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

Input:
Title: SPATIAL PATTERNS IN THE CONTRIBUTION OF BIOTIC AND ABIOTIC FACTORS TO THE POPULATION DYNAMICS OF THREE FRESHWATER FISH SPECIES
Review round: 1
Reviewer: 2

Output:
Basic reporting: In this study, the authors use statistical models to explore the influences of biotic and abiotic variables on the population dynamics of two age classes of three fish species with contrasting life histories across part of their geographical range - France. They followed this exploration with more statistical models to test whether experimental variation in these biotic and abiotic variables were best described by "range-shift" or "abundant-centre" spatial patterns. Aside from their main explorations, the authors also describe statistical models used to allocate individual fish of each species to one of two age classes (0+ and >0+) based upon their length.

Overall, I found the study interesting, well-written and well-structured. Nevertheless, I also found it difficult to understand. In part my difficulties arise from incomplete descriptions of the methods and theory. Specifically, the overall question(s) and hypothesis(es) or prediction(s) are not clearly stated, with the result that (in my opinion) the study seems to meander towards the conclusions. The question presented in the last paragraph of the Introduction is not clear: it does not mention the fact that the species had contrasting life-history strategies, nor that the study of spatial patterns was actually a test between competing a prior hypotheses (no effect versus the range-shift and abundant-centre hypotheses). In my opinion, these omissions suggest that the comparisons between species and spatial patterns were not central to the study design, but rather included as an afterthought. If I am wrong and they were central to the study design, then one could imagine an analysis that included model terms representing those effects in the population dynamical models and which could be used to test their importance, e.g., using model comparison (as is done in the current spatial patterns analysis). Specifically, “species” could be added as a three-level factor and coefficients representing altitude/latitude and distance from range centroid could be included in each age-class-specific model. I understand that this would differ from the current approach that examines how variations in each parameter due to the elasticity analyses are associated with each spatial pattern, but I remain unconvinced that this approach is any more interesting that the approach I suggest...
Experimental design: Again, I found the study to be interesting, but not entirely convincing. This is because it did not seem to address clear question(s) and hypothesis(es) or prediction(s).

I could not find it written whether the population dynamical models were fit for all species combined or separately (I assume that they are fit for species separately). Figure 1 suggests that the responses between the different species were quite similar. Would it be interesting to test for species differences in their responses to these biotic and abiotic variables thereby testing whether their "contrasting" life-histories are important in this study?

The “range-shift” hypothesis is not limited to vertical range-shifting (altitude) as described in this study, but also includes horizontal range-shifting (latitude) (e.g., Parmesan, C., Ryrholm, N., Stefanescu, C., Hill, J. K., Thomas, C. D., Descimon, H., ... & Warren, M. (1999). Poleward shifts in geographical ranges of butterfly species associated with regional warming. Nature, 399, 579-583). I therefore question the results of the spatial exploration - would the results be similar if latitude was tested instead of altitude? Personally, I don’t think that Figure 3 brings sufficient information to the study to merit its inclusion, particularly because the interpolated values are shown on different scales for all maps. In my opinion, Figure 4 ought to include plots where the null model was preferred, but that no trend line should be fitted.

The description of the methods used in the “Spatial pattern in the contribution of
biotic and abiotic factors” section were too sparse for me to understand what was done (although it seems that the elasticity values were used as the response variables; lines 246-248). Personally, I am not entirely convinced by this analysis and I would prefer to see a combination of model fitting and model selection used when fitting the population dynamical models to test the support for the competing a prior spatial pattern hypotheses.

I did not well follow the descriptions of the mixture models used to separate age 0+ and >0+ individuals, perhaps because the procedure is quite involved? I do understand random forests, but I could not fully understand what was done prior to the random forest fitting.

I could not find accessible geographical range polygons for the three species on the IUCN Red List. I would appreciate more information about how distance to the geographical range centroid was calculated.

While the functions included to account for biotic effects, such as apparent recruitment rate and density-dependence, were somewhat crude (e.g., are all >0+ individuals mature and successful spawning females?), I commend the authors for acknowledging and attempting to account for such nuanced effects in their analyses.
Validity of the findings: I also struggled to understand the study because the raw data and analysis code were not described or provided. I note that the authors sent the raw data with their submission, but I also note that the population abundances were provided as densities rather than counts, there is no length data to repeat the age classification, and neither is there a description of the data provided. Perhaps worse than those, it appears from examination of the data provided that there were many zero counts, particularly among age 0+ fish, but that this is not discussed or shown anywhere in the study write-up. Personally, I believe strongly that the raw data should be shown and if space is an issue, then Figure 3 could be dropped. Aside from the data, I note that the authors state that they provide the analysis code, but I did not find it. Although perhaps not a requirement to understand the paper (provided the questions, predictions and Materials and Methods are better described), providing the code would make it easier to understand the study.
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: SPATIAL PATTERNS IN THE CONTRIBUTION OF BIOTIC AND ABIOTIC FACTORS TO THE POPULATION DYNAMICS OF THREE FRESHWATER FISH SPECIES
Review round: 1
Reviewer: 3

Output:
Basic reporting: -	I think the introduction section reads well and is well referenced.
-	L55-75. This section would benefit from the addition of the author’s hypotheses regarding the variables tested for each age-class and species – which is somewhat provided in the first section of the methods, however I would like to see more specific hypotheses supported by literature on the ecology of the fish species studied, for example, any existing evidence on relationships between temperature and population vital rates? I would also like more specification of the direction of effects, e.g. L95-96 “(either positively or negatively)” – which direction for each species? The detail on L58-60 could be omitted as this information is already supplied in the methods.
-	I would like to see a plot or some summary information of the temperature data to see how much the annual mean temperature variables vary between sites. Also, this would show whether mean temperature ever exceeded the species maximum values as shown in Table 1. And whether a quadratic effect was necessary? Perhaps the authors can provide their hypotheses for this effect.
-	I would recommend a visualisation of the species range and geographic centre of the range, considering the spatial element is the focus of this study. Also, the table suggests there’s quite a difference in scale, with roach having a much larger range relative to the other species. And where the leading/trailing edges are, etc. This figure could be combined with topography to visualise the differences in altitude across the study sites.
-	More of the Discussion section should focus on placing the findings of the study in the context of the existing knowledge of the ecology and population dynamics of each fish species. For example, comparing the literature of temperature effects/density-dependence on population abundance, recruitment rate, survival, etc of each species and especially any literature considering spatial variation in population response of these species to intrinsic and extrinsic factors (e.g. Britton et al., 2013 DOI:10.1111/j.1600-0633.2012.00588.x; Faro et al., 2021 DOI: 10.1016/j.jenvman.2021.112100)
-	L219. There is no Appendix S1 and thus, no JAGS code – this would be a valuable addition, which I commend the authors for preparing and perhaps has been omitted by accident?
-	Fig 2. I appreciate the consistency of using terminology from the equations in the figure legends, but for ease of understanding, I would advise simpler labelling, e.g. “Mean temperature (linear/quadratic)”, “Recruitment rate”, etc. Also, in the figure legend ‘the first raw’ = ‘the first row’?
-	Fig 3. The figures should be on the same colour scale to aid interpretation, especially as the maps and legend values are too small to quickly glance and read, also it is a bit misleading when the maps are similar colours but the scale is a different range.
-	L295-296: ‘size-classes’ be consistent with terminology, these were first described on L59 as age-classes
-	I think the term ‘abiotic factors’ is unnecessary throughout the manuscript – the authors only looked at temperature so would it be clearer to refer to these as temperature variables. Also, sometimes these variables are referred to as ‘climatic variables/factors’ e.g. L265 – again, consistency with terminology helps the reader to follow the study.
-	L333. I recommend changing ‘growth rate of >0+ individuals‘ to ‘population growth rate’ as it currently reads as the somatic growth rate of individuals
-	Table 1 should be referenced.
-	L172. I appreciate the inclusion of model equations – it really helps the reader understand the analysis. Do the authors mean to include a term to show that models were built separately for each species? Or could add this information to the text to avoid repetition.

Raw data
-	From my understanding, the authors supply the following raw data for each species: Densities of 0+ and >0+ for each year and site, length of time-series, mean temperature, variation in temperature, the number of time-series, but I am not sure what $samp is? Perhaps the site area? It would be helpful to supply more descriptive identifiers either in the dataset itself or supporting text file.
-	The fish data supplied are densities, but the models are fit to count abundance data – I understand the authors include log(site area) as an offset in the models, but with these data, the analyses aren’t reproducible, and it would be beneficial to see the raw data.
-	No length data are provided, which are used to age the fish. I would like to see a summary plot of the length-frequency histograms used to age the fish for each species in the supplementary material.
-	No data are supplied for the altitude and distance to geographical centre of distribution, which are essential for the third part of the analysis.
-	A general comment is that it would be beneficial to visualise the raw data or a summary of the raw data. I think the supplementary material are a suitable place for this, or particularly the main manuscript when describing response variables and explanatory variables used in the analysis.
Experimental design: -	In my opinion, not accounting for a likely effect of density-dependence on 0+ abundance is a significant omission, as in many freshwater fish species, this is the age where density-dependent processes are considered to have the strongest effect on population sizes (e.g. Grenouillet et al., 2001 Freshwater Biology; Jonsson et al. 2001 Journal of Animal Ecology DOI: 10.1046/j.1365-2656.1998.00237.x). Furthermore, including the abundance of >0+ to estimate recruitment rate is too crude: many factors which are not considered here, such as age, maturity stage, sex ratios, size and thus fecundity of spawning individuals, will influence recruitment and should be accounted for. Also, the authors assume constant survival of recruits independent of recruit density. To improve this parameter, I recommend the authors to explore the use of a recruitment function, such as Ricker or Beverton-Holt, where recruitment from eggs to 0+ is estimated as a density-dependent function (and can be modified by explanatory variables as required).
-	I find the elasticity analysis and the spatial pattern analysis to be difficult to understand and reconcile with the research question. I do not understand why total population abundance (the sum of 0+ and >0+ abundances) was used to test the influence of a partialized effect of each explanatory variable. Different variables were included in models of each age-class so it does not seem appropriate to test for the relative influence of all variables (which were chosen specifically for the particular age-class) on the total population abundance. And of the variables that were included in both models, some influenced 0+ and >0+ abundance differently, for example temperature variation appears to influence 0+ abundance in all species linearly, but >0+ abundance in all species in a quadratic manner, therefore it does not seem appropriate to combine the abundance of each age-class to determine relative influence of each variable. I would recommend that either the elasticity analysis or another Bayesian variable selection technique (see Hooten and Hobbs, 2012 DOI: 10.1890/14-0661.1
for a review of techniques) is performed for each age-class model separately. I also find the step of first generalising the influence of explanatory variables on age-specific abundance across spatial scales by including site as a random effect, and then attempting to describe these patterns by spatial covariates to be confusing. Would it not be better to test for spatial effects within the initial abundance model?
-	L115-117. I note in the methods that the authors took steps to discard time-series data that contained at least 50% of non-null captures for at least 15 years. Was this to maximise the amount of catch data >0 in the time-series? From looking at the raw data, when these data are split by age-classes, there seem to be quite a lot of time-series that include >50% non-null captures, especially in the 0+ age-class (Barbel >0+: n = 7, 0+: n = 21; Chub >0+: n = 2, 0+: n = 55; Roach >0+: 5, 0+: n = 61). Did the authors investigate whether these data are zero-inflated and do they need to consider the amount of zero captures in the model structure? It would also be useful to note the distribution of these sites with high levels of zero-captures to ensure that the representation of sites with limited >0 catch data is not geographically bias and therefore suitable for spatial analysis. For example, high numbers of zero captures in the 0+ compared with low numbers of zero captures in the >0+ could suggest that the sites surveyed are not appropriate juvenile habitats. This could be a more reasonable explanation than consecutive years of failed recruitment or poor sampling of juveniles. It also might suggest that these data are not suitable to investigate influences of 0+ population abundance.
-	L193-194. The apparent survival transition – is it possible that fish in the >0+ age-class were different ages? If so, estimating the probability of surviving between subsequent age-classes (i.e. 0+ to 1+) would not be suitable. If all of the fish are 1+ in the >0+ age-class, perhaps this terminology would be clearer?
-	L112. Electrofishing surveys taken in periods of low flow? Could the authors clarify what ‘low flow’ represents? How might this influence the population dynamics sampled, i.e. abundance and size of individuals, and the subsequent dynamics investigated in this study? (e.g. Allouche and Gaudin, 2003. Doi: 10.1034/j.1600-0706.2001.940310.x; Britton and Pegg 2011 Doi: 10.1080/10641262.2011.599886).
-	L115-117. It would be useful to know the sampling protocol that the authors chose as the reference that is cited (Poulet et al., 2011), state different methods: 2-pass depletion fishing, point sampling and fractional sampling. Depending on the efficiency of the sampling, the authors could attempt to account for imperfect sampling by estimating capture probability for each class in an age-structured state space model (Parent & Rivot, 2003. Introduction to hierarchical Bayesian modelling for ecological data) and estimating a ‘true abundance’ with which to describe with explanatory variables.
-	Do the authors think that their temperature variables captured changes that would be relevant to preferences/behaviours described in the species life histories, i.e. that opportunistic strategy maximises the colonizing capability of species in environments with frequent changes at small temporal and spatial scales, or periodic strategy favoured in seasonal environments? It seems that a mean annual temperature variable might be too coarse to distinguish short-term or seasonal fluctuations in temperature.
-	Why did the authors only choose to include temperature as an abiotic variable and not some discharge related variable? I appreciate that with the large number of study sites, it would be difficult to obtain data for other environmental and habitat variables. Could the authors provide more justification for their choice in the methods.
-	L98-106. Are the leading and trailing edges of the population ranges always high and low-altitude populations, respectively? I would expect a latitudinal shift also as populations migrate to cooler, higher latitudes. There is existing evidence for an effect of temperature and latitude on life history traits of barbel and roach (Britton et al., 2013 DOI:10.1111/j.1600-0633.2012.00588.x). Why did the authors not consider latitude as an explanatory variable to test for evidence of the range-shift hypothesis?
-	How is the spatial distribution considered, i.e. what about sites that are closer together? Does the random effect account for this? Could the authors provide more information as to how they accounted for any spatial correlation between sites?
-	L240-248. This section is not written well enough to understand the analysis done; the response variable is not stated clearly, nor the model type or distribution or whether separate models were fitted for each species. All the other models have associated equations to aid understanding, this should be replicated here.
-	L181-182. Length-frequency histograms do not provide enough information to inform recruitment rate, for example male barbel tend to mature at a smaller size than females (Vilizzi et al., 2013 DOI: 10.1051/kmae/2013054)
Validity of the findings: -	Fig 1. Quite similar responses of the species to the abiotic and biotic variables! This is an interesting finding and, in my opinion, should be discussed more in the Discussion section.
-	L264-265. “All species presented a tendency for an effect of climatic factors on the dynamic of both 0+ and >0+ individuals…” Can the authors provide more description of the temperature effects – were they linear/quadratic for which species, direction of effect etc.
-	L270-272. The authors state that >0+ individuals are more sensitive to changes in biotic factors than 0+ individuals, but they omit testing the effect of density-dependence on 0+, which is considered a strong regulator of population size in juvenile freshwater fish, and thus, I don’t believe they can draw this conclusion from this analysis.
-	L275-278. The lack of relative contribution of abiotic variables could indicate that the temperature variables used, i.e. mean annual temperature was not at suitable resolution to capture an effect, or that other abiotic factors might be more useful in describing abundance, such as discharge, habitat and prey availability, etc. The authors do note that other variables could be important (L424-425), but could they expand on potential limitations of the temperature variables used?
-	L284-285. “For most factors we found that these spatial variations were mostly related to altitude and less so to the distance to the geographic range center”. To assess the validity of tests of relative influence of explanatory variables, it is necessary to include some information of the data used to calculate each variable or summarise the variables. Could this finding be an artifact of there being more variation in altitude rather than distance to the geographic range centre? According to the IUCN Red List maps cited as the source of species ranges, the centre of each species’ range appears to be in central Europe, so all the populations studied here will be relatively far from the centre? Again, some summary of these covariates would be useful. From Fig. 4, it looks like few values of high-altitude sites might have strong influence on the shape of the slope?
-	L279. I don’t see from Fig. 2 that the effects of abiotic variables ‘outcompete’ those of biotic factors? All of the parameter estimates for the temperature variables overlap zero and thus don’t have strong effects?
-	L338-339 – why would higher abundances result in a ‘release from competitive pressures’?
-	L353-355. The findings of this study do not support this statement, as such it should be removed.
Additional comments: This study aims to identify the relative influence of abiotic and biotic variables on the population abundance of two age-classes of roach, chub and barbel at multiple sites throughout France. The authors use a series of analytical steps to first describe age-specific abundance as a function of the abiotic and biotic variables, then test the relative strength of each variable on total abundance by partializing out the effect of each variable. Then, finally, they attempt to identify whether there are spatial patterns in the relative strength of each variable on total abundance, by testing the influence of altitude and distance to geographic range centre and performing model selection. I think the authors attempt to answer an interesting research question and that the study benefits from a large (both temporally and spatially) dataset. However, I have numerous concerns with this study, most imperative is the statistical analyses, which ultimately, I don’t believe enable them to answer their research questions. I have provided more detail in my comments, which I hope are clear and helpful.


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

Input:
Title: SPATIAL PATTERNS IN THE CONTRIBUTION OF BIOTIC AND ABIOTIC FACTORS TO THE POPULATION DYNAMICS OF THREE FRESHWATER FISH SPECIES
Review round: 2
Reviewer: 1

Output:
Basic reporting: -	Regarding a suggestion that more of the Discussion section should focus on placing the findings of the study in the context of existing knowledge of the ecology and population dynamics of each fish species, which the authors marked as ‘Done’. However, I could not find where this addition is?
-	Figure 1 is a nice addition to help the reader understand the data and modelling process. The new Figure 3 and updated Figure 4 look like good additions and Figure 4 appears to be clearer to read in terms of the colour scheme, however the resolution is too low so the figures are unreadable in their current format, so I couldn’t evaluate these (the resolutions of Figs 2, 3 and 5 should also be improved as they are also difficult to read when zoomed in).
-	I was unable to load in the revised .RData files to review, I received the following error message: ‘bad restore file magic number (file may be corrupted) -- no data loaded’
-	L218-219; 301-302 (and please check throughout) – terminology of variables have been changed elsewhere but a few places remain with the original terms.
Experimental design: -	Regards using a ‘recruitment rate’ to describe 0+ abundance: I had expected to see a more explicit parameter to account for density-dependence in 0+ abundance, such as egg biomass, or spawner biomass as a proxy for this (I stated this in my previous review). In their response to my latest comments, the authors have stated that they do not have egg data, and it seems clear that they do not have information on age-structure or maturity in the older population (or if they do, then they haven’t used it). In my opinion, the authors should clarify this situation in the Methods section (alongside the description of the analyses), in order to justify how they have attempted to account for density-dependence in 0+ abundance. Specifically, I suggest the authors add a paragraph in the Methods stating why and how it is important to account for density-dependent effects, with referenced examples for this study species, together with an description of the data available and unavailable, e.g., egg data, to account for its effect, and what assumptions had to be made in lieu of egg data. A more involved, but more convincing, addition would be to undertake a sensitivity analysis to explore the sensitivity of the results to different assumptions about the value and variation in recruitment rate.
-	Furthermore, while I appreciate the sentence added to the Discussion on L584-600 describing how the study can be expanded by exploring the influence of other factors on recruitment rate, I do not consider this a substitute for the aforementioned paragraph in the Methods section (alongside the description of the analyses) stating the data limitations and attendant assumptions. In summary, I too appreciate that there has been an attempt to account for these effects, but I think the interpretation of results should be more cautious and the explanation of this method be more explicit to allow a reader to interpret the validity of this result.

-	Regarding a previous comment on the apparent survival transition from 0+ to >0+: the authors have confirmed that the >0+ size-class comprises individuals of various ages, and so perpetuates my concern that survival transitions between all ages >0+ are assumed to be the same, i.e., whether they are estimating survival between 0 to 1+, or 0 to 2+, 0 to 3+ etc. This is a strong assumption. A more relaxed assumption might be to allow survival probabilities to change with ontogeny. Also, the authors describe in their responses that ‘the 0+ size class in a given year cannot be influenced by the number of recruits in the previous year because those individuals are transitioning to the >0+ size class between consecutive years’; but a 0+ fish cannot transition directly to a 2+ or older fish. Even assuming a constant survival rate between different age-classes, the survival rate should be applied sequentially. I assume and understand that the authors do not have the ages for the population, however the authors could limit the >0+ size-class to only 1+ individuals using the existing approach used to identify two size-classes using length-frequency histograms.
-	Furthermore, the authors could better justify the apparent survival transition by providing some information about the species ecology. For example, average/range of ages that the species mature, any information about sex ratios in the population. This would help the reader assess the validity of this approach, such as, if fish of these species are capable of spawning at ages 1+ and older, then it would be more reasonable to assume that individuals of this age, i.e., that constitute the >0+ abundance, can contribute to the apparent recruitment rate. If the authors stick with their existing approach of two size-classes, then I would expect some comment on the limitations of this study when trying to account for apparent survival transition.

-	L622-624. This addition based on previous comments regards the study findings that spatial variations were mostly related to altitude/elevation rather than to the distance from the centre of the species range might be misunderstanding my original comment: the imperative point here, is that the data points were not widely distributed throughout the species entire ranges, rather than evenly distributed, and thus the dataset seems somewhat inappropriate to test for hypotheses related to distance to centre of the species range as all the populations included in the study are in a relatively similar location in relation to the centre. This is reiterating a previous point but I feel an important one given the intentions of the study. In my opinion, I would focus more on discussing the more convincing aspects of the study such as the effects of covariates on the abundance of fish species studied and spatial variation in these effects.
Validity of the findings: no comment
Additional comments: The authors have done a large amount of work to respond to all the reviewers’ comments and I believe that the manuscript is much improved as a result. Some of my previous concerns regarding the abundance estimation and distribution of datapoints remain, and I have a few minor comments; please see details below.


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: SYNOVIAL FLUID PROTEOME PROFILE OF SURGICAL VERSUS CHEMICAL INDUCED OSTEOARTHRITIS IN RABBITS
Review round: 1
Reviewer: 1

Output:
Basic reporting: I have reviewed the indicated manuscript which attempts to assess differences in the proteome of the synovial fluid (SF) derived from the knees of rabbits subjected to an ACL transection or exposed to a chemical toxin (monoiodoacetate).

While the results indicate some differences, the experimental approach has a number of severe limitations, and as well the outcomes. Several of the figures presented (Figures 1-3) are not very informative in their current form and could be deleted. In particular, Figure on is  not relevant and Figure 2 does not indicate the state of the menisci, which is well known to be altered by 8 weeks post-ACL-T.

Aspects of the English language should be checked by an expert.
Experimental design: The experimental design has a number of flaws which are indicated below:
1. The ACL-T operation is an inflammatory stimuli and there is no sham group. While some of the inflammation may be transient, it can lead to changes in the SF.
2. Use of the contralateral joint may not be appropriate due to the contralateral effect that is well known.
3. The cells in the SF were not removed prior to freezing and thus, disrupted cells in the SF would contribute proteins.
4. The sex of the animals was not indicated-readily corrected!
5. The state of the synovium and the menisci was not indicated. In rabbits, after ACL-T, the medial meniscus undergoes degeneration by 8 weeks post-surgery. Also, the inflammed synovium contributes significant proteins to the SF including MMPs and other proteinases. 6. However, the MMPs, particularly MMP-13, were not apparently upregulated and this is well documented in the literature.
7. How did the authors decide on the dose of the chemical toxin to use? Is it a maximum to elicit a response. This toxin kills cells in more than just cartilage-synovium, menisci, capsule, ligaments. Were the affected tissues repopulated by 12 weeks? No real histology presented or performed apparently.
Validity of the findings: While the authors did detect some differences in the SF content following the two interventions, and the results may indicate differential responses, there are a number of limitations to the experimential design that limit interpretation and the significance of the differences. Based on other molecular changes that are known to occur following ACL-T in the female rabbit knee, it would appear that the primary methodolgical approach, that of 2D gels, is not sufficiently sensitive to detect the multitude of changes known to occur. The fact that the authors did not apparently remove the cells that are known to be in SF from both OA patients and the knees of preclinical animals with OA, presents a further complication to the interpretation.
Additional comments: While the concept of SF proteomics may reflect the on-going progression of OA in the knee, as well as the type of OA related to the "inciting" stimulus, there are a number of limitations to the experimental design of this study that cloud the interpretation of the 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: SYNOVIAL FLUID PROTEOME PROFILE OF SURGICAL VERSUS CHEMICAL INDUCED OSTEOARTHRITIS IN RABBITS
Review round: 1
Reviewer: 2

Output:
Basic reporting: nothing to add
Experimental design: In general the experimental design is well documented. However, the limited number of 5 animals per group is not discussed or accounted for. Based on the outcome what should be the number of animals needed to provide reliable outcome (what is the power of the study)?
Also the choice to have only a macroscopical assessment of the cartilage OA grade feels somewhat limited. Histological evaluation or even biochemical evaluation would be more appropriate, especially to place the findings in a broader context. Why is not the synovial inflammation included?
This could be helpful to put the proteins found and the validity of the models in more clinical relevant perspective.
What was the average amount of SF collected within each animal?
Validity of the findings: In general, the findings seems valid and are appropriate discussed. However, this reviewer is not certain what message the authors really want to bring across to the readers. What is the clinical context? The models differ in outcome, which can be expected but is the one more appropriate to use or does this depend on the intervention you want to apply in such a model in relation to the protein expressed.
Also the limitations of the study are limited presented, especially with regards the use of a rabbit model. for instance, the marked differences in joint biomechanics and gait when compared to humans. In addition to biomechanical differences, important structural differences also exist between rabbit and human joint tissues. Rabbit cartilage is *10 times thinner than human cartilage (0.3–0.7 vs 2–3 mm) but has much higher chondrocyte density. The distribution of cartilage zones is quite different between the 2 species, particularly because the thickness and cellularity of the transitional and radial zones are highly variable in the rabbit, even among sites within the same joint. The rabbit meniscus is also more cellular; it has less vascular penetration than the human meniscus; and it can heal rapidly. Rabbit cartilage has been reported to exhibit spontaneous healing, particularly in relativelyyoung animals. (some references: Pedersen DR, Goetz JE, Kurriger GL, et al. Comparative digital cartilage histology for human and common osteoarthritis models. Orthop Res Rev. 2013; 2013(5):13–20.; Poole R, Blake S, Buschmann M, et al. Recommendations for the use of pre- clinical models in the study and treatment of osteoarthritis. Osteoarthritis Car- tilage. 2010;18(suppl 3):S10–S16.; Cook JL, Hung CT, Kuroki K, et al. Animal models of cartilage repair. Bone
Joint Res. 2014;3(4):89–94.; Proffen BL, McElfresh M, Fleming BC, et al. A comparative anatomical study of the human knee and six animal species. Knee. 2012;19(4):493–499.)
Additional comments: In general this is a well written manuscript describing the synovial fluid proteome in two different induced rabbit OA models. In addition to the points addressed above is what message the authors really want to bring across? It seems somewhat vague formulated.

Minor:
abstract line 38: omit the word 'were'


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: SYNOVIAL FLUID PROTEOME PROFILE OF SURGICAL VERSUS CHEMICAL INDUCED OSTEOARTHRITIS IN RABBITS
Review round: 2
Reviewer: 1

Output:
Basic reporting: In the revised manuscript there seems something wrong with the references. Several references are mentioned (e.g. Snickers, Mohan) in the text but are not listed.
Experimental design: The revised manuscript has been adapted to the comments of the reviewers, .
Validity of the findings: The limitations of the study have been adjusted but the limitations of the model used are not mentioned (e.g rabbit vs human), to provide a better context. Also the number of animals used could be better justified, the argument that other studies have used similar amounts of animals and found significant outcome is not a real valid argument, data can be still be coincidence. As suggested previously, a power calculation on the primary outcome of the present results can further support the validity of the present results obtained with the 5 animals.
Also the argument that the model reacts according other literature is a bit misleading as different species have been used (e.g rabbit vs dog Sniekers et al. 2008) which might lead to different results due differences in amount of loading of the joint etc.
The histology shows a bone-cartilage interface, so the authors are able to score the subchondral bone area (thickness, tightmark changes) in order to have a felling of the bone changes as is mentioned to be of importance by the authors in the discussion.
Additional comments: Though the authors try to improve the manuscript based on the comments of the reviewers, this reviewer feels that not all items have been addressed or answered completely.

There is no statement in the answers why not the menisci or synovial tissue has been included (or discarded) in the analysis while both reviewers make clear remarks on the importance of these tissues.
Or the use of the contralateral joint as a control or the lack of a sham is not discussed in the manuscript (part of the limitations).

Though the authors have stated there goal, this reviewer misses the discussions what this means in a more clinical or pathophysiological context? What do these results implicate? Surgical induction leads to a stronger proteomic response but to less structural damage in time as compared to the chemical induction which is clinical less relevant type of induction? This reviewer feels that this is missing in the discussion.


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: EFFICACY OF BRAIN NATRIURETIC PEPTIDE VS. NICORANDIL IN PREVENTING CONTRAST-INDUCED NEPHROPATHY: A NETWORK META-ANALYSIS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The English is clear, concise and easy to read, only need small revisions on:
 1. One typing error at lines 18 (chang -> change)
 2. One inappropriate use of word in a sentence at line 47 (to therapy -> to prevent/treat)
 3. It is always better to explain an abbreviation in the first time it appears in the article, even if the author think the abbreviations is so well known that it is not necessary to explain it. (e.g. NMW at line 223)

Literature references are up-to-date  and sufficient.

All figures and tables must be self explanatory, this means all symbols and abbreviations need to be defined either in the table itself or in the notes under the tables, and the title needs to be very clear, and this needs to be repeated separately for each table and figure.

Conclusion is relevant to the title.
Experimental design: Methods of systematic review and network meta analysis  have been described with sufficient detail and comprehensive.

No more comment .
Validity of the findings: no comment.
Additional comments: Congratulations to the authors for this interesting manuscript and might be helpful for preventing CIN strategy for patients undergoing CAG or PCI.

The English is clear, concise and easy to read, will only need minor revisions on:
 1. One typing error at lines 18 (chang -> change)
 2. One inappropriate use of word in a sentence at line 47 (to therapy -> to prevent/treat)
 3. It is always better to explain an abbreviation in the first time it appears in the article, even if the author think the abbreviations is so well known that it is not necessary to explain it. (e.g. NMW at line 223)

All figures and tables must be self explanatory, this means all symbols and abbreviations need to be defined either in the table itself or in the notes under the tables, and the title needs to be very clear, and this needs to be repeated separately for each table and figure.


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: EFFICACY OF BRAIN NATRIURETIC PEPTIDE VS. NICORANDIL IN PREVENTING CONTRAST-INDUCED NEPHROPATHY: A NETWORK META-ANALYSIS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Dear Editor
thank you for the opportunity to review this interesting innovative article.
recent advances in statistical analysis and especially network meta analysis in the last decade helped in comparing heterogeneous interventions. this relatively new technique aided in answering many interesting issues related to patients health and quality of life.

the problem of CIN and the best treatment approach is on the top list of many radiologist, interventional cardiologist and patients as well.

from scientific point of view, the authors have made a nice job of clarifying the dilemma and possible solutions to it.

however the writing English needs numerous revisions. I would suggest that the authors consult an academic writing processionals to clear some statements. I will upload the original file which contain SOME of the mentioned sentences for your considerations.

some of the figures are unnecessarily duplicated. example. figure 4 is a duplication of figure 3 and 5.
the legends in figure 8 are not clear for comparisons, I might suggest using a colored version to clarify the treatment effects more in the funnel plots.
Experimental design: experimental design was nicely presented, clear and unambiguous aside from minor language grammar issues as previous.
Validity of the findings: the results need further clarification. the statement at line (127-128) for example is misleading.
i can not agree with some of the recommendations.
example at line 131-134 are not correct as the CI spans unity and hence are not significant.
this conclusion was also mentioned in the published abstract and needs further clarification or rephrasing.
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: DISENTANGLING BIAS FOR NON-DESTRUCTIVE INSECT METABARCODING
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript is well written, although there are few minor edits to be made. The tables and figures keep changing the order that the taxa are presented, which puts undue strain on the reader to keep trach of the different species used. The figure legends are often too brief without providing sufficient detail. At times I wondered about the article structure. It's okay, but not great. There are a few different aspects of metabarcoding being examined here, but I was constantly trying to establish what was being tested, shown at each step. It might be useful to add more structure to the text where you explicitly state each aspect and deal with them in turn. DNA extraction method. Primers. Insect/DNA/PCR pools. It's all in there, but I had to step away from the article and when I came back I needed to back through all the methods to figure out was going on. Could be structured to be more intuitive following the Figure 1 structure. seems like most of the code is on github and the DNA will be posted, but I didn't see the latter available.
Experimental design: An interesting design. The molecular methods and bioinformatics seem appropriate. The root mean square error is fine, but some context on what a desirable result for this may be useful. It kind of depends on  the application I think. Some details in the molecular methods may have been  left out because they are so common, but please reference any standard protocols that you use and be explicit regarding any deviations. The layout of the known pools to test how biases at different steps effect results is useful. The degree of sclerotization is probably about right, but seems a bit hand wavy. / subjective. The volume measurements are also unclear. They are taken from a stacked (2D) image, but it's impossible to know how this was extrapolated into volume. Were multiple images taken so that L x W x D could be taken? what body part was used for these? The statistical model doesn't provide some of the usual tests I expect to see regarding model assumptions, independent variables, model fit, etc. This could be improved.
Validity of the findings: I had a couple takeaways. 1) non-destructive DNA extractions can work for metabarcoding (good stuff!)
2) metabarcoding has persistent and difficult to predict biases that keep it from being useful for measuring abundance, although presence/absence is effective.

These are both useful for areas of research where metabarcoding may be considered. I'm not particularly encouraged that its a useful technique for areas where abundance does matter, which is unfortunate.

The findings seem valid based on the data / stats presented (although if this is not he main conclusions the author wants to make then maybe some more clarity is in order).
Additional comments: I made a few minor comments on attached version of the ms.


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

Input:
Title: DISENTANGLING BIAS FOR NON-DESTRUCTIVE INSECT METABARCODING
Review round: 1
Reviewer: 2

Output:
Basic reporting: Intro and background provide good context to the study, literature is well-referenced and relevant and the English language used throughout is clear and professional.

Figures are relevant however the quality is low (increase resolution/size of points on figures 2,3, and 4), however this may be the saving to PDF process

SRA supplied for raw data but no number given so could not access raw data
Experimental design: This study is within the scope of the journal and includes rigorous investigation performed to a high technical standard, methods are well-described, and the research question is well-defined, relevant and meaningful.
Validity of the findings: Novel study with benefit to literature clearly stated. Data SRA provided but no number so cannot access.

Strong conclusion and links to original research question in addition to suggesting future research ideas
Additional comments: Fantastic study – I very much enjoyed reviewing this manuscript and feel it will be a great addition to the literature.


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: MICROBIAL BIOGEOGRAPHY OF THE WOMBAT GASTROINTESTINAL TRACT
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript by Eisenhofer et al. seeks to compare the microbiota of different gut regions in two species of wombat. The paper is generally well written, and the findings clearly articulated.

However, I could not see reference to where the raw data for this study has been deposited in the manuscript itself. Please add this to the paper before publication.

Minor comments:

L64-72: There has been a study that looked at the different GI sites of the koala (Barker, Christopher J., et al. "Investigation of the koala (Phascolarctos cinereus) hindgut microbiome via 16S pyrosequencing." Veterinary microbiology 167.3-4 (2013): 554-564.). Given that the koala and wombat and phylogenetically closely related species, it seems remise not to outline this study here and compare its findings to those of this study in the discussion.

L197: If I am reading Figure S1 right (I do not have the caption for this figure) then it seems that only the distal colon samples really separate based on species on axis 2 of B. This seems to be indicated in the next sentence, however, I would suggest making that clear here.

 L206-210: Do you mean figure S2 here?

Figure 1B: DC1 and DC3 are labelled but there is no DC2. Is this a typo or is there another reason for this?

Figure 3: I would like to see a larger number of families represented in this plot as for the DC in the SHNW a large proportion of the microbiome is assigned to “other” making it difficult to see the detail of this community.
Experimental design: The main weakness of the paper is that only a single animal of each species was studied making it difficult to know if the between species differences found were true species differences or inter individual variation. However, this weakness is acknowledged by the authors in the discussion and given the difficulty in obtaining such samples the results are still worth reporting.

There are also a few instances where further information on the methods would be valuable as outlined in my specific comments.

Specific comments:

L163: Please clarify, so the ASV level analysis was or was not performed on the rarefied dataset?

Figure 1: Is it possible to indicate exactly where in the GI tracts the samples were taken from? For instance, the small intestine is quite long in both species. Were the samples collected from the middle of this section or towards one end? This may be important for reproducibility of the findings.
Validity of the findings: My main concern is related to the preliminary data manipulation prior to the analyses. Specifically, the exclusion of ASVs found in a single sample. While these ASVs will not give you any information about sharing among samples they may provide important information on the individuality of samples and on alpha diversity. The removal of singltons (ASVs for which only a single read is returned) is common and reasonable as they often represent sequencing error but the removal of a sequence because it is only seen in a single sample could be misleading. If my interpretation of how the analyses were performed is correct then this will artificially reduce the variation between samples, making them appear more homogeneous. Reducing variation in this way could make differences between the GI sites appear more convincing. Therefore, I think it is important for all ASVs to be included in the analyses or at the very least for the authors to show (in an online supplement) that it does not change the findings.

Minor comments:

L187-200: When I look at figure S2 it seems that the small intestine samples are actually quite distinct between the two species and also that the two SI sites in the SHNW are quite different from one another, which does not come across in the PCoA. Perhaps the PCoA is mostly reflecting the differences in richness between the different regions? I think it is important to identify this in the text.

L258-274: The distal colon had a high proportion of Firmicutes and this phylum has many fibrolytic members. Can you comment on how the overall capacity for fermentation is likely to differ between the GI sites based on the microbial composition? While no doubt the PC is a site of significant microbial fermentation I am not convinced that the distal colon is not based on the discussion of the results presented here.

Figure 1: Given there are only two or three samples per gut region, boxplots that show the different quartiles are not an appropriate way to represent the data. Instead, please just plot the raw data points without the boxplots.
Additional comments: Minor comments:

L232-240: I would be really interested to see what the overlap is between the sites if you repeat this analysis at the genera or family level. Given the known issues with intragenomic heterogeneity in 16S genes and also in assigning ASVs to lower taxonomic levels the differences seen in composition may not be biologically meaningful.


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: MICROBIAL BIOGEOGRAPHY OF THE WOMBAT GASTROINTESTINAL TRACT
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript is well-written and communicates a clear story based on the study data. I had some comments where the authors did not include important relevant details, and made suggestions for improvement (see attached file). I also suggested that the authors change the order of findings in the results section so that is easier to follow.
Experimental design: I made minor suggestions for communicating study aims and predictions more clearly. The authors do need to be more transparent about their sampling and study limitations throughout their manuscript. They do not need to dwell on this, they just need to remind readers that their data comes from only two individuals, and thus, their inference (and statistical power) is limited. Again, see my comments on the attached file.
Validity of the findings: The methods section was detailed and the research could be reproduced by others. The sequence data and code are accessible. The conclusions are tied to the study objectives.
Additional comments: Please see the attached PDF file for my detailed feedback and suggestions to strengthen 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: MICROBIAL BIOGEOGRAPHY OF THE WOMBAT GASTROINTESTINAL TRACT
Review round: 1
Reviewer: 3

Output:
Basic reporting: The authors present new observations of microbial diversity using current methods with molecular markers. The authors report that microbial diversity differs between the regions of the digestive tract. Most importantly assessments of digesta in the terminal part of the tract may be distinct from those taxa in the primary fermentative region in the proximal colon.
Experimental design: The interpretation of the data is limited by the lack of observations on the substrates available to microbes (e.g, plan fiber fractions, plant taxa) and the environment in the tract (e.g., pH, osmolality, temperature). The flow of substrates to the microbes and the turnover of the medium in any section could be inferred from the state of the host (e.g., season, sex, reproductive state, age, body mass and body condition).
Validity of the findings: The study is best described as a preliminary observation because only one individual of each species was sampled. This experimental design confounds individual with species, that is, the design is not sufficient to compare species without providing more observations of individuals within each species. It is likely more samples can be obtained from wild specimens that are killed on the roads for SHNW and BNW.
Additional comments: Line 178, "is thought to occur" seems overly tentative since fermentation rates and the digestion of plant fiber was reported for both species.
Line 193. species and indvidual are confounded because there is only one individual per species.
line 205 "At the phylum level, these samples" Do you mean stomach and small intestine samples?
Line 243. How does this work help us to understand the relationship between miocrobe and host? What is the big picture here? See recent papers
R. Kartzinel, J. C. Hsing, P. M. Musili, B. R. P. Brown, R. M. Pringle, Covariation of diet and gut microbiome in African megafauna. Proceedings National Academy of Sciences USA 116, 23588-23593 (2019).
C. A. Rojas, S. Ramirez-Barahona, K. E. Holekamp, K. R. Theis, Host phylogeny and host ecology structure the mammalian gut microbiota at different taxonomic scales. Anim Microbiome 3, 33 (2021).

Line 282. Both animals died after an illness. Intake of food and water was likely interrupted. Diet is also different. There is not enough replication to compare species just the samples within indviduals.
These data are not sufficient to test the hypothesis that fecal and colonic microbes differ. It is possible but you need more indviduals with covariates of diet composition.
Line 301.  "However, …" is a long compliicated sentence. What are biological replicates? Are these observations of multiple samples from the  same region? Consistency in PC scores is a circular argument because the scores are the outcome of partitioning variation in the data set with the statistical analysis.
Line 307. Any literature to support this idea about ned and live cells?


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: MICROBIAL BIOGEOGRAPHY OF THE WOMBAT GASTROINTESTINAL TRACT
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: I have reviewed a previous version of this manuscript and in general the authors have adequately addressed my comments and concerns. There are, however, a few points where I feel further improvements could be made as detailed below.

I appreciate the authors taking the time to perform the additional analyses I requested. I feel that there would be benefit to having analysis 2 and 3 included as part of the supplementary documents and referenced in the main text. However, if the authors make the additions I suggest on L170 of the revised manuscript then analysis 1 is probably not necessary to present.

L170: I suggest adding the information presented in the response to my comment here to reassure other readers that the removed ASVs were only a small portion of the dataset. i.e “These ASVs represented ~4.3% of identified variants and 0.16% of the average relative abundance of the dataset.” I also suggest clarifying that ‘sample’ here refers to a single replicate of a gut region.

L214: I suggest adding a sentence after the note here (or at another relevant point in the m.s.) pointing out the differences between SI regions in the SHNW. e.g. “On further examination of the relative abundance of the different Phyla across gut regions (supplementary figure 2) a large difference between the proximal and distal small intestine samples from the SHNW was observed, with PSI dominated by Proteobacteria and DSI dominated by Fusobacteria.”

L280-283: I would like to see a sentence here that acknowledges the high proportion of Firmicutes in the DC and their potential involvement in fibre degradation. https://www.mdpi.com/1424-2818/5/3/627 is a good reference for this.

Figure 5 and New supplementary heatmap: I think the addition of the supplementary heatmap showing all the families would be a good addition to the current set of supplementary figures. I would, however, like to see the higher-level taxonomy added to both heatmaps, particularly as some ASVs are undefined at the family level or have uninformative names such as “uncultured”.


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: MICROBIAL BIOGEOGRAPHY OF THE WOMBAT GASTROINTESTINAL TRACT
Review round: 2
Reviewer: 2

Output:
Basic reporting: Manuscript is detailed and well-written, and contains sufficient background and interpretations. See minor comments in the “General comments” section.
Experimental design: Methods are reproducible and raw data/code are publicly available.
Validity of the findings: Minor comments to improve clarity, and comments to authors to be cautious when mentioning “species differences” of any kind as they do not have the statistical power to do so.
Additional comments: Introduction
L34- replace “For both the bare-nosed wombat and the southern hairy-nosed wombat” with “For both wombat individuals”

L99-101: rephrase to “We predicted that the proximal colon, the primary site for plant fermentation, would harbor a distinct microbial community […]”

Results
L193-unclear what the acronyms stand for
L192- in supplementary material, this figure is labeled as SFig2 instead of SFig1

L200- would add that for both wombat individuals, compositional differences are more apparent between PC1&2 and the latter proximal colon and distal colon.

L207- start new paragraph with the sentence “Like richness”, to show authors are transitioning to beta diversity analysis

L209-210 - rephrase “we calculated the microbial compositions of these distinct sites” to “we compared the microbial community structure of these distinct sites”

L211-212- rephrase “Using both methods, the major differences observed in microbial composition were associated with GI tract site not wombat species, with stomach” to “As predicted, major differences were observed in microbial composition along the GI tract in both wombat individuals, with stomach…” I do not believe it is appropriate to mention host species analyses in this sentence.

L214-217- please clarify the sentence. As it currently reads, it is saying the same thing twice

L217-222: move these two sentences after the sentence “Interestingly, the microbial composition of the first proximal colon.”

L244- SI figure 3 to SI Figure 3

L269-285: authors can talk about the “species” differences without having to mention the word “species.” The authors do not have the statistical power to discuss "species" differences because they have an N=1 for each species. Thus, authors can instead say: “A major finding was that the microbial communities present in the first proximal colon region (PC1) were more similar between wombat individuals than to subsequent colon region samples from the same individuals”. Authors can still mention why the inter-individual differences were observed (the two wombat individuals represent distinct species that differ in their gut morphologies and habitats, etc).

L342- authors can add that future work can be comparative and include more host species that are closely and distantly related to the wombat to look at the potential role of host phylogeny as well.

Supplemental
I could not find the legends for the supplemental figures again
Include a legend in the spreadsheet for Table S1

Figures
Fig4- reorder color key so that stomach appears first, then small intestine, proximal colon, etc
Fig6- use non-acronyms whenever possible, I suggest authors spell out full species name (Bare-nosed wombat) at the top of the diagrams, and then for example shorten BNW.PC1 to just PC1


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: DISTRIBUTION, ECOLOGICAL RISK ASSESSMENT AND SOURCE IDENTIFICATION OF POLLUTANTS IN SOILS OF DIFFERENT LAND-USE TYPES IN DEGRADED WETLANDS
Review round: 1
Reviewer: 1

Output:
Basic reporting: (1) A proof reading by a native English speaker should be carefully conducted to improve both language and organization quality.
There should be a space between values and units. Lines 26-27: “3.71 ± 1.03 g/kg”, “57.17 ± 15.16 g/kg”.
The “Figure” and “Fig” are improperly mixed.
There is an inappropriate use of italics. Line 68: “Nemerow pollution index (NPI)”.
Line 105: The “&” should be changed to “and”.
(2) Line 126: (GB15618-1995, GB/T17141-1997, HJ491-2019). Which national standard is this?
(3) Line 138: Table S1 is not found in the manuscript.
(4) Lines 143, 155 and 161: No spaces should be left before “where”.
(5) Line 172: Distribution of nitrogen, phosphorus. However, only TN is mentioned in the content.
(6) Lines 173 and 174: It can be seen….. What does "it" stand for here?
(7) Line 390: it was found that….. What does "it" stand for here?
(8) Line 411: We know land use….. The author avoids using the first person.
(9) There are few references in recent 3 years.
(10) The format of references in the paper can not meet the requirements of journals.
Experimental design: The manuscript lacks the importance analysis of the research area.
Validity of the findings: There is a lack of in-depth discussion in the manuscript.
Additional comments: The author needs to examine the whole manuscript in detail.


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: DISTRIBUTION, ECOLOGICAL RISK ASSESSMENT AND SOURCE IDENTIFICATION OF POLLUTANTS IN SOILS OF DIFFERENT LAND-USE TYPES IN DEGRADED WETLANDS
Review round: 1
Reviewer: 2

Output:
Basic reporting: 1. This manuscript needs careful editing by someone with expertise in technical English editing, paying particular attention to English grammar and sentence structure so that the goals and results of the study are clear to the reader.
2. This study is mainly focusing on the pollutants of different land-use types. Therefore, your introduction needs more detail about how different land-use types influence the contents and distribution of pollutants in the previous study.
3. The paper is overall well-structured, while the results need to be clearly and simply stated without discussing how they related to the previous research in this part.
Experimental design: It has described clearly enough the methods to allow others to repeat them, and evaluation methods are also appropriate ways to assess the status of pollution. However, both RI and PLI could identify the comprehensive pollution level of heavy metals. I think it would be best to choose one of them.
Validity of the findings: I suggest the authors state the conclusions as clearly as possible.
Additional comments: The current study investigated the distribution and sources of heavy metals, As, and nutrients in a degraded wetland by measurement methods and multiple evaluation methods. It is a topic of interest to the researchers in the related areas but the paper needs very significant improvement before 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: DISTRIBUTION, ECOLOGICAL RISK ASSESSMENT AND SOURCE IDENTIFICATION OF POLLUTANTS IN SOILS OF DIFFERENT LAND-USE TYPES IN DEGRADED WETLANDS
Review round: 1
Reviewer: 3

Output:
Basic reporting: The writing of the article is relatively standardized, but the logic of English expression is not enough. It is recommended to further improve and polish. “Introduction”: author introduced the role of sediments and soils on the "sink" of pollutants and the importance of evaluation, but does not introduce the background of the impact of land-use types changes on pollutants. It is recommended to supplement and straighten out the logic. In addition, the GIS-based processing methods and pollutant evaluation indicators (Line64-84) introduced in the introduction have been widely used, and there is no need to repeat them. If this content is needed, it is recommended to add to the "Materials and Methods" section. The introduction of Line84-94 about study area is recommended to be placed in the "Study area and sample collection" section of the “Materials & Methods” section. Moreover, it is far-fetched to put forward the research question, recommended to reorganize and write.
Experimental design: The experimental design is reasonable, and recommended to supplement the specific depth of surface sediment collection (Line119).
Validity of the findings: The conclusion can basically summarize the results, and recommended to supplement future research prospects.
Additional comments: 1)	Some evaluation indicators are used in the article to evaluate the degree of pollution, and source analysis is carried out, so the title of the article can be appropriately corrected to match the content of the article
2)	It is recommended to add the significance of the study in the abstract
3)	Line111, it is recommended to supplement the relevant information of three rivers, which can correspond to the information of Line258. It would be better if the rivers can be marked in Figure 1.
4)	Line174-175 and Line195-196 are duplicated, which leads to confusion in the logic of this paragraph. It is recommended to rearrange the language
5)	Line180: Is this water area? Or Lake area?
6)	Line201，What kind of change pattern?
7)	7) It is recommended to directly use p < or > 0.01 or 0.05 to express the significance in the text to be more concise and clear.
8)	Line221, There is a problem with the english expression.
9)	Line249 "The pollution degree was clean" has a problem, it is better to change to "the pollution degree was lower".
10)	The references in the text and the reference list do not correspond.
11)	Line352-358 language logic needs to be reorganized.
12)	Line366-367, Line372-373 add corresponding references.


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: DISTRIBUTION, ECOLOGICAL RISK ASSESSMENT AND SOURCE IDENTIFICATION OF POLLUTANTS IN SOILS OF DIFFERENT LAND-USE TYPES IN DEGRADED WETLANDS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The author has revised the relevant content.
Experimental design: The author has revised the relevant content.
Validity of the findings: The author has revised the relevant content.
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: DISTRIBUTION, ECOLOGICAL RISK ASSESSMENT AND SOURCE IDENTIFICATION OF POLLUTANTS IN SOILS OF DIFFERENT LAND-USE TYPES IN DEGRADED WETLANDS
Review round: 2
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Title:” Distribution, ecological risk assessment and source identification of pollutants in soils of different land-use types in degraded wetlands”

I have read the revised MS and I think it is the scope of Peer J, but I am afraid a minor revision is needed for the authors to improve the MS before acceptance for publication.

Specific comments:

1. PLZ add a conclusion or suggestion sentence in the Results portion in the Background part.
2. line 46-48, PLZ add a conclusion or suggestion sentence in the Results portion.
3. line 26, a specific experiment type should be mentioned here.
4. line 56, sorption is also an existed form for heavy metals in the soil environment.
5. line 57-58, revise this sentence, what is ‘the accumulation of these pollutants in wetlands’?
6. line 59, ‘soils pollution’ is a mistake. And line 294, ‘soils heavy metals’, check throughout this paper.
7. line 73, differences in soil pollutants? Types? concentration? Distribution?
8. line 84, what is the ‘to data’? PLZ revise the sentence.
9. line 87, what is the ‘to our knowledge’? PLZ revise the sentence.
10. line 173, revise the unit format.
11. Authors should further improve the writing. More attention should be paid to the logical improvement.
12. The Figures were finished well.
13. Land pattern does determine much of the biogeochemical processes including the changes of soil pH, microorganism communities, the availability of the heavy metals, etc. Authors should further focus on the mechanism for the reason why the land pattern can efficiently control the distribution, risk assessment and the bioavailability of the heavy metals in the soils in the wetland system.


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

Input:
Title: LAND USE AND LAND COVER DYNAMICS AND TRADITIONAL AGROFORESTRY PRACTICES IN WONCHI DISTRICT, ETHIOPIA
Review round: 1
Reviewer: 1

Output:
Basic reporting: 1. The manuscript “Land use and land cover dynamics and traditional agroforestry practices in Wonchi District, Ethiopia (#66775)” provides important data for policy makers of the land use and land cover (LULC) dynamics and the status of traditional agroforestry practices. In addition, the manuscript is clearly written in professional, unambiguous language.
2. If there is a weakness, it is in the Figures and Tables which should be improved upon before acceptance. The manuscript includes sufficient introduction and background, and the work can fit into the broader field of knowledge.
3. The structure of the manuscript conforms to an acceptable format of ‘standard sections’. Figures are relevant to the content of the article, but not sufficient resolution. All appropriate raw data has not yet been provided.
4. The submission is ‘self-contained,’ but the results associated with the hypothesis are insufficient.
Experimental design: 1. The contents of manuscript within Aims and Scope of the journal.
2. The submission clearly defines the research question((1) Are the current agroforestry and crop species taxonomically diverse in Wonchi District? (2) Is there a difference between highland and midland agro-ecological zones in agroforestry practices and species distribution over the three decades? (3) Is there a significant change detection in land-use types in Wonchi District in the past 34 years? and (4) Are there major change drivers in the two agro-ecological zones?), which is relevant and meaningful. The knowledge gap being investigated is identified (LULC changes in Wonchi District in the past 34 years), and the analysis of four objectives in this study contributes to filling that gap.
3. The investigation is conducted rigorously. The research is conducted in conformity with the prevailing ethical standards in the field.
4. The method description provides sufficient information.
Validity of the findings: 1. This research has certain policy guidance, especially through the investigation of land use and land cover change dynamics in Wonchi District in the past 34 years, can provide a basis for government decision-making.
2. The data on which the conclusions are based is provided or made available in an acceptable discipline-specific repository (the Earth Explorer free data provider website (https://earthexplorer.usgs.gov/) of the United States Geological Survey). The data are statistically sound, and controlled (See lines 173-230).
3. The current conclusion section is complex and unclear and should be reorganized and written.
Additional comments: 1. The resolution of theFigures in this study is too low and must be remade before acceptance; Tables must be strictly three-line tables.
2.  No more than three references are recommended for one point of view.（see Lines 46, 58, 68,73, etc.）


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

Input:
Title: LAND USE AND LAND COVER DYNAMICS AND TRADITIONAL AGROFORESTRY PRACTICES IN WONCHI DISTRICT, ETHIOPIA
Review round: 1
Reviewer: 2

Output:
Basic reporting: The is well presented. It can, however, be improved with review of recent literature, especially on the drivers of deforestation and forest degradation in Ethiopia
Experimental design: Most of the methodological descriptions are well presented.
The authors mention that they have conducted analysis of both quantitative and qualitative data. Methods how the data were collected, and types of data collected are, however, not presented in descriptions of methodology. This needs to be presented.
Validity of the findings: The findings are valid and highly relevant to understand about rural landscape management practices and make informed decisions for further improvements.
The analysis was based on both social and biophysical data, including remotely sensed data to assess trends over time. The conclusions are well stated, and are in line with the findings.
Additional comments: Here are few comments/suggestion:
1. Line 22 and 23- it states, 67 indigenous species, and then seven endemics separately. The endemics are also indigenous. I suggest stating it as 74 indigenous species, including seven endemics and 29 exotic species (instead of introduced species, since introduction can also from other locality within the country).
2. Line 32: recommendation only about agroforestry. The study showed that agroforestry has actually increased, through the magnitude is small. Forest is the most affected. recommendation should be regarding all land cover or use types that need special attention, and management action. The recommendation does not indicate any management action required to improve practice as well.
3. Line 98: give the exact range of the geographic coordinates. What is given is one point, and even that is described as 'near'.
4. Line 101. Population data is very old. Use projected population data of the current year, provided by the CSA.
5. Line 104. There is no town called 'Woliso-Giyon'. It should only be 'Woliso'.
6. Lines 135 and 136: please cite all the Flora of Ethiopia and Eritrea volumes that you have referred to.
7. Line 174: It is not clear how you have collected qualitative and quantitative data. There is no data collection method, and no mention of the type of data you have collected.
8. Line 237: like for line 22 and 23, the number of species under different categories should be rephrased.
9. Line 276: 'bee farming' should be replaced with 'beekeeping' here and in all parts of the manuscript.
10. Line 388: replace 'composite' with 'compost'.


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: METHODOLOGICAL APPROACHES FOR ESTIMATING POPULATIONS OF THE ENDANGERED DHOLE CUON ALPINUS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The paper is clearly written, providing sufficiently detailed background and explanations. It is appropriately organised. The supplementary materials are sufficiently detailed to reproduce the analyses. (See Additional comments for specific recommendations.)
Experimental design: The research questions and rationale for the work are well defined/explained. Investigations are performed to a high technical and ethical standard. (See Additional comments for specific recommendations.)
Validity of the findings: Above and beyond the utility of the paper with respect to the surveying and the subsequent management of Dhole populations, the comparison of existing density models applied to new (and bench-marked) data sets is a useful contribution to the literature. The models appear to be specified and estimated correctly, using robust methodology. (See Additional comments for specific recommendations.)
Additional comments: General comments

This well-written paper, which includes both a review of relevant literature and an empirical study, addresses the important practical problem of estimating population densities for unmarked species with small population sizes. In the case of dholes (the species of interest), the authors provide a strong rationale for their work based the paucity of existing knowledge and the need to better inform conservation efforts.

Although many statistical methods have been developed for unmarked density estimation, it is not always obvious which method is most appropriate for a given study. The problem of selecting among candidate models is not just about goodness-of-fit or predictive scores, the validity of inferred quantities (e.g., density) depends on both the degree of violation of the underpinning assumptions of the model and the sensitivity of the model to these violations; yet, these dependencies are difficult to assess. To this end, the authors include a study of a second (marked) species as a bench mark for (unmarked) model performance, leading to useful model recommendations for practitioners working on similar studies.

Overall, I would recommend this paper for publication in PeerJ, given appropriate adjustments/responses to the specific comments/questions that I have added below.

Specific comments

1) Line 135: How many cells have >20% cover?
2) Line 205:206  The correlated binomial model should be expressed as either
N_i ~ poisson(lambda); C_ij ~ binomial(N_i,p_ij,rho); p_ij ~ beta(alpha,beta)
or
N_i ~ poisson(lambda); C_ij ~ beta-binomial(N_i,p_ab, rho)
where the correspondence between the two formulations is
p_ab = alpha/(alpha + beta) and rho = 1/(alpha+beta + 1)
I do not believe it is correct as you have written it. I’d suggest the first variation with the derived parameters expressed in the text.
3) Line304: I found this line hard to make sense of. The text reads very well overall, but I found this whole paragraph difficult to read. In terms of contrasting and assessing alternative estimation methods, it is probably one of the most important  paragraphs in your paper, so you might like to reassess its structure.
4) None of your models included any spatial covariates (i.e., you assumed homogeneous habitat suitability). Model comparison is used in the SECR model to choose among candidate distributions (i.e., to test the inclusion of overdispersion parameters), but it could also be used to assess the merits of including any available predictors. Did you have any suitable covariates? This should be discussed.
5) Failing to account for imperfect detection is identified as a problem in the introduction, yet you assume perfect detection throughout your models (e.g., Line 230). Even though the weaker models appear to overestimate the density (suggesting lack of independence rather than thinned observations), the rationale your modelling choices concerning imperfect detection should be discussed/justified.
6) Line 321-322 Do you have any further thoughts as to why the beta-binomial model produces such large estimates? You mentioned the low detection rates, but is overestimation a known issue in this low-rate scenario? What was the estimated correlation, did it seem reasonable?
7) I found the plots difficult to study because the leopard and dhole results are spread across different plots. It would be helpful to see the plots grouped by species to make a direct comparison of the estimates for the different models. In particular, as side-by-side comparison of the closeness of the SECR and STE estimates for leopards, and the divergence of STE and Beta-Binomial models for Dholes would emphasise your main results. I don’t think that including both abundance and density adds anything useful to the plot since one is a re-scaling of the other.
8) The inclusion of MLE and Bayesian SECR estimates seems unnecessary. Unless it is your goal to draw attention to the similarity of the results, I would suggest it is sufficient to state that estimates are similar, presenting just one and reallocating the figure space.
9) You have presented results for various percentage-adjusted viewshed estimates, but these results are not discussed. I think they should be.


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: METHODOLOGICAL APPROACHES FOR ESTIMATING POPULATIONS OF THE ENDANGERED DHOLE CUON ALPINUS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The article is well written and balanced with the correct use of language.
Experimental design: The study is designed well in that the camera traps were randomly placed and the estimates of dhole population (unmarked) from various methods were compared with that of the leopard (marked) for checking their reliability, using appropriate analytical tools. However, I am concerned with the duration of camera trapping and the method of selecting trap stations. I am not sure whether 16 to 18 days of camera operation is adequate to capture all dholes in the area. The authors need to provide an empirical basis as to why this duration was chosen. I am tempted to ask how camera-trap stations were selected within a chosen grid (4 sq. km) – e.g., based on sign density, proximity to a den, etc. It would also be helpful for future study replication if there is an explanation on why a particular grid size of 4 sq. km was chosen and only 34 out of 80 grid cells were selected for camera stationing.
Validity of the findings: The findings are appropriate, but there is a need for stating the population figures estimated by site-based models since it was hard to understand population figures from figure 3. Please discuss why REM or REST models could not be applied to camera-trap data for dholes in this study. What precluded their use?
Additional comments: Here are some specific comments:

Line 72: Considering removing the comma after 2018b.
Line 156: fit or fitted?
Line 252: The supplementary file 3 was not available for viewing; the authors may have seemingly forgotten to upload it.


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

Input:
Title: GUT MICROBIOTA DIFFERENCES BETWEEN PAIRED INTESTINAL WALL AND DIGESTA SAMPLES IN THREE SMALL SPECIES OF FISH
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript is well written, with an interesting topic and a logical structure. It is focused on demonstrating the baseline of the gut microbial diversity and composition variation between mucosa and digesta samples in three small species of fish. This will provide insights into fish residential gut microbiota identification.  The introduction is appropriate to support the context, and the results are well discussed. If more information is provided as described below, I recommend that the manuscript can be published in Peer J.

Line 31. Please consider removing the word ‘time’ to keep consistent.
Line 64-66. Please support your statement with relevant references.
Experimental design: The research question is well defined, relevant, and meaningful. The experiment is well designed, but more detailed information in methods is needed. Genomic data analysis seems solid, but in the reviewer's opinion, the taxonomic analysis can go deeper to a further level, such as the genus level.

Line 78-81. More detailed information in terms of fish size is needed, such as fish length, weight, etc.
Line 92. If emptied intestines are not washed with saline buffer, how do you make sure there is no digesta left?
Line 152. ‘>=’ is not the correct format. Please change the symbol to ‘≥’.
Line 153-155. It stated that phylogenetic trees were generated.  Please indicate the result and include it in the supplementary section at least. If this is irrelevant, you should consider removing this sentence from the manuscript.
Line 185-200. The indication of nMDS and PERMANOVA analyses belongs to the β diversity analysis. These sentences are more suitable for the last section ‘Analysis of diversity.
Line 199-200. How was the resemblance matrix of the dataset created? For example, the resemblance could be created by calculating the Euclidean distance or Bray-Curtis distance.
Line 202. The fish gut microbiome has been studied in many studies via 16S rRNA sequencing in recent years. Taxonomic composition at the family level may not be powerful or informative enough to explain the variation in the intestinal microbial community. One wonder why you only analysed the microbiota at the family level.
Validity of the findings: All underlying data have been provided. The last section in the discussion can provide insights to further studies, but a clear conclusion can be helpful for summarising the highlights.

Line 256-257. An additional nMDS figure showing the overall microbial similarity between the two sample types is recommended here.
Line 257-259. How do you identify the variance regarding sample type and location? And where is the detailed information?
Line 264. Where is the ‘Table 3’? I assume it is the attached Table 1.
Line 261 -266. This part is a bit confusing. In the discussion (Line 302), you stated the location explained most of the variance. However, the result indicated that the explained variance was lower compared to digesta samples.
Line 267-269. “Most of the families” is not precise. Please demonstrate the result in number or percentage.
Discussion
Line 285-286. The word ‘unique’ is not appropriate to be used here. From my understanding, unique families indicate the families that are either detected in mucus or digesta only. so, there is no comparative degree.
Line 287 and line 366. Subtitles are unnecessary in the discussion section.
Line 319. Remove the word ‘unique'.
Line 323. Please clarify the ‘Salmonids’ species. Mycoplasmataceae are not found to be dominating the gut of freshwater farmed Chinook salmon.
Line 330-331. Please reword this sentence. Detecting these families in digesta and mucus samples does not mean it can be detected in the surrounding environment. It can only be confirmed by analysing the microbiome from the rearing water.
Additional comments: All comments have been listed above.


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

Input:
Title: GUT MICROBIOTA DIFFERENCES BETWEEN PAIRED INTESTINAL WALL AND DIGESTA SAMPLES IN THREE SMALL SPECIES OF FISH
Review round: 1
Reviewer: 2

Output:
Basic reporting: A figure showing where the fish were sampled from along with pictures of the various species would be useful.

Figure 2 could be improved by
a)  showing an NMDS with all samples
b) improving the legend to describe the various metadata categories
Experimental design: Overall the design is good. There is enough replication across species and locations to test the hypothesis if the digesta differs from the general GI tract resident community. The computation methods are generally ok as well. A few questions for clarification:
Why were these species of fish chosen? Did you measure the GI length and total length? Do they occupy different trophic niches?

Line 88 states fish with empty stomachs were excluded. How did one determine this – please explain in more detail along with the approximate proportion of fish which were excluded in the end? Also what were the sizes of the actual fish?

Its likely that during transport many of the fish would have been stressed and therefore defecated in the bags. Were fish transported in individual bags or mixed bags? If mixed, was that also tested to determine if fish from the same transport bag had a more similar microbiome? In the future, I would recommend the researchers kill the fish onsite and preserve either direct in 95% etoh at RT until processing or directly place on dry ice. It would make this a bit easier logistically.

Line 90 states the method of dissection. There are a lot of historical papers describing these protocols which would be good to cite. Did you measure how much digesta was collected in mg? Did you measure the mass of the tissue which was processed through extraction? These could be important for your diversity estimates. If stored in etoh, how exactly did you then extract the sample… did you for instance add the entire volume of etoh or just some volume/biomass.

Lastly, the authors do not describe what part of the gut they actually sampled. Because the length of the fish aren’t described its hard to know the extent this matters but its important to describe if the whole gut vs partial was used. If partial was it towards stomach or anus. The site of the GI will differ in the microbiome.

Line 97: what were the modifications?
Line 98: extraction blanks or negatives aren’t very useful as they will primarily consist of ASVs from neighboring samples rather than background contaminants in a kit. (PMID: 31239396)

Line 146: The decontam pipeline, although published, severely overestimates the contaminants. It will remove many ASVs which are actually important to the outcomes. To ensure the results are robust, authors should reprocess and rerun stats on the dataset without removing these putative contaminants. Please provide details on what these actual contaminants were and their prevalence in the samples. Assuming this was supplemental table 9, you can see clearly that most of these organisms are common aquatic or fish digesta associated and likely should not be removed.

Line 169: how did you account for phylogenetic relatedness?

Line 172: how were the outliers determined?

Line 184: To compare compositional differences, authors only report using jaccard. I would recommend including other distances such as bray-curtis. I would also recommend and am unsure why they opted on not including phylogenetic measures such as unweighted and weighted unifrac.

Line 224: Its unclear if the authors rarified these samples. If they did not, they should justify this in the methods. Sequencing depth is a function of starting biomass which may not have been controlled.
Validity of the findings: The goal of this paper “Gut microbiota differences between paired mucus and digesta samples in three small species of fish” was to investigate and evaluate a new method for comparing the transient vs resident microbiome of the fish gut from small fish. The authors used 16S and compared microbiomes between 3 species of fish where were sampled from a total of 11 locations in Spain. Each fish was processed for 2 sample types: digesta and mucus.

Overall the findings are inline with the methods. I do however believe that some of the findings could change depending on the distance measure used along with the re-inclusion of ASVs which were removed by decontam.

Any reason why V hispanica was less differentiated by sample type and location?
Notes to editor
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: GUT MICROBIOTA DIFFERENCES BETWEEN PAIRED INTESTINAL WALL AND DIGESTA SAMPLES IN THREE SMALL SPECIES OF FISH
Review round: 2
Reviewer: 1

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