some key reproductive traits across three geographically widely separated populations, each of which appears to be in very different habitats. This could become the basis for an interesting comparative study that builds on these initial findings.


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

Input:
Title: VARIATIONS IN THE REPRODUCTIVE STRATEGIES OF THREE POPULATIONS OF PHRYNOCEPHALUS HELIOSCOPUS IN CHINA
Review round: 1
Reviewer: 2

Output:
Basic reporting: The MS is well-written, and the datasets are large enough to address the questions of interest. The literature review is adequate.

Many of the empirical patterns are well-known from other taxa (e.g., small-bodied females produce elongate eggs simply because there isn't room in a slender oviduct for a rounded egg). However, there is value is having such data for a "new" lineage of lizards, especially because so much of the existing literature is based on taxa from the USA and Europe.
Experimental design: My main suggestion is that at the moment, the comparisons among the three populations are based on whether tests on data for each population (separately) meet or do not meet the standard threshold for "significance" (P < 0.05). It is easy for one dataset to fall below that threshold and another above it even if there is no "real" (statistically significant) difference between them.  So to conclude for example that one species shows a maternal-size constraint on egg size whereas another does not, ideally we need to see a significant difference between those taxa in that relationship not just in size-corrected mean values for egg size etc. There are simple ways to evaluate such differences (including absolute values of residual scores from linear regressions, as measures of dispersion).
Validity of the findings: I think the data are useful. The tradeoff between fecundity and egg size is clear. I am less convinced about the exact nature of tradeoff disparities among populations. For example, I find it difficult to imagine maternal body size constraining egg size in a lizard, given the flexibility of the egg and the cloaca, and the ability of selection to fashion elongate eggs. However, I don't see that ambiguity as a crucial issue.
Additional comments: This well-written manuscript analyses a substantial dataset on poorly-known lizards to explore issues of reproductive allometry. Substantial geographic differences in both maternal and egg traits suggest differences in selective forces, but inevitably such hypotheses are difficult to test in any rigorous ways. The paper does a good job of describing the patterns in the data, and suggesting possible interpretations.


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: VARIATIONS IN THE REPRODUCTIVE STRATEGIES OF THREE POPULATIONS OF PHRYNOCEPHALUS HELIOSCOPUS IN CHINA
Review round: 3
Reviewer: 1

Output:
Basic reporting: OK, although some of the new text needs correction for English expression.
Experimental design: OK
Validity of the findings: OK. The primary value is the patterns, rather than the interpretation.
Additional comments: The paper is considerably 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: CHRONOLOGICAL AGE, BIOLOGICAL AGE, AND INDIVIDUAL VARIATION IN THE STRESS RESPONSE IN THE EUROPEAN STARLING: A FOLLOW-UP STUDY
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript, “Chronological age, biological age, and individual variation in the stress response in European starlings: A follow-up study” is a rigorous examination of the relationships among telomere shortening and the glucocorticoid stress response in chronologically aging birds. By using variation in developmental conditions as the basis for expected variation in ‘biological aging’ (the rate of telomere shorting) this study is well positioned to address the correlation, if any, between telomere shortening and declines in corticosterone (CORT) response to an acute stressor. The manuscript is very well written and thoughtfully organized and the replication of work is meaningful. One minor comment is that work by Rensel and Schoech (2011) could be cited regarding consistency in CORT response (e.g., line 78, 305).
Experimental design: I have two requests for additional analysis that I think could strengthen the independent contribution of this work and the interpretation of findings.

First, I appreciated the approach of placing a smaller study in the context of similar work by including a meta analysis of all the data available. However, a direct analysis of the effects of the developmental treatments in the present study on telomere shortening was not reported outside of the metadata. I’m very curious to know the results of such an analysis and suspect it would strengthen the paper. Running and including this analysis might also clarify the effects of the treatments on ‘biological aging’ and thus bring some new insights to the last paragraph of the discussion, which struggles to explain unexpected treatment effects on the glucocorticoid response (also inferred to decline with ‘biological age’).

Second, this smaller study follows upon a prior examination of the relationship between chronological age, telomere shortening, and glucocorticoid response by directly measuring age-based reductions in corticosterone elevation in response to an acute stressor. This is an important gap to fill and the present study is designed to do just that, yet the statistical approach does not include a model with a repeated measure design (rather, two separate models are run, one at each point in chronological age). If I understand the statistics correctly, the value of this work is somewhat diminished by the omission of this test, which would have answered whether change in telomere length is related to change in corticosterone response. I see that the authors chose their current statistical approach to mirror the methods in the prior study, but isn’t the experimental design of the present work specifically aiming to contribute repeated measures?
Validity of the findings: The approach of replicating a study, even with a smaller sample size, is extremely strong and I appreciated the strategy of integrating this work with prior data. In several places the authors suggest that it was small sample size that limited their ability to replicate prior findings (e.g., line 289, 308). I appreciate the desire to avoid speculation, but it seems these results could also reflect something about the strength of the relationships among developmental conditions, ‘biological aging’, and changes in CORT response. Could the authors comments on the biological importance of these relationships and provide some ecological context such as the average life span of a European starling?
Additional comments: I have a few minor questions and comments in addition to the general comments, listed by line, below:

Line 65	In other studies and earlier in the introduction I understood ‘biological aging’ to be synonymous with telomere shortening yet this sentence seems to be relating telomere shortening and declining CORT response (which is also being proposed as a proxy of biological aging, if I understand correctly). I am simply confused as to how telomere shortening is inferred to reflect ‘biological ageing’ without lifespan data being referenced. Forgive me if I am over thinking this but perhaps it is simpler to cite existing evidence that DTL reflects lifespan?

Line 201	I would add that baseline CORT was ‘lower in chronologically older birds’.

Line 285	Here or somewhere in the paper could you include the sample sizes in Andrews
et al., 2017?

Line 322	Is there a citation that provides evidence that begging increases the rate of
telomere loss (which is what I infer from the statement that it ‘accelerate biological aging’)?


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: CHRONOLOGICAL AGE, BIOLOGICAL AGE, AND INDIVIDUAL VARIATION IN THE STRESS RESPONSE IN THE EUROPEAN STARLING: A FOLLOW-UP STUDY
Review round: 1
Reviewer: 2

Output:
Basic reporting: -	Abstract is not very clear and feels choppy. After reading the method and results, the abstract makes sense. I suggest rephrasing sentences in the abstract to be clearer and flows better, particularly after “unlike the original study…..”
-	Writing is not clear at some places. I pointed out where those spots are below.
Experimental design: -	In the introduction or discussion, it would be helpful to lay out the rationale for using Effort in the experiment. What was the purpose of this manipulation and what was the hypothesis and prediction?
-	The analysis of the change in corticosterone between 15 and 30 min was informative and adds to our understanding of adrenocortical responses in starlings.
Validity of the findings: -	I support replication of previous studies which we see so rarely in our field. The authors went further than simply replicating the experiment by conducting meta-analysis and statistical simulation which strengthen the comparisons and overall conclusion which can be made.
-	Effects of family (genetics) at 2 ages are interesting but I am not sure if repeatability across 2 ages can be confidentially determined because of differences in antibodies and inter-assay variation of corticosterone assays.  My suggestion is to remove the repeatability results and discussion related to them. I believe removing these will not impact the importance of this paper.
-	The meaning of correlation between delta TL and CORT values are not discussed in this paper. I assume this is because it has been discussed in the Andrews et al (2017) paper. However, it would be helpful to a reader who has not read the Andrews paper to have this either in the introduction or in discussion section.
Additional comments: I completed reviewing a manuscript #29791 by Gott et al. The authors aimed to replicate the study published by Andrews et al (2017) with an exception of measuring stress response at 2 ages. Unlike the previous study, this paper did not find a significant correlation between developmental telomere attrition and corticosterone parameters. When this study was analyzed with previous 2 studies in a meta-analysis, there was a significant correlation between developmental telomere attrition and the difference in corticosterone levels between time 15 and 30 minutes. Aside from major comments listed above, I have minor comments (see below). I hope my comments will be helpful in improving readability and conclusion drawn from the data.

Minor comments:
Abstract:
Line 24: In the method section, authors states that stress response was measured from 30 individual at age 2. In the abstract, it states 27 starlings. Please clarify the difference in sample size.
Lines 26-28: It is little confusing to know if this is an experimental paper or meta-analysis paper or both.
Lines 25-32: The abstract seems to highlight the shortcomings of the experiment more than what the results of the experiment shows. I suggest rewording the paragraph to describe results, what they mean, and caveats.
Introduction:
Line 43: I suggest removing “would suggest”.
Lines 70-72: I am a bit confused about this sentence. Why having quartets of siblings allow investigation of effects on baseline and peak CORT but not on the change between 15 and 30min? Please clarify.
Line 93: What do authors mean by “familial resemblance”?

Materials and Methods:
Lines 105-106: I assume n = 8 for 4 treatment groups with total of 32 birds. Please specify this.
Line 108: I suggest adding “as the following” or something similar after “under controlled conditions” so it is clear to the reader that the food and begging effort manipulation were only during day 5 and 15 post-hatch. Alternatively, the authors can state this duration close to the beginning of this paragraph.
Lines 121-123: This sentence is not clear to me. It may be me but would it be possible to simply say delta TL of each individual was compared to the mean delta TL to obtain the corrected delta TL? I am not sure what “expected regression to the mean in imperfectly correlated repeated measures” means.
Lines 128-130: Does this sentence mean that birds were separated from a group housing to an individual housing 3 to 27 days prior to blood sampling? Please clarify.
Lines 142-143: This sentence is missing something. “Blood sampling was (collected?) by puncturing an alar or……”?
Lines 157-158: I assume this was out of authors’ control but why were 2 different antibodies used in 2 years of assays?
Lines 162-163: Why are concentration for 2 control samples were expressed in %?
Lines 218-221: With different batches of assays and antibodies used, would it be possible to infer repeatability of adrenocortical responses across 2 ages?

Discussion:
Lines 275: I suggest switching “to” and “clearly” so it reads “our failure to clearly replicate”.
Line 289: What is the sample size? I noted this under method section above.
Lines 294-296: I am not sure what these 2 sentences mean. Please rephrase.
Lines 322-324: One can argue that aging HPA axis would make keep the CORT levels high rather than return to baseline quicker. Please elaborate or cite here.


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: PHOSPHATE SORPTION AND DESORPTION BY TWO CONTRASTING VOLCANIC SOILS OF EQUATORIAL AFRICA
Review round: 1
Reviewer: 1

Output:
Basic reporting: The merit of this study is vague as comparable adsorption extents and mechanisms have been determined for decades.
Experimental design: Lack of sufficient details for methods.
Validity of the findings: The current data are not sufficient to describe the comprehensive adsorption and desorption behaviors.
Additional comments: Manuscript Number: 27906
Title: Phosphate sorption and desorption by two volcanic soils of equatorial Africa

This study aimed to determine the adsorption and desorption of phosphate on two Andosol soils in equatorial Africa using the sorption isotherms. Phosphate adsorption on agricultural soils and soil minerals have been widely studies for decades. The sorption capacities and mechanisms for phosphate on Andosols reported in this study are comparable to that of previously studies. Although impact and novelty are not assessed in PeerJ, this journal asked research question to fill an identified knowledge gap. Given that the mechanisms to control the phosphate adsorption on volcanic soils have been well developed, authors failed to convince the merit of this study. The only difference between this and previous studies is that the sorption isotherms in this study could not be fitted using the Langmuir or Freundlich equations appropriately, which may be caused by the various sorption mechanisms. Thereby, I would suggest authors to discuss the possible mechanisms that could account for the inappropriate fitting using the Langmuir or Freundlich equations. In addition, I suggest to add the adsorption kinetics for phosphate adsorption on Andosol to provide a more comprehensive sorption mechanisms. For all these reasons, I recommend a major revision for this manuscript.

Specific comments:
Line 106-108: “The concentration of Fed is very high in the São Tomé's vitric Andosol, which presents moderate concentrations of non-crystalline Fe and Al, but a large amount of crystalline iron oxyhydroxides.” Please show the exact numbers for all results to make this description more concise.

Line 110-112: the aluminium extractable by dithionite-citrate is higher than that extractable by acid oxalate, which indicates the presence of aluminium in the crystalline lattices of “iron” oxyhydroxides. Is the “iron” in the sentence a typo?

Sorption and desorption isotherms:
What is the tested pH? How long did the equilibration take? Did the pH remained constant over the course of equilibration? How to control the pH? Please provide more details for the methods.

Line 138-154: “The Langmuir model assumes the adsorption of a monolayer, that all the adsorption sites have the same adsorption energy and that there is no interaction among the adsorbed molecules (or ions).” Add references to the description of models for adsorption isotherms.

Line 156: “P sorption was very high in both the silandic and the vitric Andosols.”
Please provide the numbers for the P sorption capacity. Are the P sorption capacities of silandic and vitric Andisols generally higher than other soil or mineral samples?

Line 156-162 and Figure 1: This paragraph focused on the proportion of P adsorbed by soil samples decreased with the increasing initial addition. However, it is a very well-known and common sense for the adsorption behavior. Such description seems redundant. What is the reason to address this point specifically?

Line 163: Langmuir or Freundlich equations are two most general models to fit the data of adsorption isotherms. Why couldn’t these two models fit the P adsorption data in this study? What mechanisms were involved in the P adsorption on Andosols, resulting in the in appropriate fitting using the Langmuir or Freundlich equations? This information is the key contribution for this study.

Line 177-185: The information in this paragraph is repetition of the content in the information.

Line 186-187: The highest values of P sorption derived in this study are comparable to that for other volcanic soils. Given that the extents and mechanisms of P adsorption in this study are similar to that widely reported previously, what is the contribution of this study?

Line 207-209: Authors proposed that the fits for P adsorption isotherms indicated that the sorbing surface is heterogeneous and that there is no sorption maximum, i.e. there is no apparent limit to P sorption. Is the deduction between no fitted sorption maximum and no apparent limit to P sorption reasonable?

Line 209-212: The proposed sorption mechanisms are vague. What do the “high energy sites” and “lower energy sites” mean by? Please add specific sorption mechanisms in the manuscript.


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: PHOSPHATE SORPTION AND DESORPTION BY TWO CONTRASTING VOLCANIC SOILS OF EQUATORIAL AFRICA
Review round: 1
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Abstract
Line 14 -- replacing “and” with “but” could be better.
Line 16-17 -- what is attributable to active species of aluminum and iron? “The major limiting factor” or “phosphate fixation”?
Introduction
Line 77 -- “Cameroon Hot Line” is a proper noun, which means “h” and “l” in the manuscript should be in upper case.
Line 79-80 -- What do you want to achieve by studying the adsorption and desorption of phosphate by surface horizons of agricultural soils in equatorial Africa? Also, in line 84-86, the reason why you did this research may not be adequate. I suggest you rewrite the reason why you did this research and the purpose of doing this research to make future readers better understand the necessity of the study and the motive for this paper. By the way, I think you may cite papers on volcanic soils on Africa relevant to your topic if you can so that future readers may better know the scarcity of research concerned on volcanic soils in Africa.
Results
Line 171 -- It should be “was” instead of “is”.
Discussion
Line 200 -- “slow-release phosphorus fertilizers” may be better.
Line 202 -- There should be a comma before “the best fit”.
Line 203 -- It should be “well describe”
Line 216 -- The word “presents” should be before the word “not only”.
Line 222-223, “o” and “d” should be in subscript.
Reference
The title of papers and books cited should be basically in lower case.
Figure
In figure 1, using “Percentage of” is better.
You can also show the equation of model in Fig. 3 and 4 to make it easier to understand.
Table
In table 1, “o” and “d” should be in subscript.


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: PHOSPHATE SORPTION AND DESORPTION BY TWO CONTRASTING VOLCANIC SOILS OF EQUATORIAL AFRICA
Review round: 1
Reviewer: 3

Output:
Basic reporting: The work presented is a very basic study of the sorption-desorption process of phosphate in volcanic soils. On the other hand authors worked only with Andisols, therefore the title is not appropriate. In the literature there are many antecedents referred to other orders of volcanic soils. Despite the above, the authors do not adequately justify the need to carry out a study of the type presented. The most essential question would be if the soils studied are significantly different in their properties from the numerous other soils (Andisols) in which phosphate adsorption has been studied.
Experimental design: In the experimental design authors considered only two soils for the study, so conclusions obtained are very limited. The characterization of soils and the sorption and desorption experiments were  performed properly.   However, isotherms must be carried out at constant and controlled temperature. Methods used were described with sufficient detail and can be replicated.There are other studies that could be made for obtaining more antecedents, for example the study of pH and temperature effects are very important to characterize both processes and discuss results more properly.
Validity of the findings: Comments are in the general comments for the author.
Additional comments: In the manuscript “Phosphate sorption and desorption by two volcanic soils of equatorial Africa” the study is performend by using the surface horizons of two agricultural soils of Africa. The analysis of data is based on the different composition of both soils related to the more important presence of amorphous Fe-and Al active forms in a silandic Andosol and the high amounts of crystalline iron and aluminum oxides in a vitric Andosol. The work is well presented but it is not novelty because the subject has already been investigated in volcanic derived soils and specifically in allophanic and non-allophanic Andisols.  This aspect could be discussed for example in the introduction section.  There are important references that could be considered for example: Path Analysis of Phosphorus Retention Capacity in Allophanic and Non-allophanic Andisols (Hashimoto, Y; Kang, J.; Matsuyama, N; et ál. Soil Sci. Soc. Am. J., 76 (2) 441-448 (2012), Spatial distribution assessment of extractable Al, (NaF) pH and phosphate retention as tests to differentiate among volcanic soils (Valle, S; Carrasco, G., Pinochet, D. et al. CATENA, 127, 17-25, 2015), Phosphorus sorption maxima and desorbability in selected soils with andic properties from the Azores, Portugal (Auxtero, E.; Madeira, M.; Sousa, E., Geoderma 144 (2008) 535–544.  As presented and with the work carried out, the impact and novelty would be relevant only for a local level interest. As can be observed from these manuscripts and also in several works cited by authors, the antecedents correspond to a great number of soils, for which an extensive interpretation of data has been performed by taking into account a great variety of soil properties. In the present work the results and discussion are restricted to only two soils and no interpretation could be made, apart from the one presented, where the other properties of the soils are included. According to the above considerations conclusions are too general and limited to a very scarce supporting results.


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

Input:
Title: CREATING FUNCTIONAL GROUPS OF MARINE FISH FROM CATEGORICAL TRAITS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The paper is written in clear professional English. There are seldom typos in the text, e.g., line 282: "give -> gives",
line 228: The package name is differently formatted than other packages in the text.
line 254: "all 12 variables"->"all 13 variables",
etc.

The topic of the paper and the used statistical methods are described in a comprehensive way. Introduction sufficiently acquaints readers with the broader field of knowledge.

Throughout the paper, the citations are used sufficiently, but not everyone is used correctly.
Line 236: The package "nomclust" was not introduced in (Boriah et al., 2008), but in (Šulc and Řezanková, 2015) with the name: nomclust: An R Package for Hierarchical Clustering of Objects Characterized by Nominal Variables.

Lines 241, 242: the statement: "deleting observations or variables reduces statistical power and increases estimation bias (Nakagawa and Freckleton, 2008)" is not valid for clustering tasks, and thus, I would recommend deleting it or explain it in a content of clustering.

Line 292: Instead of (Šulc and Řezanková, 2014), where the package was not introduced, use (Šulc and Řezanková, 2015).

The structure of the paper is standard and logical. The figures in the main paper are well done and explained, but some of the supplementary materials contain errors.

S5, Figure 1: On the right-side axis is "PSTau". I suppose, all the three charts are reflecting values of PSFM. In the notation of this figure is mentioned ten distance matrices, but there are only five similarity measures.

S5, Figure 2: In the notation is mentioned WCE as for "entropy", but it should be WCM as for "mutability". Again, it should be five distance matrices.

There are also some mistakes regarding the used equations.

Eq. 4, Line 294: There is an inconsistency in the used symbols. In the main paper, a symbol c is used for variables, but in supplementary material, S4 the symbol k is used. Moreover, the symbol k is used for the number of clusters in the main paper. The formulas in S4 should also be uniformly formatted.

The submitted paper is self-contained, it contains complete analysis.
Experimental design: The paper is within the scope of the PeerJ journal. The research questions are well defined, and the methods used to answer them are appropriate. The provided results are accompanied by scripts and raw data, which makes them easily reproducible.
Validity of the findings: All the decisions of the authors in the paper are based on the data driven approach. The findings correspond with the common knowledge in clustering that no one clustering method and algorithm is the right one. Always, more algorithms should be investigated and that is what the authors have done.

The authors collected their data. The variables in the dataset seem to be well chosen. The more I am surprised by a large number of missing observations that occur in their data. The authors should have devote more effort to fill out the missing values, for instance, using knowledge of experts on these species, rather than imputing missing data.

Conclusions of the paper are appropriately stated, and they are linked to the original questions.
Additional comments: Throughout the paper, the authors consider the categorical data equal to the nominal data, but it is not precise. Categorical data can be divided into two subgroups, nominal and ordinal data. By nominal data, it is not possible to determine the order of categories (e.g., the variable Body form), whereas by ordinal data the order can be determined (e.g., the variable Population doubling, which is wrongly considered as nominal by the authors). All the discretized variables have similar properties as the ordinal variables. There is nothing wrong using nominal similarity measures on ordinal data, but the authors should be aware of losing some information about the data, and it should be stated in the paper. Maybe, it could be worthy to reduce the number of categories of some of the discretized variables, since their order is not taken into account by the nominal clustering. This procedure could lead to better-defined clusters.


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: CREATING FUNCTIONAL GROUPS OF MARINE FISH FROM CATEGORICAL TRAITS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript is well prepared, the text is clear and understandable. However, the term “a novel approach” is only in the title of the paper. The authors do not propose any new method of clustering. The words “a novel approach for” could be omitted. The title e.g. “Creating functional groups based on nominal data characterizing marine fishes” would be more accurate. The equations should be included into sentences, including punctuation marks (comma, dots). The equation number  is a part of a sentence; no reference is needed in this sentence.
Introduction describes present knowledge in the investigated research topic. This part of the paper could contain a formulation of the type: “The aim of the paper is…”, similarly as it is in Abstract or in Conclusion (the aim should be defined in Introduction instead of in Conclusion). The literature is relevant and well referenced. However, some references concerning the R project and R packages are missing, e.g.
R Core Team. 2018. The R project for statistical computing. Vienna: R Foundation, http://www.r-project.org/.
Šulc Z, Řezanková H. 2017. nomclust: Hierarchical Nominal Clustering Package. R package version 1.1.1106.
Some references concerning similarity (or distance) measures are missing, e.g.
the Eskin measure:
Eskin E, Arnold A, Prerau M, Portnoy L, Stolfo SV. 2002. A geometric framework for unsupervised anomaly detection. In D. Barbará and S. Jajodia, editors, Applications of Data Mining in Computer Security, 78-100.
the Lin measure:
Lin D. 1998. An information-theoretic definition of similarity. In ICML '98: Proceedings of the 15th International Conference on Machine Learning, 296-304. San Francisco: Morgan Kaufmann Publishers Inc.
the IOF measure:
Sparck-Jones K. 1972. A statistical interpretation of term specificity and its application in retrieval. Journal of Documentation, 28 (1) : 11–21.
The structure of the manuscript is according to PeerJ standards. The subtitle Limitations in the Discussion section could be omitted. The Reference section should be prepared according to the instruction, e.g.
Blashfield RK. 1976. Mixture model tests of cluster analysis: Accuracy of four agglomerative hierarchical methods. Psychological Bulletin 83(3) : 377–388.
instead of
Blashfield, R. K. (1976). Mixture model tests of cluster analysis: Accuracy of four agglomerative hierarchical methods. Psychological Bulletin, 83(3):377–388.
(without “and” in case of two or more authors, etc.).
The references should be written correctly, e.g. the surname Řezanková is correct.
The citation “Hennig, C. (2013). fpc: Flexible procedures for clustering.” is not complete. (“R package version…” should be added, see above.
The figures and tables are prepared well, they are relevant and well described.
The analyzed data are supplied. The raw data can be opened and they are well described in English.
Experimental design: The manuscript presents an original primary research within scope of the journal.
The research question should be expressed more precisely in Introduction, see above. In Abstract the authors write: “The goal of this research is to determine a suitable procedure for creating and evaluating functional groups that arise from clustering nominal traits.” In Conclusion there is the sentence: “It was our aim to understand if meaningful groupings of teleost fish species can be made from known or easy to gather information.”
The authors applied advanced statistical methods for data preparation, clustering and evaluation results, including selection of distance matrices, clustering methods and number of clusters. The methods are described with sufficient detail (with the exception of the Jacard coefficient and the adjusted Rand index, see below); the data analysis can be replicated with provided information.
Validity of the findings: The statistical methods are applied correctly.
The conclusions are well stated. They are linked to the goal expressed in Abstract, to the text in Introduction and to the title of the manuscript.
Additional comments: The dimensions of “the trait matrix” should be mention in the text (not only in Abstract) – only the number of traits is mentioned in the text, not number of fish species.
The Euclidean distance (with “E”) is a measure, not a method. Similarly, Goodall and Lin distances are correct (not methods); “Goodal and Lin show” is not correct (similarly, “Eskin tended” is not correct) without the previous explanation of using the abbreviated name.
Boriah et al. (2008) do not propose 14 alternative measures but they evaluate them.
After Eq. (4) explanations of symbol “n” and “m” are missing.
In the sentence “The clusterboot function draws a sample of size n from the original data set..”, another symbol then “n” should be used when “n” is the number of objects in the original data set.
In the “Data S4” file the symbols are not chosen appropriately. The symbol “k” is used as the index of variables (in the manuscript the word “variable” is not used). In the manuscript, the symbol “k” means the number of clusters. In the “Data S4” file the text after Eq. (2) is not correct, “c-th variable” is wrong.
The adjusted Rand index (not “Index”) is not explained well (what is the “expected index”?). It is not clear without explanation the Jaccard coefficient. It should be written either with only references to the citations or with the complete explanation.
All abbreviation must be explained before its first use. The abbreviation “SM” (p. 9 and Fig. 6) is not defined. The abbreviation “PAM” (Fig. 6) is not defined and the PAM clustering is not explained.

In References, the names of journals should be written in capital letters, e.g.
Encyclopedia of Biodiversity,
Journal of Machine Learning Research.


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: CREATING FUNCTIONAL GROUPS OF MARINE FISH FROM CATEGORICAL TRAITS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The manuscript was changed according to the comments, including the title. However, there are still some minor mistakes in the paper.
Punctuation marks (comma, dots) are missing after equations.
The reference concerning the R project is wrong. It should be:
R Core Team. 2018. The R project for statistical computing. Vienna: R Foundation, http://www.r-project.org/.
„Team“ is a word „team“, it is not the name. „R Core“ means „R project“, there are not names.
In the citations
„Šulc Z., Řezanková H.“ the letter should be „á“, not „à“.
The figures and tables are prepared well, they are relevant and well described.
The analyzed data are supplied. The raw data can be opened and they are well described in English.
Experimental design: The manuscript presents an original primary research within scope of the journal.
The authors applied advanced statistical methods for data preparation, clustering and evaluation results, including selection of distance matrices, clustering methods and number of clusters. The methods are described with sufficient detail; the data analysis can be replicated with provided information.
Validity of the findings: The statistical methods are applied correctly.
The conclusions are well stated. They are linked to the goal expressed in Abstract, to the text in Introduction and to the title of the manuscript.
Additional comments: After Eq. (4), the word “where” should be written as “where”, not “Where”.


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: EPIDEMIOLOGICAL AND GENETIC CHARACTERISTICS OF SWINE PSEUDORABIES VIRUS IN MAINLAND CHINA BETWEEN 2012 AND 2017
Review round: 1
Reviewer: 1

Output:
Basic reporting: The paper is well written. It is clear and easy to read. It is an extensive epidemiological work based on PRV strains isolated in China. The background is relevant and the references are appropiated. Figures and tables are relevant
Experimental design: Methodology is described with sufficient detail to replicate by others. The analysis of the strains contributes to reevaluate the use of those types of vaccines in China
Validity of the findings: Data obtained were robust and very important in the epidemiology of PRV in China. References are well used througout the paper
Additional comments: I strongly recommend the publication of the work with minor changes. Please see a pdf attached to this review


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: EPIDEMIOLOGICAL AND GENETIC CHARACTERISTICS OF SWINE PSEUDORABIES VIRUS IN MAINLAND CHINA BETWEEN 2012 AND 2017
Review round: 1
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: The PRV was outbreak in late 2011. Epidemiological survey that cover the period before and after 2011 and compare the situation of clinical infection and the genetic diversity of PRV before and after 2011 will be more meaningful.
Validity of the findings: no comment
Additional comments: The manuscript investigated the prevalence of PRV from 2012 to 2017 in 27 provinces of China. A total of 16256 samples collected from large-scale farms suspected of PRV infection, and the positive rates of PRV, 5.57% to 12.19% for 2012-2017, were given. Some positive samples were DNA sequenced and aligned. The study has a large sample size and introduces the situation of clinical infection in detail.
> The PRV was outbreak in late 2011. Epidemiological survey that cover the period before and after 2011 and compare the situation of clinical infection and the genetic diversity of PRV before and after 2011 will be more meaningful.
> How about the situation of small farms in the backyard? Since the backyard farms usually don’t carry out good vaccination, when compared with large-scale farms.
> There is no further discussion and analysis on the results of PRV positive detection in different regions in different years.
> In the Abstract, please clearly give the method for determining wild-type virus. PCR or ELISA?
>“Of the 16256 samples detected, approximately 1345 samples were positive for the detection of PRV-gE,”the word " approximately " need to be removed.
>“To understand the genetic characteristics of PRVs currently circulating in China, a total of 25 PRV strains isolated herein were used for further analysis in this study” Why did the authors choose these 25 isolates? Are they representative?


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: EPIDEMIOLOGICAL AND GENETIC CHARACTERISTICS OF SWINE PSEUDORABIES VIRUS IN MAINLAND CHINA BETWEEN 2012 AND 2017
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comments
Experimental design: no comments
Validity of the findings: no comments
Additional comments: Thank you for sending revised version. It is acceptable in the present form


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

Input:
Title: EPIDEMIOLOGICAL AND GENETIC CHARACTERISTICS OF SWINE PSEUDORABIES VIRUS IN MAINLAND CHINA BETWEEN 2012 AND 2017
Review round: 2
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: There is no further question for the manuscript


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 EFFECTIVENESS OF PAYMENTS FOR ECOSYSTEM SERVICES AT DELIVERING IMPROVEMENTS IN WATER QUALITY: LESSONS FOR EXPERIMENTS AT THE LANDSCAPE SCALE
Review round: 1
Reviewer: 1

Output:
Basic reporting: Looks good to me; the text is well written and the arguments well articulated.
Experimental design: -	Initially, E. Coli bacteria spread is strictly speaking a “brown” (pollution) problem, not related to the ecosystem functioning – i.e. arguably it is not an ‘environmental service’. Real env services (e.g. decompactation of soils, erosion control, etc.) might involve longer time lags. E. coli might this be seen as a bit of a canary in the coalmine for the impacts of this type of PES – or for the lack of them…

-	E coli, treatment vs control: It may be a problem in the RCT evaluation method if the key output variable is skewed between sample and control -- that is randomization has not been effective in creating similar distributions.... The author cite a source that this is not a problem, but there are different opinions about that in the literature. There may be other systematic biases being introduced. It is quite weird to see in Figure 3 that for both 2010 and 2015 not even the whiskers overlap! Upfront, this raises the question how the random selection was in practice being done: some sort of lottery? Second, authors may need to do post-RCT matching of the sample before they compare the results (at least, also reporting this would increase confidence in the results).

-	Treatment and control samples: were there no attrition communities, i.e. where communities resisted PES implementation? Zero attrition would be surprising. Please discuss.

-	Similarly, the different levels of sample selection (and possible selection biases) are important to keep in mind: a) communities, b) landowners, c) land allocated by individual landowner. While for a) there is an RCT design, at the levels of b) and c), there is likely to be strong presence of adverse selection bias (ASB), i.e. ‘choosing the wrong parcels’ vis-à-vis additionality. ASB as a phenomenon is not much discussed here. For instance,	who  refused/ abandoned contracts within the selected communities (attrition)?
Validity of the findings: A lot of the interesting findings in the article are about PES effectiveness. I am integrating knowledge from reading Botazzi (2018) -- in order to better understand the scheme and the analysis of its results:

- upfront, it is remarkable that in a naive 'before-after' comparison, E Coli level go so much up, also in control communities.

- on that note, L.146-8 say: “Consent to randomization was granted by community leaders on the understanding that should the program be found to be effective, it would subsequently be implemented in all communities (this general roll-out was subsequently conducted in 2016).”   But the results presented here can sow doubt about to what extent the approach was indeed effective.

-	“A recent analysis demonstrated that the scheme has been 170 successful at incentivising additional conservation (Bottazzi et al., 2018).” Looking further into the evidence presented, the levels of additional conservation were not that high.

- Furthermore, self-reporting of respondents, done with Fundacion Natura paid interviewers, likely underreporting of e.g. non-additionality, if interviewers are perceived as non-fully independent of implementers.

-  Apparent ‘micro-macro effectiveness/ additionality paradox’: the scheme is supposed to have been effective in terms of additional conservation, especially so for cattle retrieval (Botazzi et al. 2018). But at the same time, there is no effect at the landscape level (E Coli levels in communities).

-	Possible explanations of ‘paradox’:
a) too little land area contracted (size)
b) too little focused on env sensitive areas (targeting)
c) mismatches between ‘action’/ proxy (cattle retrieval) and ‘results’ (E Coli content)
d) time lags between proxy and results
e) intra-community leakage effects from contracted to non-contracted lands

=> the draft so far focuses on a), b), c), d) (great discussion of those!), but maybe leakage also plays a role? Intra-community leakage: Did contracted landowners perhaps move cattle to other riverine areas – their own, or neighbours’ plots? Since only small land areas were typically enrolled, compared to the total of ‘suitable’ (target) land classes, this raises the risk of leakage…

However, the authors should also consider more about the option that ‘there is no paradox’, because the intervention is also not really effective at the micro level (challenging the conclusion in Botazzi et al. 2018), due to:
f) lack of careful spatial targeting
g) self-declared additionality levels of the ‘action’ is too low to make a community-level difference;
h) those self-declared levels are still upward biased by respondents’ drive to please (F. Natura employed) interviewers re. project impacts

Finally, while I have deep respect for Fundacion Natura's efforts and experience in conducting and replicating PES schemes, and think the RCT design is a great idea, the question arises: How to run a 65 community PES schemes as a single NGO without losing your sanity? Implementing a PES scheme requires significant effort: how can one do that seriously in 65 communities at the same time? E.g. what about quality of the design (spatial targeting etc.) and compliance (monitoring and sanctioning) system, outlined recently as key for PES functioning (Wunder et al 2018)? Where so many corners necessarily cut, so that PES effectiveness would have to suffer?
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 EFFECTIVENESS OF PAYMENTS FOR ECOSYSTEM SERVICES AT DELIVERING IMPROVEMENTS IN WATER QUALITY: LESSONS FOR EXPERIMENTS AT THE LANDSCAPE SCALE
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript is polished and reads clearly. Its excellent exposition is one of the greatest strengths of the paper. The motivation for the paper is clear, the approach is unique, and the paper is certainly likely to make an impact in the field.

Perhaps my only concern is that I seem to be missing a table with results? Or perhaps those results are only in the supporting information? The authors might want to consider including at least one table of results in the main text, although now that I think about it, perhaps the authors did this intentionally to illustrate their findings with figures rather than tables?
Experimental design: The authors do a very good job describing what was done, and what the limitations were with the study.

Water quality monitoring for 241 sites is a massive undertaking. I am familiar with the Coliscan Easygel method and agree that it is appropriate for this context. The authors recognize different procedures in baseline and endline data collection, but justify this and explain it well.
Validity of the findings: The authors eliminate sites from their sample if they were unable to verify T & C consistency in the two sampling periods. But could there have been systematic bias that eliminated sample sites? Were there issues of non-compliance?

What about seasonal variation in which samples were taken?

The results are not what one would like to see as a researcher, but the authors do a good job of pursuing the topic a bit further with the second set of models. This only produces a somewhat unsurprising result, but in a sense, it confirms the justification for the program in the first place, so the two analysis work well with one another.
Additional comments: The paper reads very well, and is an innovative piece of research. It certainly will be well received.

It seems odd that there are no Bolivians included as authors?  Especially given the length and intensive fieldwork of this study. It seems odd, and does not reflect well in my opinion.

Lastly, one  minor editing suggestion, consider rewording the sentence on line 466. Otherwise, it is a brilliantly written piece.


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 EFFECTIVENESS OF PAYMENTS FOR ECOSYSTEM SERVICES AT DELIVERING IMPROVEMENTS IN WATER QUALITY: LESSONS FOR EXPERIMENTS AT THE LANDSCAPE SCALE
Review round: 1
Reviewer: 3

Output:
Basic reporting: Although the research question is very interesting, I find the paper poorly motivated. The reasons why we need to evaluate the effectiveness of PES (in general and here in particular) are not given in the introduction, and yet there exists a variety of reasons for a PES not to be effective in changing practices. A discussion about self-selection in voluntary programs and potential spillovers is needed.
The motivation of the program under study is also unclear: why do we have to pay people to stop polluting the river with their livestock? They are the first victims of this pollution; they should not need to be paid for it. More background about the program is needed.
The literature mentioned is relevant but the main findings of these studies are not given; it is thus difficult to evaluate the contribution of the paper.
Overall, the paper does not look like a standard “RCT paper”, like those that can be found here for example: https://www.povertyactionlab.org/evaluations Many information is missing. I would suggest completing the manuscript following the standard approach used in papers in economics.
Experimental design: The study relies on a randomised controlled trial, which is gold standard in the evaluation of treatment effectiveness when well designed and implemented. In this study however, the sample size is very small (n=123) and the control and treatment groups are not comparable ex ante, since E. coli concentration is higher in the control group. I does not mean that the data cannot be used (since the allocation of clusters between groups is carried out randomly, it is known that any differences that do occur must have occurred by chance (Hayes and Moulton, 2009)). However, the authors should at least provide balance t-tests of baseline observables in both groups, so that one can judge the seriousness of the problem. In particular, I would like to know the average number of cows per village, the average number of households that leave their cows in riparian zones, the average number of children with diarrhea, other sources of income (other than cattle ranching), etc.
The methodology used is called Difference-in-Difference but this is never mentioned in the paper.
The econometric part of the analysis that aims to correlate water quality and cattle presence is very unclear (for example, the econometric model used is missing) and does not bring much value to the paper I think, since it has already been established in the literature that the major source of water contamination is the presence of cattle.
Validity of the findings: The main result lacks precision, so that the authors cannot conclude about the effectiveness of the program. The sample size being very small, it would have been interested to calculate the minimum detectable effect (MDE).
The main outcome (water quality) is not measured in the same way during both surveys (monitoring is different in 2015; the location of taps is also different in 2015). The authors should explain to what extent these changes threaten the validity of the results.
Additional comments: The research question is potentially interesting but poorly motivated, so it is difficult to appreciate the contribution of the paper. In general, the paper is not written as a paper in economics, whereas it should, it seems to me, since it deals with changing the practices of breeders in Bolivia.
The statistical method used is good but the quality of the data (especially the main outcome) is poor and the sample is too small to show the impact of the program – if there is any. In the absence of significant results, it is difficult to see the interest of the paper.


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

Input:
Title: THE EFFECTIVENESS OF PAYMENTS FOR ECOSYSTEM SERVICES AT DELIVERING IMPROVEMENTS IN WATER QUALITY: LESSONS FOR EXPERIMENTS AT THE LANDSCAPE SCALE
Review round: 2
Reviewer: 1

Output:
Basic reporting: Fine!
Experimental design: A much better description than in the first submission.
Validity of the findings: I think the authors have done a very good job in using the reviewer comments to significantly improve the paper! This is now a very thoughtful and interesting contribution to the literature. I have no doubt in recommending it for publication in its current stage.

Some very minor issues that the authors may consider:

- It might be worth mentioning that F Natura's pilot scheme in Los Negros was also analyzed from a PES angle (referring e.g. to Asquith et al, 2008, EcolEcon), Already at that point the likely lack of additionality was alleged, due to low payments and lack of targeting (see also Robertson & Wunder, Fresh Tracks in the Forest, 2005 on this aspect).

- l.352, downweighted (join words)
- l.450-63, point on payment levels very well-taken -- just with the caveat that Mexico and Costa Rica (possibly also Uganda) are higher-income countries than Bolivia, where 1 USD has more purchasing power.
Additional comments: None


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

Input:
Title: THE EFFECTIVENESS OF PAYMENTS FOR ECOSYSTEM SERVICES AT DELIVERING IMPROVEMENTS IN WATER QUALITY: LESSONS FOR EXPERIMENTS AT THE LANDSCAPE SCALE
Review round: 2
Reviewer: 2

Output:
Basic reporting: Once again, the authors provide a well written piece.
Experimental design: In my first review, I had fewer objections than others.  The new version should address the concerns raised, as the responses are detailed. Some of the issue is just language, like the choice to use "difference in difference" - ecologists refer to this as BACI, etc...

I am not enthusiastic about the addition of a Matching approach (Ho et al). I understand why this is added, and it makes sense for those with sample sites, it us back to an "observational world", while the whole point of the RCT is to avoid going there.
Validity of the findings: The section on the lessons is very valuable, especially the observations pertaining to the randomization unit and using well developed interventions in RCTs. Overall, this section is very nice.
Additional comments: I recommend publication. This paper must have been a monumental undertaking. It was clear that one of the other reviewers had no idea how difficult and enormous this water monitoring project must have been. My only regret is that credit could not have been shared with Bolivian co-authors, but of course the authors are best positioned to make such decisions.

It is a fine piece of research.


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 EFFECTIVENESS OF PAYMENTS FOR ECOSYSTEM SERVICES AT DELIVERING IMPROVEMENTS IN WATER QUALITY: LESSONS FOR EXPERIMENTS AT THE LANDSCAPE SCALE
Review round: 2
Reviewer: 3

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: In this new version of the paper, the authors acknowledge the main failures of their RCT: attrition, spillover, data quality, unit of randomization, etc. This makes the study more honest about the scope of the results.

In my previous report I asked the authors to provide the minimum detectable effect, which is the difference between the 2 groups that could have been estimated given the sample size (the smaller the effect we seek to recover, the larger the sample must be to have a chance to detect the effect); I did not find it the revised manuscript.
Additional comments: The authors have made the effort to be explicit about the limits of their design, which is a good thing in itself. On the other hand, it is now clear that the absence of conclusive results can be explained by the many weaknesses of the design of their RCT. I wonder then what is the real contribution of the article to the literature on the effectiveness of the PES. The authors have rewritten the paper by guiding the discussion on the lessons to be drawn from their failure, but this type of discussion has already been done, and in more depth in several papers, like the one by Heard et al. (2017) for example. I thus remain unenthusiastic about the publication of this paper.
Cited reference:
Kenya Heard, Elisabeth O’Toole, Rohit Naimpally, Lindsey Bressler (2017) "Real-World Challenges to Randomization and Their Solutions", J-PAL North America, April 2017


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: SURGICAL ANTIBIOTIC PROPHYLAXIS USE AND INFECTION PREVALENCE IN NON-COSMETIC BREAST SURGERY PROCEDURES AT A TERTIARY HOSPITAL IN WESTERN AUSTRALIA—A RETROSPECTIVE STUDY
Review round: 1
Reviewer: 1

Output:
Basic reporting: 1.	The use of punctuation marks particularly comma is inadequate. There is need to improve this so as to improve comprehension.
2. 	Kindly provide a detail legend for Table 3.
Experimental design: 1. The title should be reworded. As it is currently captioned, it is not line with the aim and did not reflect the full scope of the study.
2.	Evaluating the the impact of prophylactic antibiotics  on SSI incidence and length of hospital stay is one of key objective of this study. Unfortunately, there is no table or data in the result section of the manuscript to establish this important relationship. Kindly provide this data and reword your conclusion to show explicit weather there is a relationship between prophylactic antibiotic use and occurrence of SSI.
3. Can you justify the adoption of 250 as appropriate sample size for this study?
Validity of the findings: No comment
Additional comments: this article will make an interesting read for researchers in the field of surgery and infection control practitioners generally. Important areas of concerns have been highlighted in the manuscript.


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: SURGICAL ANTIBIOTIC PROPHYLAXIS USE AND INFECTION PREVALENCE IN NON-COSMETIC BREAST SURGERY PROCEDURES AT A TERTIARY HOSPITAL IN WESTERN AUSTRALIA—A RETROSPECTIVE STUDY
Review round: 1
Reviewer: 2

Output:
Basic reporting: Clear professional language used throughout.
Well-structured format.
Tables with clear and relevant information.
Data supplied well.

The current article contains information related to oncologic aspect and management of breast surgery. There is only 1 patient who had Breast Reduction and 1 patient who had implant insertion, in the series of 250. Therefore the article does not cover the entire scope of breast surgeries, with special reference to Aesthetic or Cosmetic aspect of the surgery.
Antibiotics also plays an important role in implant related aesthetic breast augmentation mammoplasty and augmentation mastopexy. Inclusion of the research related to aesthetic aspect of breast surgery and carried out in the past, is important to cover the role of antibiotics related to this spectrum of breast surgery. Without such information, current article will not appear complete or comprehensive. I would strongly recommend the role of duration of antibiotics in breast augmentation mammoplasty contained in the following article:
1.  Khan UD. Breast Augmentation, Antibiotic Prophylaxis and Infection: Comparative
     Analysis of 1628 Primary Augmentation Mammoplasties to Assess the Role
     and Efficacy of Length of Antibiotic Prophylaxis. Aesth Plast Surg. 34:42-47. 2010

Equally there is an article where no antibiotics were given to 899 patiernts who had breast surgery and had a low (2.2%) infection. This reference is also very important to include in this article. (Courtice EH, Goldwyn RM, Anastasi GW (1979) The fate of breast implants with infection around them. Plastic Reconstr Surg 63:812-816
Experimental design: Data ant its analysis is robust, statistically sound.
Experimental Design
Original research.
Research questions well defined and fills an identified knowledge gap.
Methods well defined with reasonable details.
Validity of the findings: Data is robust and statistically sound.
Conclusions are well stated and linked to original research questions.
Additional comments: Congratulation on writing such a great, informative and scientific article highlighting some very important aspects and gapes  related to the protocol of Australian Therapeutic Guidelines for the prevention of Surgical Site Infection. However, I would like to recommend changing the title to;
"Surgical antibiotic prophylaxis use and infection prevalence in non-cosmetic breast surgery procedures at a tertiary hospital in Western Australia - a retrospective study".
 There are only two procedures in the series of 250, which appears to be aesthetic in nature, These two procedures may well have been performed in patients, admitted for management of breast cancer.


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: SURGICAL ANTIBIOTIC PROPHYLAXIS USE AND INFECTION PREVALENCE IN NON-COSMETIC BREAST SURGERY PROCEDURES AT A TERTIARY HOSPITAL IN WESTERN AUSTRALIA—A RETROSPECTIVE STUDY
Review round: 1
Reviewer: 3

Output:
Basic reporting: Line 67 what is WA? Please write in full.
Lines 91-94 should be remove or moved to the introductory section.
Lines 128-136 should be remove or moved to the introductory section.
Line 122 to 123 rephrased as follows …………. “were performed using chi square statistics within crosstab menu dialog of spss version ……….”
Experimental design: It is necessary to clarify the type of surgery (clean, contaminated, dirty) etc. Because the rate of infections may differ according this.

What was the criteria used in the determination of SSI from

1.	No Clinical correlate between laboratory and infections and antibiotic selection?

2.	In order to properly examine the impact of prophylactic antibiotics on SSI incidence and length of hospital stay the author should include data on Microbial pathogens obtained from laboratory investigations the patient's records, Because the rate of infections differ according to this.

3.	The author should in addition consider looking at the relationship between SSI, type of surgery and microbial distribution and include (if available) record the hand wash before approaching the patient.
Validity of the findings: The scientific level is not very high appears to be only data collection.
Why chi-square test and not ANOVA or MANOVA?

As a limitation, the author should indicate that no post-discharge infections were recorded for this study.

Finding are valid

Conclusions needs will need slight modification if corrections are made.
Additional comments: A well written manuscript.  However  the suggested modifications should be made.


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: SURGICAL ANTIBIOTIC PROPHYLAXIS USE AND INFECTION PREVALENCE IN NON-COSMETIC BREAST SURGERY PROCEDURES AT A TERTIARY HOSPITAL IN WESTERN AUSTRALIA—A RETROSPECTIVE STUDY
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors have satisfactorily responded to the comments. However, the authors have earlier published an article in 2017 with a similar aim as the current one ''To examine adherence with therapeutic guidelines (eTG) in breast surgery .. ''. May the authors justify the need for the current publication and assure the journal that this is not is not a duplicate publication.
As stated in the last review, discussion is not necessary in abstract. The authors should preferably state their conclusion and possible implications of their findings.
Experimental design: Satisfactory
Validity of the findings: The authors have conducted an excellent review of the level of adherence to therapeutic guidelines, well written with professional language.
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: SURGICAL ANTIBIOTIC PROPHYLAXIS USE AND INFECTION PREVALENCE IN NON-COSMETIC BREAST SURGERY PROCEDURES AT A TERTIARY HOSPITAL IN WESTERN AUSTRALIA—A RETROSPECTIVE STUDY
Review round: 2
Reviewer: 2

Output:
Basic reporting: Clear professional language used through out.
Experimental design: The article contains information related to the oncologic aspect of breast surgery and this original research clearly meets aim and scope the Journal.
Validity of the findings: I am happy with the experimental design of the study. The data presented is robust and statistically sound.
Additional comments: Thanks for making the changes to the article. The article itself contain useful information based on scientific research and data collection.


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: SURGICAL ANTIBIOTIC PROPHYLAXIS USE AND INFECTION PREVALENCE IN NON-COSMETIC BREAST SURGERY PROCEDURES AT A TERTIARY HOSPITAL IN WESTERN AUSTRALIA—A RETROSPECTIVE STUDY
Review round: 2
Reviewer: 3

Output:
Basic reporting: I find it satisfactory. the authors has address all my observations
Experimental design: Adequate,considering his stated limitations.
Validity of the findings: A good work.
Additional comments: The author addressed all off my comments humbly.


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: SURGICAL ANTIBIOTIC PROPHYLAXIS USE AND INFECTION PREVALENCE IN NON-COSMETIC BREAST SURGERY PROCEDURES AT A TERTIARY HOSPITAL IN WESTERN AUSTRALIA—A RETROSPECTIVE STUDY
Review round: 3
Reviewer: 1

Output:
Basic reporting: My concerns have been addressed.
Experimental design: Satisfactory
Validity of the findings: Excellent
Additional comments: No additional comments


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

Input:
Title: MOLECULAR CHARACTERIZATION OF THE GIANT FRESHWATER PRAWN (MACROBRACHIUM ROSENBERGII) BETA-ACTIN GENE PROMOTER
Review round: 1
Reviewer: 1

Output:
Basic reporting: I would like to commend the authors on presenting the data and results in a clear and unambiguous way.

I would like to see some improvements made to the introduction. In its present form, the introduction seems like a compilation of semi-disconnected paragraphs. By the end of the introduction, a connection can be seen. But I would suggest modifying the introduction to present a more connected background, which clearly justifies the relevance of the study, as well. Furthermore, the introduction goes into a lot of details about aspects such as humoral factors etc which are not appearing in the study at all. While it is always nice to have sufficient background and teach the reader more about the field, it could also help to shorten it and utilize that section to clearly mention the goals and gains of this study.

Some minor errors:

1. In the entire manuscript, please replace the apostrophe with the prime symbol for 5' etc.
2. Corrections needed:

Line 45: replace culture with aquaculture
line 57: "neutralize against invasion" -- please fix the sentence
Line 112: replace nest with nested
Line 127-28: change to: ..RNA sample was first treated with CIAP (...) to remove...
Line 246: replace islands with island
Line 249: Mba54 is used without introducing the concept. Please rearrange this section.
Line 345: rosenbergii was (space between the two words is missing)
Experimental design: The authors have presented a systematic study and have well characterized the promoter region. The molecular dissection, luciferase studies and identification of the various genetic elements has been very well conducted and presented.
Validity of the findings: I would again like to complement the authors for presenting a very neat study. They have thoroughly investigated and characterized the beta actin promoter.

I have one general comment. While reading the introduction, I got the impression that the use of Mbap over other promoters including Cbap would prove beneficial in driving gene expression. But, their activities are about the same. While it is useful that Mbap works as well as Cbap, I would recommend modifying the introduction accordingly.
Additional comments: No additional comments


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

Input:
Title: MOLECULAR CHARACTERIZATION OF THE GIANT FRESHWATER PRAWN (MACROBRACHIUM ROSENBERGII) BETA-ACTIN GENE PROMOTER
Review round: 1
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: In this manuscript, the authors study and characterize the gene promoter of actb1 in freshwater prawn, which can be a potential approach to protect prawn from disease and therefore benefit aquaculture economics. The author does sufficient and solid work as well as good interpretation of the experiment data. Meanwhile, the conclusions are clearly stated and reasonably drawn according to the experiment data. Overall, the paper is well-prepared without big issue of experiment design or data analysis. The only question is that the last part of study (comparison between prawn and carp actb1 promoter) doesn't fit the whole story of paper well due to the weak connection with previous parts. A better transition is necessary for its addition in the main context of paper. Otherwise, it should be deleted or moved into the supplementary part.
     As far as the authors fix this, I would suggest acceptance 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: NON-VISUAL EXPLORATION OF NOVEL OBJECTS INCREASES THE LEVELS OF PLASTICITY FACTORS IN THE RAT PRIMARY VISUAL CORTEX
Review round: 1
Reviewer: 1

Output:
Basic reporting: No Comment
Experimental design: See "General Comments"
Validity of the findings: See "General Comments"
Additional comments: There is little doubt that touch interacts with vision, even at the primary sensory level, as has been shown by numerous studies (Merabet, Lotfi B., et al. "Combined activation and deactivation of visual cortex during tactile sensory processing." Journal of neurophysiology 97.2 (2007): 1633-1641.; Merabet, Lotfi B., et al. "Rapid and reversible recruitment of early visual cortex for touch." PLoS one 3.8 (2008): e3046.; Shams, Ladan, and Robyn Kim. "Crossmodal influences on visual perception." Physics of life reviews 7.3 (2010): 269-284.; Vasconcelos, Nivaldo, et al. "Cross-modal responses in the primary visual cortex encode complex objects and correlate with tactile discrimination." Proceedings of the National Academy of Sciences 108.37 (2011): 15408-15413.; Lunghi, Claudia, and David Alais. "Touch interacts with vision during binocular rivalry with a tight orientation tuning." PLoS One 8.3 (2013): e58754.).

I am therefor not sure what the authors are trying to achieve with yet another study that demonstrates that the primary visual cortex responds to tactile stimulation. The interesting question is ignored! i.e. “WHY does touch trigger a response in V1?”

What the authors do not mention, neither in the introduction nor in the discussion, is that the results can be explained simply by visual imagery. Many neuroimaging studies of visual mental imagery have revealed activation of V1 (Kosslyn, Stephen M., and William L. Thompson. "When is early visual cortex activated during visual mental imagery?" Psychological bulletin 129.5 (2003): 723.). It is therefore plausible that tactile exploration of objects triggers visual imagery.

I guess that the authors, by exposing the rats to novel (and not familiar) objects, automatically did rule out visual imagery to explain the results; there is however no reason to believe that tactile exploration of unfamiliar objects in the dark does not trigger visual imagery.

I wish the authors had included a condition where rats explore familiar objects (for instance objects placed into the cage, days or weeks before the experiment). My prediction is that it would be easier for the rats to visualize those familiar objects, compared with novel objects (in the dark), and that the expressions of the molecular markers, for the “familiar” condition would even be stronger than for the “novel” condition. Any outcome, comparing a “familiar” with a “novel” condition would yield information that contributes to our understanding of why touch interacts with vision at the level of V1.

I encourage the authors to do one of the following:

-	Either address all my concerns and provide (very) convincing arguments of why this study is novel and contributes to our understanding of cross-model interaction AND discuss the possibility of visual imagery (or why to exclude it as a possibility), in the introduction and/or conclusion.

-	OR (preferred!!) perform additional experiments, adding a familiar objects condition, and change the scientific question from “does touch interacts with vision at the V1 level?” (already answered) to “why does touch interact with vision?” (interesting!).


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: NON-VISUAL EXPLORATION OF NOVEL OBJECTS INCREASES THE LEVELS OF PLASTICITY FACTORS IN THE RAT PRIMARY VISUAL CORTEX
Review round: 1
Reviewer: 2

Output:
Basic reporting: Previous work has shown that mRNA levels of certain immediate-early genes (IEGs) are elevated in V1 following whisker-based exploration of novel objects in a dark arena. Pereira et al. are essentially providing a replication study where they build on these previous results and show an elevation of the corresponding protein product. The manuscript is clearly written; however, the findings are somewhat over-sold: there is no evidence in the paper for long term plasticity or cortical reorganization, I would caution the authors to refrain from such speculation. The methods are described clearly. The two major issues (detailed below) relate to experimental design and a statistical error. Short of these being addressed the work is not suitable for publication. However, if the issues are remedied the paper represents a solid piece of histological work and could be considered for publication in PeerJ.

Minor points:
1.	Third to last sentence in the abstract (line 49) was probably intended to read: “three hours after exploration” rather than “after three hours of exploration”
2.	In the discussion, linking IEG expression to long term plasticity is a bit of a jump, the results certainly don’t warrant the phrase “indicate directly”
Experimental design: Major issues:
1.	Locomotion (more precisely, all type of movement, including rearing, grooming, active whisking etc.) also activates the cortex, in fact it was recently shown to be one of the strongest activators, even comparable to relevant sensory stimulus (see preprints from Harris and Churchland labs). It is easy to imagine that animals in control boxes, with no foreign objects to explore, spend more time sitting quietly / asleep than their “stimulated” counterparts. Short of demonstrating that the animals spend similar amount of time moving (locomoting, grooming etc.) the results can be just as easily explained without cross-modal activation. Satisfactory demonstration could involve quantification of infra-red video footage or some other motion sensor and should not be particularly costly or time consuming.

Minor points:
3.	It would be important to describe what environment are the animals exposed to in the 40 minutes / 2 hours and 40 minutes between exposure and euthanasia, as this could have a profound impact on IEG expression. Discussing the time dependence of IEG expression would also be helpful to allow the reader to contextualize the observations.
4.	Specificity of an antibody should be determined in a mouse where the antigen was knocked out, using serum with no antibody only proves that the concept of immunolabelling works, not that the antibody labels its target. If the KO strains are not available, the minimum would be to cite previous work that validated these particular antibodies in some way.
Validity of the findings: Major Issue:

2.	Since the authors provide all the data used in the quantification I have re-run their analysis using the exact same statistical method in the same software. If all data points are treated as independent observations there is still no significant difference between EGR-1 in control and at 3 hours. I am not sure why the authors claim a difference there. C-Fos and pCaMK2 calculations match the manuscript. However, this way of calculating differences is incorrect: the paper treats each image as an independent observation. Due to the inherently nested nature of the data (3 images collected from each animal, variance between animals is comparable to variance within each animal), results from the 3 sections / animal should be averaged and statistics should be done on a basis of 1 animal = 1 observation (n). Calculated correctly the only significant difference was between control and 1 hour after exposure for all three proteins. There is no detectable difference between either control and 3-hour or 1-hour and 3-hour time points.

Minor points:
5.	Nuclear EGR-1 staining after exploration is clearly visible and the difference in pCaMK2 staining is appreciable as well on Figure 2 but it is hard to see the if there is any change in c-Fos staining. Is it just a poor example?
6.	There are very visible luminance differences in the example images which might be problematic since the results hinge on accurate image quantification. The authors should explain why there are such large differences in the images if, as stated, they were processed all together.
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: NON-VISUAL EXPLORATION OF NOVEL OBJECTS INCREASES THE LEVELS OF PLASTICITY FACTORS IN THE RAT PRIMARY VISUAL CORTEX
Review round: 2
Reviewer: 1

Output:
Basic reporting: In their revised manuscript the authors have addressed the concerns I brought up in the previous round. I recommend the publication of the manuscript in PeerJ.
Experimental design: -
Validity of the findings: -
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: ACCURACY OF DEEP LEARNING, A MACHINE LEARNING TECHNOLOGY, USING ULTRA-WIDE-FIELD FUNDUS OPHTHALMOSCOPY FOR DETECTING IDIOPATHIC MACULAR HOLES
Review round: 1
Reviewer: 1

Output:
Basic reporting: 1. line 61-
Please correct Optus to Optos and rewrite the sentence as “The study dataset included 910 Optos color images obtained at Tsukazaki Hospital (Himeji, Japan) and Tokushima University Hospital (715 normal images and 195 MH images).” because the original one was difficult to read.

2. line 111, ROV should be ROC.

3. line 125-
I don’t know what this sentence meant.

4. line 203
The authors wrote that "If surgical treatment is performed at an appropriate time in MH patients, a good prognosis can be obtained".
How the Optos-based telemedicine system is used for the determination of appropriate timing?
Experimental design: 1. As the authors commented, the limitation of this study was the inclusion of only normal and MH eyes.

2. line 81-,
When did authors obtain the informed consent from each subject? Were all images used in this study collected for the purpose of this study after obtaining the informed consent from each subject?  According to the clinical research ethical guidelines, the researchers can include the existent data after they disclose the research information.
Validity of the findings: Although I admit the accuracy of the AI, the scores of ophthalmologists for the diagnosis of MH were low, especially the sensitivity. Were those ophthalmologists instructed 1:1 ratio of the normal and the MH image in the data set?
Additional comments: 1. There are eyes having “pseudo” MH. Please discuss whether the AI can differentiate true and pseudo MH.

2. The results discourage the "real" ophthalmologists. In addition to the speed, the accuracy of the diagnosis was superior in the AI than in the ophthalmologists. Please discuss the role of the ophthalmologists in the future.


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: ACCURACY OF DEEP LEARNING, A MACHINE LEARNING TECHNOLOGY, USING ULTRA-WIDE-FIELD FUNDUS OPHTHALMOSCOPY FOR DETECTING IDIOPATHIC MACULAR HOLES
Review round: 1
Reviewer: 2

Output:
Basic reporting: Good enough.
Experimental design: Concise and good.
Validity of the findings: Data is robust, statistically sound.
Additional comments: Nagasawa et al. reported the possibility of deep learning for the detection of idiopathic macular holes in ultra-wide-field fundus images. This study is unique and new. I think this paper has a sufficient priority to be published in PeerJ. However, I also have several minor concerns in this manuscript.

1. line 39; the authors emphasize that Optos dose not need mydriasis. In the current study, it is not clear all the Optos images were taken under the condition of non-mydriasis.
2. line 75; Images from patients, complications, such as vitreous hemorrhage, asteroid hyalosis, 76 intense cataract, and retinal photocoagulation scars, and other conditions, such as fundus diseases, were excluded. Additionally, images with poor clarity were excluded. Moreover, images from patients with stage 1 MHs and those with retinal detachment were excluded. The authors need to describe how many Optus images were excluded from all images.
3. Table 2; it is unclear what 32:80±7:36 and 13:58:00±3:19:16 actually mean.
4. I am not sure why the authors use Optos to detect MH. OCT should be more accurate, easy, and more common.