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: UPTAKE AND TOXICITY OF CLOTHIANIDIN TO MONARCH BUTTERFLIES FROM MILKWEED CONSUMPTION
Review round: 1
Reviewer: 2

Output:
Basic reporting: References:
The authors missed citing information. They should review the following studies:
- Jesse and Obrycki 2003. Occurrence of Danaus plexippus L. (Lepidoptera: Danaidae)
on milkweeds (Asclepias syriaca) in transgenic Bt corn agroecosystems
- Jesse and Obrycki 2003. Field deposition of Bt transgenic corn pollen: lethal effects on the monarch butterfly
- Hellmich et al. 2001. Monarch larvae sensitivity to Bacillus thuringiensis- purified proteins and pollen
- Hellmich et al. 2001. Impact of Bt corn pollen on monarch butterfly populations: A risk assessment.
- Wolt et al. 2003. A Screening Level Approach for Nontarget Insect Risk Assessment: Transgenic Bt Corn Pollen and the Monarch Butterfly (Lepidoptera: Danaidae)
- Krischik et al. 2015. Soil-Applied Imidacloprid Translocates to Ornamental Flowers and Reduces Survival of Adult Coleomegilla maculata, Harmonia axyridis, and Hippodamia convergens Lady Beetles, and Larval Danaus plexippus and Vanessa cardui Butterflies
- Mattila et al. 2005. Response of Danaus plexippus to pollen of two new Bt corn events via laboratory bioassay
- Oberhauser and Rivers. 2003. Response of Danaus plexippus to pollen of two new Bt corn events via laboratory bioassay.
- Obrycki et al. 2001. Transgenic Insecticidal Corn: Beyond Insecticidal Toxicity to Ecological Complexity

Line 165: provide a reference to justify waiting for 1-month between plant dosing and introduction of larvae.
Experimental design: Methods: Additional details and clarifications should be provided in the methods. Specifically:
1. Information about the location where the experiments where performed, the average temperature, humidity, photoperiod, and time of the year when the study was performed. This information should be provided for each experiment. Insecticides can degrade depending on environmental conditions.
2. How did the researcher ensure that the plants were not exposed to other pesticides due to drift? The authors should provide clarification on the methods.
3. Provide more information about the colony used for the experiments (i.e., the origin of the colony, the number of generations in the lab, is the colony supplemented with field insects?).
4. Where the adults checked for OE? If not, please provide a reference or clarification that rinsing eggs in bleach is enough to eliminate OE.
5. Line 130: indicate the commercial use of Arena 0.25G.
6. To increase the ability of other researchers to replicate the study, it will be useful to include a picture or diagram of the terrarium set up used.
7. Line 144-146: indicate in the rationale for the second experiment (e.g., .estimate LC50).
8. Specify what was used as the control.
9. Line: 71: Where the larvae transferred at the same time? Please clarify.
10. Lines 167-172: explain why fewer eggs were used in the second experiment.
11. Sample collection: indicate the conditions at which the samples were collected and stored.  Is not clear what the author meant by randomly paired.
12. Line 208-209: indicate the tango of the total number of larvae evaluated per treatment per experiment.
13. Data analysis: explain why the difference of analysis was performed between experiment 1 and 2. Indicate the software(s) used for the analyses. Why not perform pairwise comparisons? More details need to be provided for the probit analysis, where the 95% confidence intervals calculated, slope and chi-square estimated? Was mortality corrected to control mortality? An EC50 could have been estimated with the growth rate.
Validity of the findings: Conclusions: the authors missed to discuss and speculated in without indicating that this was speculation and not a direct finding of the study. Specifically:
1. Plants with heavy aphid infestation can increase cardenolide levels in the plants. The authors should discuss if this could have affected the results of their experiments.
2. Line 343-344: Here is important to indicate the concentration found in the study was potentially higher due to the mode of application granular vs seed treatment or foliar, and formulation evaluated (i.e., different adjuvants will affect the effect of the product). The authors should expand on the discussion on the potential difference in concentration depending on the type of application and formulation.
3. Line 359-363: Authors should indicate that the results obtained in this study should be taken with caution given the limited sample size.
4. Lines 393-394: indicate the type of behavioral effects observed in bees and what this would imply for monarchs.
5. Lines 397-407: Authors should specify and discuss that the effects observed in this study were at concentrations higher than what is expected in the field. Also, they should discuss how the concentrations obtained in this study relate to spray applications since they infer that it will be a risk during flowering. Different types of applications/formulations will affect exposure in the field. Furthermore, in what type of landscape the product tested is expected? the effect of a product used in an orchard should not be assumed to have the same effect than in a cornfield for example. The authors should be careful with their conclusions given the limited sample size and the use of a laboratory colony and indicate the limitations of the study.

Figures: provide sample size in the figure legends. Figure 2 and 6 are hard to interpret change the line types or colors to increase legibility.
Additional comments: This paper reports the effects of milkweeds treated with granular clothianidin on monarch butterfly larvae from hatch to pupation, and the effects upon larval survival, larval growth, pupation success, and adult mass. The manuscript is well written, and the research is timely, relevant, and fills a critical knowledge gap. However, before it can be published the manuscript needs additional details and clarification in the methods, further discussion, and interpretation based on the specific use of the product tested, and revise some of the statements provided since they are highly speculative given the sample size evaluated and can lead to misinterpretation. Review the attached document for additional minor suggestions.


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: UPTAKE AND TOXICITY OF CLOTHIANIDIN TO MONARCH BUTTERFLIES FROM MILKWEED CONSUMPTION
Review round: 1
Reviewer: 3

Output:
Basic reporting: There are a couple of locations where references should be added as indicated in the comments to authors. Other than that, the basic reporting in the article is fine.
Experimental design: A couple of locations where the Methods should be clarified regarding the data collection and analysis as indicated in the comments to authors.
Validity of the findings: A couple of locations where the authors might consider an alternative to data analysis and presentation of results in the Results section to improve the manuscript.
Additional comments: L 24 – please indicate here that this was a laboratory or controlled study and not a field study. Perhaps “…monarch butterfly larvae were exposed in the laboratory to contaminated…” would be suitable.
L 30 – if possible, please indicate some statistic or metric to your last sentence to provide evidence regarding reduced growth rates.
L 55 – change “utilize” to “use”
L 59-69 – might consider removing most of the second paragraph regarding bees and merging the topic sentence (L 58-59) with the next paragraph on L 71.
L 120-123 – Perhaps re-write this sentence to ensure it is clear as: “All eggs collected by the vendor from their breeding stock were rinsed in a bleach solution to ensure no infection by the OE (Ophryocyctis elektroscirrha) parasite from wild monarchs butterflies, which can result in mortality of larvae and pupae”. Should also cite an appropriate paper to support this such as: Altizer and Oberhauser 1999 Effects of the protozoan parasite Ophryocystis elektroscirrha on the fitness of monarch butterflies (Danaus plexippus). Journal of Invertebrate Pathology 74:76-88.
L 189 – males generally have larger wings than females so if you did not record sex at eclosion it would be good to note this here.
L 194-216 – thank you for writing this section so clearly. Very easy to understand and I appreciate that.
L 241 – would the value for A0 be zero or is A0 the length the day after hatching? If the later, then please state this.
L 243-246 – Can you indicate why you used different statistical tests for Experiment 1 and Experiment 2?
L 248-252 – Does the probit analysis provide the estimate of the LC50? If so, could you explain that further here as it wasn’t evident to me. If not, the LC50 analysis needs to be included in the Methods section.
L251-252 – Perhaps state this sentence first before explaining the analysis for data from Experiment 2.
L 254-256 – I think this is the information I was seeking in point above L 243-246. Can you somehow move the text in L 254-256 up to address that point?
L 261-264 – The text is not clear here. Perhaps better to have 1 or 2 sentence to present the results from leaves. Then 1 or 2 sentences to present the results from larvae. The last two sentences from adults is clear.
L 273 – Please change “Average” to “Mean”. Also remove the words “like mortality” in this sentence.
L 277-281 – I think this paragraph should be revised in a couple of ways. First, you didn’t test if the growth was exponential, you assumed it was and used an exponential model to estimate the growth rate. So, your first sentence should be revised (or deleted) with that in mind. Delete “during that time”. See comments below for L 313-315 for comments about the analysis and presentation of results.
L 302 – 305 – these results come out of the blue and I wonder what they mean for your analysis. Is this something that should be indicated in the methods and then you explain how you deal with it in regards to your analysis?
L 313-315 – I am having a hard time understanding your growth rate analysis. First, it would be more appropriate to present the estimate and 95% confidence intervals of the growth rate for each dose level rather than the estimate and SD current in Table 1. Given that the relationship is significant (F statistic on L 312-313) it should be obvious which dose level(s) do not overlap the estimate and SE of the control. Also, how does a “relatively low growth rate in the control group” mean for your ability to determine which exposure level significantly depresses growth rates? Second, I wonder if a generalized linear model might be more appropriate for this analysis using Dose as a continuous predictor variable. These same comments apply to comments made above in L 277-281.
L 317-322 – I recommend this paragraph be moved to the Methods section.
L 325 – write out “from leaves to larvae to adults”.
L 324 – 334 – I think the results on lines 327-334 are important to present so I recommend you move the first two sentences to the Methods section and then expand what these ratios indicate (it is too limited here to fully appreciate what these larval body burdens mean) and how you conduct this analysis – an important aspect to address in the Methods is how the response values (larva:leaf ratio) are not independent from the predictor values (leave values). In the results, please present the statistical results from the model presented in Figure 7.
L 343 – Experiment 1 also followed recommended dosages on the label so might be worth noting that recommended dosage of pesticides are unlikely to have an effect on growth, survival, mass, etc.
L 347 – suggest removing μg/kg so all units are consistent among these comparisons.
L 391 – the effect was not evident because you did not find a significant relationship. Please revise this sentence.
L 409 – please write out what is in the parentheses so that those without a background in pesticide applications (like me) can understand.
Figure 1 – please indicate what MDL stands for. Could probably exclude the 3 levels that had no data from this figure and indicate in the text that there was no detections from those doses. In the figure legend the sentence that presents the Chi-square, df and p-values is not clear and might be better if you state the results for leaves in one sentence and the results for larvae in another sentence – also present the results for leaves first since that is how the figure is laid out.
Figure 2 – I think if you only used data until day 9 (or 10) to estimate the growth rate (k) then you should exclude the lines beyond those days. Also, lines with different colours and a legend would help with interpretation here, or else use different shades of grey, or different line types (dashes, dots, etc.).
Figure 4 – please write out the x-axis what “ww” stands for.
Figure 6 – Similar comments as to presentation in Figure 2. Also, it would be good if the presentation/explanation of C and Ls were written in a consistent manner between Figure 2 and 6 to help readers interpret these data.
Figure 7 – Please add the 95% confidence interval around the line on this figure. Also, the caption is rather short. Since the points come from across a range of doses, it would be nice if the point color varied on a grey scale based on their dosage.
Table 1 – Please change “Average” to “Mean” throughout. In footnote 1 your left side of equation should At and “Exposure Study” should be changed to “Experiment” for consistence. In footnote 4 please revise the df which is indicated in two spots but without equal signs so I don’t know what it means.


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: UPTAKE AND TOXICITY OF CLOTHIANIDIN TO MONARCH BUTTERFLIES FROM MILKWEED CONSUMPTION
Review round: 2
Reviewer: 1

Output:
Basic reporting: Basic reporting.  Adequate. With some minor points:
1.	Line 87:  While systemic exposure of milkweed can result in internal neonic concentrations that become a dietary source of exposure, not aware label insecticide label claims that efficacy against insects is also made through contact exposure.  A citation to support this route of exposure and/or a study showing systemic exposure results in external residues of neonic recommended.
2.	In the results include the average milkweed ng/g with, or instead of, using Dose 1, Dose 2 etc.  Easier for the reader to synthesize information by ng/g rather than Dose 1 etc. since the concentrations are very  different across the 3 experiments.
Experimental design: Experimental design.  The paper includes Experiments 1 and 2 that were described in the original submission with the addition of a third experiment that uses a higher exposure range.  As noted by the authors, the first two experiments were confounded because of stress on the swamp milkweed, due at least in part to an aphid infestation.  In the third experiment plants were maintained ‘aphid free.’
Line 118 – provide source of seeds
Line 138 – provide vendor name and location
Line 162 - how was the transfer accomplished?  Same technique as described in experiment 2?

Line 171 – per plant or per replicate; i.e., after transferring larvae from the plant that had the attached cup with the eggs.
Line 223 - where were the larvae placed on the plants.  assume larvae were placed on all 3 plants in a replicate.  In Experiment 1 states btwn 1 and 8 larvae per plant.  what was the range in larvae per plant for experiment 2?

Line 238 – clothianidin free, not pesticide free
Validity of the findings: Validity of Findings.  The mortality and growth data is difficult to reconcile across the experiments.  Experiment 2 is clearly difficult to interpret with the aphid infestation.  Results from experiment 3 suggest the larvae were 4 -5 times more sensitive than larvae in Experiment 1 and Experiment 2, which is counter intuitive since plants in experiment 3 were, presumably, not stressed.  In addition, mortality data from experiment 3 does not reflect a strong dose-response relationship – from 54 to 1007 ng/g, mortality was roughly 50% and was 100% at 1545 ng/g.  Not surprisingly, the fit to the dose response curve must have been poor given the 95% CI interval ranged from about 10 to 450 ng/g.  Perhaps an ANOVA analysis of mortality with post-hoc multiple comparisons would be more insightful?  Are the mortality responses not significantly different across the 54 to 1007 ng/g groups but different than the response associated with the 1545 ng/g exposure? Unfortunately results from experiment 1, which might be able to inform mortality responses between control and 54 ng/g in experiment 3, do not seem to help in that in experiment 1 there was no larval mortality at a dose of 53.9 ng/g.

The residue data from soil, to plant tissue, to larvae to adults is the strength of the paper and provides some useful insights for researchers and risk assessors to consider when evaluating studies that use different exposure matrices.

Line 478 – The formulated product was selected to facilitate the means of treating the soil over a wide range of concentrations; i.e, the study was not undertaken to assess this specific formulation.  Suggest this sentence be dropped.  The text in line 485 is good.

Line 550 – This summary is misleading in that it implies a more precise summary of the toxicity studies than can be supported when looking at across and within experiment variability. It would be more appropriate to state that toxicity values were variable but generally well above high end clothianidin foliage concentrations of X to Y reported to date.

Some additional minor notes:

Table 3 – Define NA mean
Table 3, Experiment 2, leaf concentrations – include meaning of a, b, c footnotes
Table 3, Experiment 3.  Could a post-hoc analysis; e.g., dunns-test, be used to determine if dose groups 4&5 different than 3, which may be different than 1&2?
Additional comments: As noted above the strength of the paper is the residue data and linking relationships of the residue data from soil, to leaves to larvae and adults.  The paper’s toxicology data is very difficult to interpret and it is difficult to place high confidence in the results from a quantitative perspective.  It would be reasonable use the toxicity data in a qualitative manner to conclude that it is unlikely currently reported clothianidin residue levels in plants sampled near agriculture fields are high enough to cause significant effects on survival or growth of monarch larvae and pupa.


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: EXPANDING THE UTILITY OF THE DEXTRAN SULFATE SODIUM (DSS) MOUSE MODEL TO INDUCE A CLINICALLY RELEVANT LOSS OF INTESTINAL BARRIER FUNCTION
Review round: 1
Reviewer: 1

Output:
Basic reporting: This manuscript reports on a topic that has been extensively investigated  over the years.
Experimental design: The experimental design   is flawed by the fact that on day 14 only two animals were available for assessing intestinal permeability
Validity of the findings: All data provided.
Additional comments: Limit of the study not described clearly


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: EXPANDING THE UTILITY OF THE DEXTRAN SULFATE SODIUM (DSS) MOUSE MODEL TO INDUCE A CLINICALLY RELEVANT LOSS OF INTESTINAL BARRIER FUNCTION
Review round: 1
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: On this manuscript, the authors reported that at the experimental colitis model, four-day DSS administration represents the best option by comparing to conventional method that administrate DSS for seven days. They also have highlighted that the four-day protocol mimic better the IBD patients. Therefore, this protocol will be more indicated to investigate possible treatments aiming to restore or improve barrier function in colitis patients

Please to replace “sacrificed” to the scientific term more suitable such as                       “euthanized”
 It will be interesting the authors highlight some aspects involving DSS administration and the short chain fatty acid production. An important aspect to evaluate the intestinal barrier is the microbiota analysis. Probably the concentration of these acids could explain the attenuated injury on intestinal epithelium after 04 days of DSS administration in regarding to others investigated times.
Line  169-  The authors should to replace the term “intestinal barrier function” by only intestinal permeability, once the intestinal barrier involves others aspects that  were not investigated in this manuscript.
Validity of the findings: Figure 2- Intestinal Permeability
It isn’t clear the relation between the asterisk number (*, **, ****) and the statistical difference level (p=0,005, p<0,0001). In this sense, it would be interesting the authors to clarify better in the Figure 2. For example in the lines 179-180 the authors described  “the seven-days DSS group showed  the most intense increase in permeability, increasing 35-fold compared to the control” However, in the Figure 2 this results is represented only by one asterisk (p= 0,005), while the six and five days groups were represented by **** p <0,0001.

Conclusion
Although, the four-day DSS protocol has showed similar results of intestinal permeability that could correspond to IBD patients, the outcomes obtained in this manuscript are not enough to suggest this protocol as model to investigate possible treatments to colitis. The literature data have shown that others parameters such as tight junctions proteins, collagen deposition, cytokines, mucus and immunoglobulins production are necessary to understand the complex mechanisms involved in the intestinal barrier. Therefore, the authors should improve the conclusion focusing only the data obtained.
Additional comments: Although, the four-day DSS protocol has showed similar results of intestinal permeability that could correspond to IBD patients, the outcomes obtained in this manuscript are not enough to suggest this protocol as model to investigate possible treatments to colitis. In this sense, others parameters such as immunologic response, citokines and tight junctions proteins should be investigated to support the conclusion due to complexity of intestinal barrier function.


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: EXPANDING THE UTILITY OF THE DEXTRAN SULFATE SODIUM (DSS) MOUSE MODEL TO INDUCE A CLINICALLY RELEVANT LOSS OF INTESTINAL BARRIER FUNCTION
Review round: 1
Reviewer: 3

Output:
Basic reporting: The dextran sulfate sodium (DSS) mouse model of colitis was used to study inflammatory bowel diseases (IBD), which affects more than one million people in the United States. Kyle Cochran et al. optimized the duration of DDS administration to mice to obtain an attenuated DSS colitis model that mimics the conditions of the IBD patients better than any existing DDS mouse model.

The structure of the manuscript conforms to the PeerJ standard. The manuscript is well-written with the proper context of the research questions supported by relevant literature. The figures are of high quality, well-labeled, and described. The raw data were provided.
Experimental design: The research questions are well-defined and appropriate. The methods contain sufficient details to replicate the results.
Validity of the findings: After a systematic investigation, the authors successfully established that the reduced duration of DDS administration to mice better emulate the physiological conditions of IBD patients. The conclusions are well described, related to the original research questions, supported by the results.
Additional comments: Please provide the ethical approval statement for vertebrate animal usage.


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: EXPANDING THE UTILITY OF THE DEXTRAN SULFATE SODIUM (DSS) MOUSE MODEL TO INDUCE A CLINICALLY RELEVANT LOSS OF INTESTINAL BARRIER FUNCTION
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: The explanation regarding to Figure 2 was enough to clarify the data obtained related to intestinal permeability
Validity of the findings: In the Discussion (lines 318-324) the authors highlighted other aspects related to complexity of intestinal barrier function as mentioned by this reviewer
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: EXPANDING THE UTILITY OF THE DEXTRAN SULFATE SODIUM (DSS) MOUSE MODEL TO INDUCE A CLINICALLY RELEVANT LOSS OF INTESTINAL BARRIER FUNCTION
Review round: 2
Reviewer: 2

Output:
Basic reporting: The authors stated in the Methods section that all the studies were performed following local, institutional, and federal guidelines for vertebrate research.
Experimental design: No comment
Validity of the findings: No comment
Additional comments: No additional comments


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

Input:
Title: POSTCRANIAL ANATOMY AND HISTOLOGY OF SEYMOURIA, AND THE TERRESTRIALITY OF SEYMOURIAMORPHS
Review round: 1
Reviewer: 1

Output:
Basic reporting: Dear Editor of PeerJ,
Dear Authors,

I have reviewed the manuscript entitled Postcranial anatomy and histology of Seymouria, and the terrestriality of seymouriamorphs by Kayla D Bazzana, Bryan M Gee, Joseph J Bevitt and Robert R Reisz.

It is a very interesting study about histology and morphology of Seymouria and implications for the interpretation of the mode of life and it was a pleasure to be able to review this paper. Authors based on the long bones morphology and thin sections proofed that Seymouria was a terrestrial animals. The most important part of this study is the histological description; they are the first known thin sections from long bones from this taxon and even wider, from seymouriamorphs. The only second known histologically seymouriamorphs is Discosauriscus from Europe. Moreover based on the histological sections authors concluded about ontogenetic stage/age of tested bones.
Although the issue is really interesting and deserves to be published in a high ranked journal as PeerJ, I found some problems that must be assessed before final acceptation of the paper. Some of them I have marked directly on the manuscript, general comments you can find below.

Authors used professional English language throughout. My only concern is about saying ecology of Seymouria. I think that ecology it is a more complex term and you are trying the discover/proof mode of life. Of course mode of life (adaptation to environment) is a part of ecology, but I won’t use this as a basic form. To describe ecology you should analyze much more factors.
Authors cited all important papers which are published about this topic. Only small error occurred in MS with the year. Konietzko-Meier and Sander it is 2013 (not 2012).
The structure is mostly clear and conforms to PeerJ standards and discipline norm. The only point is a construction of results. I prefer a separation between results and discussion. In your morphological description you use a lot of external sources. It is acceptable if you are doing a taxonomical paper and need a direct “morphological comparison” with other taxa (taxon A has this processus small, and taxon B has it long, etc). Thus I can understand the mixing of results and discussion in your morphological report. However, still some of your sentences are clear interpretations, and should be in discussion (see pdf).
 I would propose to extract histology as a separate part. Also you should add more details about histology. It is a first published description about bone histology of Seymouria and I think it is a good opportunity to provide as detailed as possible description (tissue type, other growth markers, osteocytes, vascularization type, etc.). Especially, if histology is a crucial factor for your conclusions about mode of life and metamorphosis. Moreover, you should add more information about microanatomy, as this is a correct tool to discuss mode of life.
Figures need some improvement. You need more labeling to make all characters described in MS also to be visible on figures. Also in Fig, 4 something happened with the letters, you have no D. For all figures – there is no explanations of used abbreviations.
Experimental design: It is an original primary research within Scope of the journal. Goals are well defined. Methods described with sufficient detail. Beside the morphological description and classical destructive thin sections authors also used modern technologies to access microstructural information – it is an important point, as histology itself is usually a destructive method. Thus all alternatively methods which are safe for fossils are very welcome. The lacking information is about construction of the phylogeny presented on the end of discussion. Authors should add details about this to methods part.
Validity of the findings: For sure it is a very important paper and should be published after improved.
Additional comments: My most important concern is the conclusion about postmetamorphic stage of sampled animals. I agree that this material looks adult-like. But do we know how should look a premetamorphic histology and morphology? I think that it will be useful to add a chapter where you can discuss which characters, morphological and histological, tell us about ontogenetic stage. First, based on literature, then compare data from literature with your material. Only one sentence: “In contrast, the individuals of Seymouria that were analyzed here are regarded as being definitively postmetamorphic in spite of at least one (ROMVP 81200) being distinctly younger than the onset of metamorphosis in Discosauriscus (Sanchez et al., 2008).” is not enough to proof your point. You need provide arguments, both morphological and histological. Now it is difficult to follow your point for researches not familiar with seymouriomorph.
Similar comment about your conclusion about terrestrial mode of life. You need a list of arguments pro and contra, based on literature and your material.

For other comments see pdf.
If you have any further questions please feel free to contact me.
Best regards
Dorota Konietzko-Meier


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: POSTCRANIAL ANATOMY AND HISTOLOGY OF SEYMOURIA, AND THE TERRESTRIALITY OF SEYMOURIAMORPHS
Review round: 1
Reviewer: 2

Output:
Basic reporting: 'no comment'
Experimental design: 'no comment'
Validity of the findings: 'no comment'
Additional comments: Manuscript “Postcranial anatomy and histology of Seymouria, and the terrestriality of seymouriamorphs” by Kayla D. Bazzana et al. describes the postcranium of the seymouriamorph stem-amniote Seymouria based on outer morphology, bone histology and neutron computed tomography. The postcranium of this early tetrapod has been neglected in comparison to its cranial anatomy, the only comprehensive description of postcranial elements dating back to the first half of the 20th century (White 1939), a description which is very detailed, but which does not meet modern standards anymore. Thus, the description of the postcranium based on new material with new characters is highly welcome. Furthermore, the present manuscript provides data on bone histology and microstructure of limb bones and vertebrae for the first time in Seymouria; these data are essential to assess the mode of life of a fossil tetrapod. The morphological and histological description of this work is always detailed and thorough, and I appreciate the clear and informative illustrations. I also appreciate the documentation of the ontogeny of long bones (humerus and femur), and to my knowledge, this has so far not been described in the literature. The conclusions of the authors are sound and comprehensive, and I agree with most of them. The authors have nicely shown that the larval period must have been rather short in Seymouria in comparison with its relatives (the discosauriscid seymouriamorphs), which had an extended larval period. The greatest surprise for me was to see that the long bones of Seymouria have a modestly developed medullary spongiosa, normally a feature of more aquatic or semi-terrestrial tetrapods. Thus, I suggest that the authors should rethink the hypothesis that Seymouria was strictly terrestrial.
I have some specific suggestions that are listed below. The manuscript is an important step in our understanding of seymouriamorph paleobiology (and thus of stem-amniotes in general), and I fully support its publication in PeerJ.

General remark: I did not find a list of the anatomical abbreviations that are used in the figures.

Specific comments for the authors

Line 38: “Seymouriamorphs are among the best-known stem amniotes…” Although most authors (and I) agree that seymouriamorphs nest on the amniote stem, there is still a different phylogenetic hypothesis (Marjanović & Laurin 2019), stating that seymouriamorphs are stem-tetrapods and might even be paraphyletic (Reference: Marjanović D, Laurin M. 2019. Phylogeny of Paleozoic limbed vertebrates reassessed through revision and expansion of the largest published relevant data matrix. PeerJ 6:e5565 DOI 10.7717/peerj.5565). This unorthodox view should be cited.

Lines 40-44: you should also cite White 1939 here

Lines 121-123: Why do you use Linnean categories like order and family in the Systematic Paleontology section? I would delete them.

Lines 136-143: Description of vertebrae. How do you know or infer the position of vertebrae, even when the column is not complete? Please explain.

Lines 144-145: You cite White 1939 because of the characteristic swollen zygapophyses; I would also cite Holmes 1989 (already cited in the manuscript elsewhere) here that deals with seymouriamorph vertebral morphology and functional aspects

Line 175: supraneural canal: is this a true canal or only an anterior and posterior depression?

Line 176: “A pair of closely spaced, distinctive growth lines can be identified…” Please label in Figure 4A

Line 251: “…cortex is relatively compact…” and well vascularized

Line 252: “less organized”: do you mean woven?

Lines 295-296: you should cite also Holmes 1989 here, and you may mention that also Kotlassia has pre- and postzygapophyses that face dorsally and ventrally, respectively (Bystrow 1944)

Lines 305-329: In this section, you compare the morphology of humerus and femur of Seymouria with those of different discosauriscids. For example, you write that the humerus of Seymouria is more extensively ossified than those of Utegenia or Ariekanerpeton; you state that the lack of ossification may represent ontogenetic immaturity, and I think that is true. We do not know the humeral or femoral morphology in a “true adult” discosauriscid, and therefore such a 1:1 comparison is a bit problematic. You should emphasize this more in the text. Likewise, the lack of a supinator process (line 319) might be an ontogenetic character. The lesser degree of twisting of the humeri of Discosauriscus and Ariekanerpeton (lines 321-323) could also be explained by taphonomy (compaction of the poorly ossified limb)

Line 355: For interpretation of the ecology (aquatic versus terrestrial) you cite Moodie 1908; you should also cite one or more more recent publications. For example, see discussion of this topic in Schoch (2002) and Witzmann (2016) (References: Schoch, R. R. (2002). The evolution of metamorphosis in temnospondyls. Lethaia, 35(4), 309-327; Witzmann, F. (2016). CO 2‐metabolism in early tetrapods revisited: inferences from osteological correlates of gills, skin and lung ventilation in the fossil record. Lethaia, 49(4), 492-506.)

Lines 360-361: Lateral line sulci are indeed absent in Seymouria, however, the absence of the sulci are not definitive proof that Seymouria did not possess a lateral line system. You should argue more cautiously here. The neuromasts could have simply been located more superficially in the (thicker) skin, so that no imprints were made on the bones (e.g. as in lissamphibians, which lack any imprints, but many retain lateral lines). So the presence of grooves are a proof for the presence of the lateral line system, but the absence of sulci is not necessarily a proof for the absence of the lateral line system.

Line 375: “Previous authors have inferred that Discosauriscus underwent metamorphosis” Discosauriscids (or some of them) might have been paedomorphic, but it can be assumed that they were derived from metamorphosing ancestors with terrestrial adults (see e.g. Boy and Sues 2000). Reference: Boy, J. A., and H.-D. Sues. 2000. Branchiosaurs: larvae, metamorphosis and heterochrony in temnospondyls and seymouriamorphs; pp. 1150–1197 in H. Heatwole and R. L. Carroll (eds.), Amphibian Biology, Volume 4: Palaeontology. Surrey Beatty and Sons, Chipping Norton, New South Wales, Australia.

Lines 381-382: “In contrast, the individuals of Seymouria that were analyzed here are regarded as being definitively postmetamorphic in spite of at least one…being distinctly younger…” This is a very interesting observation, please justify why you think they are postmetamorphic.

Line 387: What do you mean with “environmentally stable”? Please be more specific here.

Lines 387-389: “Histological sections also indicate a less developed trabecular network in the medullary cavity of Discosauriscus (Sanchez et al., 2008:fig. 2); the significance of this is unclear in the absence of additional data” This is indeed an interesting contrast to the pattern found in Seymouria. Maybe the less developed trabeculae in Discosauriscus just reflect that the bones are very small. The long bone microstructure in small forms like most lissamphibians is rather simple, with few or no trabeculae, in contrast to larger animals (for example, only cryptobranchids, which are the largest salamanders, possess spongy bone in the tibia). For a discussion see Laurin et al. 2011 and references therein (Reference: Laurin, M., Canoville, A., & Germain, D. (2011). Bone microanatomy and lifestyle: a descriptive approach. Comptes Rendus Palevol, 10(5-6), 381-402.)

Lines 405-406: In my opinion, it is far from certain that Lydekkerina was a terrestrial animal. It has persistent lateral line sulci on the skull roof and Canoville & Chinsamy (2015) – on the basis of bone microstructure – regarded it as “amphibious with a tendency to be more terrestrial” (Reference: Canoville, A., & Chinsamy, A. (2015). Bone Microstructure of the Stereospondyl Lydekkerina Huxleyi Reveals Adaptive Strategies to the Harsh Post Permian‐Extinction Environment. The Anatomical Record, 298(7), 1237-1254.)

Lines 539-541: “…what to make of the persistence of a modestly developed medullary spongiosa in the femur of Seymouria, either compared to Discosauriscus or to other more distantly related terrestrial tetrapod…” As stated above, the rarity of trabeculae in Discosauriscus might be a matter of size of the animal. Concerning the modestly developed medullary spongiosa in Seymouria: maybe this indicates that Seymouria was a bit more aquatic than previously thought? Maybe terrestrial to semi-terrestrial?

Figure 4: “C” on top right of the figure should be D, and the close up picture (E) should be reoriented (rotated through 180°) to be consistent with the overview figure D (“C”)


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: POSTCRANIAL ANATOMY AND HISTOLOGY OF SEYMOURIA, AND THE TERRESTRIALITY OF SEYMOURIAMORPHS
Review round: 2
Reviewer: 1

Output:
Basic reporting: Dear All,

After the second check of submitted article I am happy to see the improvement of the text.
However, I still found some small problems that must be assessed before final acceptation of the paper, comments you can find below, in general comments.
Experimental design: no comments
Validity of the findings: For sure it is a very important paper and should be published after improved.
Additional comments: I think that a little change of the organization of the chapter Material and Methods would make following of the paper easier.
Page 8, line 77:  ROMVP 80915 and ROMVP 8091…
Page 9, line 96: For OMNH 79348,….
The list of the material is in a next chapter, so in this moment readers do not know what the number does mean. Maybe add what kind of bone it is (like you did in histological description).

However, in my opinion it will be good to start with the presentation of the material. No you have:
Page 12, lines 157-167 – long “technical” description of vertebrae. Move this better to the part material and methods. And make from this a first part of the section M and M.
Page 14/ line 203 - ROMVP 80915 is a complete left femur (Fig. 5)-… also to M and M
Page 15/68 – fibula – comment see above
Page 17/267-272 – should be in M and M
Etc.

This way you will have a complete list of material, with all necessary information about kind of bone, state of preservation, etc. Now, reading i.e. a discussion, if you have only a coll. number – it is difficult to follow. You have: Referred specimen, but it is only a list. It will be good to have all information together.

Figure caption – fig. 12. You have gz, growth zone - It is enough to say zone. Zone it is always a growing “layer”.
The same figure – you have resting lines. In text you use rest lines – both are correct, but be consistent.

16/253: In both specimens, the neural arch is much thicker along the posterodorsal surface
behind the neural spine and extending down to the posterior indentation of the supraneural canal when compared to the anterior surface. – what do you mean? Cortex is thicker? Or you mean in morphological sense?
16/258: thickened region of ROMVP 81199 (Fig. 8A)… thickened region of cortex?
19/314: For example, the lesser porosity of the diapophyses of the first sacral vertebra relative to the presacral and possible second sacral suggests that the first sacral undergoes the majority of the stress loading.
 1. references (usually the lower porosity means lower stress level). 2. Moreover, this sentence somehow does not fit here.
23/422-426: Skeletochronological markers also differ between the taxa. Discosauriscus possesses numerous, well-defined and evenly spaced LAGs, whereas Seymouria is characterized by distinctive growth zones and annuli bearing numerous closely spaced rest lines but without clear LAGs. Lastly, the medullary spongiosa is distinctly less developed in Discosauriscus (Sanchez et al., 2008:fig. 2); the significance of this is unclear in the absence of additional data.
You can observe similar situation for Temnospondyli. Metoposaurus shows thick annuli with numerous resting lines, whereas Dutuitosaurus (metoposaurus from Morocco) normal LAGs. For discussion see: Konietzko-Meier and Klein, 2013.
30-31/560-566: This disparity among closely related taxa may reflect the different environments that these taxa inhabited, as Seymouria is primarily found in fluvial environments of North America that probably experienced marked seasonality, and Discosauriscus is primarily found in lacustrine settings in Europe that may have experienced less seasonal disparity. Such seasonality is evident from the clearly defined annuli and growth zones in our sampled specimens (Figs. 11-12), and it seems probable that these environmental conditions would have favored an early onset of metamorphosis in the taxon.
I would say opposite. Distinct LAGs suggest strong seasonality. See Konietzko-Meier and Klein, 2013.

If you have any further questions please feel free to contact me.
Best regards


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: SPORTS EXPERTS’ UNIQUE PERCEPTION OF TIME DURATION BASED ON THE PROCESSING PRINCIPLE OF AN INTEGRATED MODEL OF TIMING
Review round: 1
Reviewer: 1

Output:
Basic reporting: No comment.
Experimental design: No comments.
Validity of the findings: No comment.
Additional comments: This study examined whether sports experts (i.e, divers) show longer duration perceptions when viewing stimuli in relation to their expertise domain compared to experts (i.e., wrestler) with other expertise domain and non-experts. Their findings are in line with the study hypothesis by showing that divers reproduced longer durations for diving figures as compared with the neutral figures, while the other groups showed the opposite patterns. More specifically, they also reported a positive correlation between years of training experience and the magnitude of the pronged reproduction duration in the divers.

In my opinion, the manuscript is concisely written, the figures are adequate, and the topic is of interest to PeerJ. However, there are some minor caveats of this study which are needed to be addressed appropriately.

1.	It may be beneficial if the author could refer to the recently published work (i.e., Scharfen, & Memmert, 2019) to re-consider the “elite” or “expert” definition for their participants.
2.	It is suggested to provide more details about participants’ demographic information that may potentially bias the results of interests such as BMI, physical fitness, the dose of current training.
3.	The authors adopted Bayesian statistics for their data without ever making explicit the a priori Bayes Factor they would consider significant or providing a citation that would explain quite what their analysis involved. Please provide more details regarding the use of Bayesian analysis.
4.	The discussion reads very well and provides new insights into the expertise-difference in duration perception. I only have one remark: the authors are suggested to propose the potential implications of the current finding to field-based applications.


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: SPORTS EXPERTS’ UNIQUE PERCEPTION OF TIME DURATION BASED ON THE PROCESSING PRINCIPLE OF AN INTEGRATED MODEL OF TIMING
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper addressed important topic of time perception and examined rare group of elite athletes that I greatly appreciate. The performed analysis is valid and applied professionally, while the English might be improved at some parts.

My major concerns lays in the group matching. Two important differences between the athlete’s groups were ignored, that needs to be considered. Unfortunately, the athletes’ groups were not matched by gender and, most importantly, years of training. While gender difference between groups is unlikely to affect the interpretation of the results, it needs to be acknowledged and discussed. At the same time, taking into account that wrestler and diving groups are substantially different in the years of training (8.06±2.84 vs 2.94±1.63) the difference in time perception parameters between the groups can be accounted by the general length of training experience, not specific for particular activity (diving or wrestling), as claimed by authors. Indeed, when subjects need to evaluate the duration of picture representing human body (expertise-related stimuli in the current study was a body images) they might involve the body signals that might be important component of time perception (see Wittmann et al., 2013). Years of physical training experience might increase vividness of one’s body representation and lead to longer time perception regardless of the sport you are professional in. In line with this interpretation, the divers time perception results correlated with years of training and those divers who have compatible years of training with wrestlers did not differ from wrestler group (see fig 7). Other evidence to support the “length of training” hypothesis came from AE ratio results from this paper. AE ratio advantage was evident for divers only for general stimuli, but not expertise-related ones, contradicting the initial authors’ hypothesis that a particular expertise leads to changes in time perception, and more consistent with the ideal that, in general, intense physical training leads to changes in time perception irrespective of the field of training (wrestler, diving etc). Such interpretation is also in line with previous research on motor timing (Sysoeva et al., 2013).  While smaller AE ratio (time perception precision) and longer duration reproduction for body images in athletes might be unrelated phenomena they might be different sides of the same processess.

Thus, I believe that this study might provide important message to scientific community if takes into account the pointed above limitations, either by better matching the groups or by changing the focus of analysis and interpretation of the results.
Experimental design: The experimental design is valid, the topic is relevant and relatively well defined. Statistical analysis used appropriately, but the problems with group matching by important parameter, such as years of training make the results ambiguous and difficult to interpret.
Validity of the findings: no more to add to the above provided comments
Additional comments: Some recommendation for abstract improvement:
The background section of the abstract need improvement. In the current form it is hard to understand what the authors meant by “integrated timing model” and its prediction.
I’d also like to have the exact duration of stimuli stated in the method section.
As I stated before, the years of training is clearly different between compared athletes group that suggest different interpretation of the results, so this should be also reflected in abstract.


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: SPORTS EXPERTS’ UNIQUE PERCEPTION OF TIME DURATION BASED ON THE PROCESSING PRINCIPLE OF AN INTEGRATED MODEL OF TIMING
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: Based on my previous comments on the manuscript followed by authors' replies and incorporated changes in the latest version of the manuscript, I am fully convinced with these changes/replies. Thanks for the authors' effort. I would recommend publishing this manuscript in its current form.


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

Input:
Title: SPORTS EXPERTS’ UNIQUE PERCEPTION OF TIME DURATION BASED ON THE PROCESSING PRINCIPLE OF AN INTEGRATED MODEL OF TIMING
Review round: 2
Reviewer: 2

Output:
Basic reporting: no comments
Experimental design: I believe there is a mistake in the description of the statistical analysis of additional ANOVA analysis that aimed to examine if the gender differrence between the group influence the observed group diffference in duration reproduction parameters. " Additionally, to evaluate the effect of gender difference on our results, we ran repeated-measures ANOVAs of RD, RDD, bias, CV, and AE ratio results for divers (15 female) and non-athletes (13 female) with both group and gender as the between-subjects factors, time range as the within-subjects factor, and age as the covariate." Author implemented valid approach and decided to examine if the results hold when only females of both groups is considered. However, at the same time they stated that they heve "gender" as between-group factor. How can you have gender as a factor if you have sample of only females? You can examine here the group effect and if it holds here similar as with a full-sample, this is an indicator that gender difference is unlikely to influence the results.
Validity of the findings: no comments
Additional comments: I belive authors undretake signifcant amount of work to examine alternative explanations of their findings  that was raised by not optimal group matching. Generally, I satisfied with the current version of the ms, and reccomend it for the 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: EFFECTS OF MUCUS TRAIL FOLLOWING ON THE DISTANCE BETWEEN INDIVIDUALS OF OPPOSITE SEX AND ITS INFLUENCE ON THE EVOLUTION OF THE TRAIT IN THE EZO ABALONE HALIOTIS DISCUS HANNAI
Review round: 1
Reviewer: 1

Output:
Basic reporting: The use of the English language will still require considerable attention. There are quite some odd wordings and use of grammar.
Some supplemental data were lacking. I recommend Table 1 is expressed in graphical form for easier assessment.
Other specific comments are included in the attached file.
Experimental design: “Materials & Methods” section is highly difficult to follow and needs rephrasing. Specific comments are included in the attached file.
Validity of the findings: The author should also consider whether abalone follow mucus or not depends on environmental factors. Specific comments are included in the attached file.
Additional comments: This is an interesting paper dealing with evolutionary benefits of mucus trail following in abalone species using observation of tank experiments, individual-based models, and population genetic models. While I am briefly familiar with the behavioral ecology of abalone species, I am not an expert in genetic models and cannot adequately comment on the technical aspects of data analysis. However this paper would be a contribution on the behavioral and reproductive ecology of important abalone species.


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

Input:
Title: EFFECTS OF MUCUS TRAIL FOLLOWING ON THE DISTANCE BETWEEN INDIVIDUALS OF OPPOSITE SEX AND ITS INFLUENCE ON THE EVOLUTION OF THE TRAIT IN THE EZO ABALONE HALIOTIS DISCUS HANNAI
Review round: 1
Reviewer: 2

Output:
Basic reporting: A bit disjointed and unclear. The findings are interesting, but not well presented. At least one of the references is a bit misleading, as mentioned in general comments. Seems to be a few bits of evidence thrown in randomly without really explaining their relevance or significance.
Experimental design: It is not explained why a model is used rather than the real animal assay conducted in the trail-following experiment, and there is inconsistent use of terminology. Ie. Encounters or distance between?
Validity of the findings: I am not qualified to comment on the validity or reliability of the model-based experiment.
Additional comments: Line 33 – was this a significant difference?
40 – externally fertilized
43 – opposite sexes
53 – through olfaction
55 – the opposite sex
57 – following mucus trails
60 – with the opposite sex
61 – Are they testing distance between or encounter rate? Those two things don’t seem to be the same to me…
64 – this is not worded very clearly
71 – and in the field
73 – this doesn’t make much sense to me
77 – conditions
79- Why is Fig. S1 not in the results section, or was it performed in a previous study?
82 – In this ONE study, it only implies this, and only in relation to food. A big reach to make this statement I think.
86 – Should stipulate that this was using a model, to differentiate between the previous investigation using live animals
94 – These species?
111- starting point – what kind of camera?
128 – this is not clear, needs rewording
139 – Not S4, think it should be Data S2
143 – Can’t see how this relates to what I think is Figure 1
185 – this is confusing – no Supplemental Data S3 received in files
187 – Results (the?)
194 – Would be good to have absolute numbers here. Ie how many followed trail?
223 – Grammatically incorrect, needs rewording
237 – Opposite sex members of wild males? – doesn’t make sense
270 – trail
283 – not the only evolutionary driving force
284 – was not 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: EFFECTS OF MUCUS TRAIL FOLLOWING ON THE DISTANCE BETWEEN INDIVIDUALS OF OPPOSITE SEX AND ITS INFLUENCE ON THE EVOLUTION OF THE TRAIT IN THE EZO ABALONE HALIOTIS DISCUS HANNAI
Review round: 1
Reviewer: 3

Output:
Basic reporting: The manuscript “The effects of trail following on the distance between opposite sex and the effect of its benefit on the evolution of trail following in Pacific abalone Haliotis discus hannai” tries to determine the importance of mucus trail following behaviour as an adaptive trait. This is a very complex eco-evolutionary issue of broad biological relevance.

The English should be improved, the ideas are not clear and in some paragraphs there are several contradictions. This makes it hard to access the manuscript. For example, in lines  63-65, 72-73, 77-79, 255-261 the current phrasing makes it very difficult to follow the ideas. I recommend that the author have a native English speaker review the text.

Although it is difficult to follow, the background is sound enough to have an idea of the main question. The structure of the manuscript follows a traditional format. However, the subdivisions of the methods make it difficult to read and the subtitles are extremely wordy without providing relevant information, especially the part describing the models (Lines 133-159).

I think the results are enough to test the hypothesis proposed, but the evolutionary model has several problems (see below). The figure in the main text could be the most important result, but some modifications to the model should be done (see my comment below). The table could be in the supplementary material, substituted for a figure showing the same results.
Experimental design: The author used mainly the correct statistical and experimental approaches. These allowed to them to establish the prevalence of trail following behaviour in the species (although this has been reported in several species of molluscs) and that this behaviour reduces the distance between individual of the same species. However, these methods were not enough to determine the evolutionary consequences of this behaviour, which would be the most broadly relevant result in the manuscript.

It is very weird that the two models (trail following and drift) show very similar results. More specifically, the high number of simulations where the allele D got lost in both models is huge; this, and the fact that both models reach a maximum of 90% frequency of the D allele around the same number of generations, makes me believe something is wrong with the simulations. I can understand how the advantage of Dd in the trail following model prevents a fixation of D, but why does this fixation never occur in the neutral model? Perhaps another problem is the simulated density; most species of abalone are distributed in patches with natural densities over one individual per m2 (Goodsell et al 2006). As the author pointed out, the density is more relevant for evolutionary processes than a population census size without geographic context. This is especially true in species with low mobility such are the abalone. I suggest including models with slightly higher abalone densities to better represent the wild populations.
Validity of the findings: As I mentioned before, I think the results are well supported, except for the evolutionary consequence of trail following behaviour. I personally found the discussion very limited, underexploring the results. For example, I suggest more discussion about the possible problems in the evolutionary model.
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: EFFECTS OF MUCUS TRAIL FOLLOWING ON THE DISTANCE BETWEEN INDIVIDUALS OF OPPOSITE SEX AND ITS INFLUENCE ON THE EVOLUTION OF THE TRAIT IN THE EZO ABALONE HALIOTIS DISCUS HANNAI
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: The paper has been improved since the prior submission. Please see my minor comments as below.

Line 29: “arm” -> “y-maze arm”

Line 47: “higher rates of fertilization rate” -> “higher rates of fertilization?”

Lines 97-98: The author should show how to observe the sex of non-reproductive individuals.

Lines 105-106 and 109-110: I notice that follower abalone were placed on mucus-attached substrates at the beginning of trials, so the author examined the trait of abalone avoiding mucus, rather than that of abalone attracted to mucus? I think that the author should examine whether abalone are attracted to mucus and they follow it, and this point should be discussed.

Lines 154-155: Supplemental dada S2: Perhaps the measuring moving distance was conducted under a lower temperature than the Y-maze experiments?

Lines 199-200: “The combination of marker and follower combinations” -> “The marker and follower combinations?”

Line 312: “species”; not italic.


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

Input:
Title: EFFECTS OF MUCUS TRAIL FOLLOWING ON THE DISTANCE BETWEEN INDIVIDUALS OF OPPOSITE SEX AND ITS INFLUENCE ON THE EVOLUTION OF THE TRAIT IN THE EZO ABALONE HALIOTIS DISCUS HANNAI
Review round: 2
Reviewer: 2

Output:
Basic reporting: The authors improve the manuscript in this second round, however I still have difficulties to follow the ideas. Some paragraphs are repetitive (e.g. Lines 146-147 and Lines 153-155), and some ideas are not clear (e.g Lines 57-70).

In terms of format, I think the authors did not change enough. I think the methods are subdivided too much, with the subtitles still extremely wordy without providing
relevant information. The simulation model is intrinsically complex, and this style of writing  makes it more difficult for the reader to understand.

The previous version has enough results to test the hypothesis proposed, but this version has removed the neutral evolutionary model. These simulations are important to distinguish between a random effect and a selection effect on the allele frequency due to mucus  following behaviour.
Experimental design: The statistical and experimental approaches are mainly correct. The methods are related to the questions but there are still problems with the simulation model. The authors removed the neutral model (random), which is fundamental to establish the evolutionary effect of the trail following behaviour.
Validity of the findings: The results are clear about the prevalence of trail following behaviour and its effect on the distance between individuals. However, the evolutionary consequences of this behaviour are still unclear. The authors modified the model as requested. But still, there is not clear evidence for the effect of this behaviour on the reproductive success of the species. I think this is related with the bad writing style of the manuscript but also the removal of the neutral model results.
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: AMENDMENTS TO SALINE-SODIC SOILS SHOWED LONG-TERM EFFECTS ON IMPROVING GROWTH AND YIELD OF RICE (ORYZA SATIVA L.)
Review round: 1
Reviewer: 1

Output:
Basic reporting: .
Experimental design: .
Validity of the findings: .
Additional comments: REVIEW (PeerJ Manuscript, 38932)

GENERAL COMMENTS:

This manuscript reports results from a study conducted in China to determine which
amendment treatment, among four tested, gave the best results in improving rice growth and
yield in a saline-sodic soil. The study is relevant because of the increasing need to expand food
production onto soils, like saline-sodic soils, that traditionally have been very unproductive. The
four treatments were compared against an untreated control and with each other by collecting
data on the osmotic potential in soil solution, the selective absorption (SA), selective transport
(ST), the distribution of K+ and Na+ and yield components in rice plants. The best results were
obtained when a combination of manure, sand, and gypsum was used as a soil amendment.

The study seems to have been conducted appropriately and the results will be of interest to
readers wanting information on the best way to treat saline-sodic soils to improve crop yields.
The writing, however, needs to be carefully reviewed and the entire manuscript needs editing.
Obviously, some of the problems are due to English probably not being the first language of the
authors.

I have written extensive edits directly on the hard copy pages of the manuscript. I have scanned
these edited pages into a .pdf file and returned this file with my review. I hope the authors find
these edits useful when revising their manuscript. Below, I make some specific comments about
things in the manuscript that I think need to also be addressed to improve the overall quality of
the manuscript.

SPECIFIC COMMENTS:

1. Title. The title can be shortened. The suggested shortened title still is informative and useful
to describe the paper.

2. Line 77-85. It is not clear whether the treatments were only applied once in 2017 and then
the soil and crop responses measured annually afterwards. Alternatively, were the same plots
treated every year with the same treatment. For example, was the gypsum plot treated every
year so that there were nine total applications of gypsum to the plots for this treatment before
sampling was done in 2017?

3. Since this study seems to have data on rice yields for the entire time of 2009 to 2017, I think
it is important to inform the reader as to the yield trends observed. For example, was the best
treatment in 2009 different compared to the best treatment in 2017? Were soil properties
quickly improved or did they improve slowly with treatment.

4. Line 98. When were the soils sampled? Were they sampled only in 2017 at planting? After
harvest?

5. Line 128 uses the term “concentration” and that is the correct term. But then many times
afterwards the term “content” is used. That is incorrect.

6. Lines 133-134. This sentence is not supported by the data. The differences in mean root Na+
concentrations were actually greater than the concentrations in shoots.

7. Lines 140-155. The writing in this section was not very clear. Please review and make
appropriate edits.

8. Line 174. Please report all data to only three significant digits. I very much doubt your
experiment was so precise as to report yields using six significant digits. For example, it is not
appropriate to report rice yield as being 8924.87 kg/hm2. Also, I believe the appropriate
abbreviation for hectare is “ha” and not “hm2”.

9. Lines 192-194. This sentence is not clear to me.

10. Lines 207-209. What is the meaning of “redundant Na+”? This sentence is not clear to me.

11. Line 212. What is the meaning of “bypass flow of rice”?

12. Line 232. Is it really true that increased Na+ uptake increased plant growth?

13. Font size should be increased in Figures 2 and 4. With computers, this is easy to do and
makes the figures easier to read.

14. Tables 1 and 2 need footnotes defining the treatments in the same way the treatments are
defined in the figures.

15. Table 2. Please restrict reporting of data to three significant digits. I don’t think it is possible,
in an experiment like this, to measure a difference of 0.01 kg/hm2 in rice yield. There are too
many sources of variation that are involved in this experiment to be so precise.


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: AMENDMENTS TO SALINE-SODIC SOILS SHOWED LONG-TERM EFFECTS ON IMPROVING GROWTH AND YIELD OF RICE (ORYZA SATIVA L.)
Review round: 1
Reviewer: 2

Output:
Basic reporting: In the present study, the long-term effects of different amendments application in saline-sodic soils on improving growth and yield of rice were  analyzed. It is interesting and can provide a theoretical basis for the reuse of solid waste and reclamation of saline-sodic soils. I think that this paper is within the scope of the journal, but for the reason I detailed in the general comments I recommend to make a major revision before acceptance.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: 1. Your introduction needs more detail. The relevant review on reclamation of saline-sodic soils using desulfurization gypsum is not comprehensive, and the following references can help to improve this issue.
Potential flue gas desulfurization gypsum utilization in agriculture: A comprehensive review. Renewable and Sustainable Energy Reviews, 2018, 82:1969-1978.
Sodic soil properties and sunflower growth as affected by byproducts of flue gas desulfurization. Plos One,2012,  7（12）: e52437.
 Effect of byproducts of flue gas desulfurization on the soluble salts composition and chemical properties of sodic soils. Plos One, 2013,  8（8）: e71011.
2.The English language should be improved to ensure that an international audience can clearly understand your text.
Some examples where the language could be improved include lines 40-41, 58 – the current phrasing makes comprehension difficult. The authors should check this issue throughout this manuscript.
3.The authors should describe field design and treatment in detail. The amendments were applied once or repeatedly. The layout of plots should be provied.  The managment of plots should be added, including irrigation, etc.
4.Soil physicochemical properties in Section Results should be moved to Materials and Methods.
5.L121-122: The osmotic potential can serve as a good index for evaluating plant response to saline-alkali stress (Souza et al., 2012). should be moved to Materials and Methods.
6.L140-142: These contents should be moved to Materials and Methods.
7.L254: in the western Songnen Plain should be in the western Songnen Plain of China.


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: AMENDMENTS TO SALINE-SODIC SOILS SHOWED LONG-TERM EFFECTS ON IMPROVING GROWTH AND YIELD OF RICE (ORYZA SATIVA L.)
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comments.
Experimental design: No comments.
Validity of the findings: No comments.
Additional comments: The authors have done a good job revising their manuscript taking into account the review comments. I have no problem accepting the manuscript as it is currently written. There are still some editorial issues, such as verb tense errors, etc. that will need to be corrected as the manuscript is set for publication.

The addition of Figure 6 helps make the paper stronger.


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: AMENDMENTS TO SALINE-SODIC SOILS SHOWED LONG-TERM EFFECTS ON IMPROVING GROWTH AND YIELD OF RICE (ORYZA SATIVA L.)
Review round: 2
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The mauscript has been improved, and it can be accepted for publication in present format.


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: OPTIMIZING ALFALFA PRODUCTIVITY AND PERSISTENCE VERSUS GREENHOUSE GASES FLUXES IN A CONTINENTAL ARID REGION
Review round: 1
Reviewer: 1

Output:
Basic reporting: No comments.
Experimental design: No comments.
Validity of the findings: No comments.
Additional comments: This study uses a space-for-time approach to determine the optimum trade-off between alfalfa productivity and GHG-emission dynamics as related to stand age. Overall, the study is well-designed and the methods/results are clear, and the manuscript is well-written. More justification and rationale for the study is needed in the introduction, with some recommendations in the specific comments below. Additional comments/suggestions are included below.

Abstract
L32—37: Please add a sentence or two here that clearly states the implications and impact of the study results for management practices and/or ecosystem outcomes of semi-arid alfalfa stand management.
Introduction
L41 & 45: Specify that alfalfa is a forage legume, and that rhizobia are root-dwelling symbiotic bacteria.
L55: What are “certain” successive growing years? Is there a specific amount or range?
L61: The shift from alfalfa stand age in the previous paragraph to lack of alfalfa-GHG emissions research here seems sudden. Why are GHG emissions an important missing aspect of previous studies? I would recommend adding a better transition between alfalfa stands and GHG emissions, moving the third long paragraph (L68-82) about GHG emissions in general up to L59, and then expanding the paragraph currently in L59-67 to clearly explain the knowledge gap and potential ecosystem consequences of not addressing this missing research. Each of these paragraphs need clear transitions to the subsequent paragraphs/ideas.
L87: Specify which GHGs were measured and converted to CO2-equivalents.

Methods
L97-102: References for this information?
L105: The phrase “And one year study was designed due to stable climate condition and change of alfalfa stand age” followed by descriptions of different years and treatments is confusing. Does this mean that a long-term established forage study with differing stand ages was used for this experiment, and data collected for this experiment took place over one year? Please revise to clarify.
L112: “quadrat” not plural
L121: A 0.14 mm sieve seems very small. Why not 2 mm for air-dried samples? Was soil passed through this sieve size after crushing to a fine powder specifically for C and N analysis? Please clarify.
L130: Capitalize “Two”
L150: Delete “As” at beginning of sentence.
L165-166, 167-169: Could references be added for the WUE equation and GEE equation?

Results
L199: “mid-spring”?
215-218: This sentence is worded confusingly (easy to get mixed up with long sequence of “increased then decreased then decreased then increased”, etc.). Recommend splitting into at least two sentences and revising for clarity.
L223: Does “since April” mean the period leading up to April?

Discussion
L250: “although there were” instead of “although the”
L261—265: These sentences include fragments and are confusingly worded. Try altering to “…regrowth, greater amounts of C is translocated to the root system (refs). However, root development and C-fixation may decline after extended dry periods, which decreases SOC at the end of the growing season (Fig 3E).”
L289: Split into two sentences. Delete i.e. and begin with “Increased”.
L291-293: This paragraph conclusion seems sudden and could use more explanation. Why is soil structure invoked?
L324: “limited by” instead of “overlain by”?

Conclusion
L331: “overrides” instead of “overlies”?
L335—338: A much stronger study-specific conclusion and implications sentence is need after this call for more research. What are the current management recommendations and ecosystem outcomes that can be inferred from this study?

Table 2
This caption is the first time that structural equation modeling (SEM) is specifically mentioned in the manuscript. The construction and use of this model should be clearly explained in the methods and referenced in the results.

Figures 3 & 4
Recommend adding the equations/p-values for each panel to the figures themselves, not in the caption, and instead describe the parameters related within each panel.


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: OPTIMIZING ALFALFA PRODUCTIVITY AND PERSISTENCE VERSUS GREENHOUSE GASES FLUXES IN A CONTINENTAL ARID REGION
Review round: 1
Reviewer: 2

Output:
Basic reporting: See details in general comments below.
Experimental design: See details in general comments below.
Validity of the findings: See details in general comments below.
Additional comments: Dear editor and authors:

The present manuscript（ID: peerj-43325）is a report regarding optimizing alfalfa productivity and persistence vs GHG fluxes in the arid area of China. The reviewer argue this study with good design and labored works to give some novel information for accessing GHG fluxes of alfalfa production. The overall MS was prepared well except for those figures with poor quality, hopefully, it could be improved if this MS could go further. In addition, some suggestions and questions could be considered for revising as follow:
-With respect to abstract, I would suggest to rewrite it, please highlight the objective of study and add information about treatments.
-Line 69 and 74- Carbon dioxide and methane could be changed to CO2 and CH4.
-Line 131 to 133-is that ok using mean gases records from three successively sunny days to represent the average daily fluxes for that month? According to your results regarding SWC, I assume that gases fluxes would be changed largely when the field was irrigated, if it is necessary to record more measurements during that time. Definitely, you could not do it again, thus please add a reference here.
-Line 132-“after removing the above-ground materials”, remove the plants or something else, please make it clear.
-Line 134-Please add information about the size of chamber.
-Line 168 to 169-Please add the information on GEEwater.
-Line 170 to 185- suggest to remove all fig and table information from this part.
-Line 193 to 194- no statistical analysis results were shown in the fig, add or revise the description.
-Line 215- not clear “it increased with increasing when alfalfa”, please revise.
-Line 283-change leads to leading.
--Line 312- fig.
-Line 312-313-“may be that the increasing STN (Fig. 3D) promotes the uptake of NH4+-N plants, producing higher forage yield (Fig. 1A)”, how does increasing STN promote the uptake of NH4-N by plants? dose alfalfa prefer to use NH4+-N rather than NO3-? Please explain the causes of negative effect of STN on N2O effluxes with more accurate words.
-As for reference, suggest using more documents published recently.

Based on above comments, the final recommendation regarding this manuscript is major revision.


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

Input:
Title: OPTIMIZING ALFALFA PRODUCTIVITY AND PERSISTENCE VERSUS GREENHOUSE GASES FLUXES IN A CONTINENTAL ARID REGION
Review round: 2
Reviewer: 1

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


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

Input:
Title: CLPP REGULATES BREAST CANCER CELL PROLIFERATION, INVASION AND APOPTOSIS BY MODULATING THE SRC/PI3K/AKT SIGNALING PATHWAY
Review round: 1
Reviewer: 1

Output:
Basic reporting: 1. English needs to be proof-read by native speaker or professional proof-reader
2. Introduction needs substantial modification to provide more background
3. Figures need to be properly labelled, few figures need to be replaced with better quality images (refer to general comments)
Experimental design: No comment
Validity of the findings: Refer to general comments
Additional comments: Figure 1
•	Please provide high quality representative images for IHC data in Fig. 1E. It is hard to draw any conclusion based on the image provided in this manuscript.
•	Fig. 1F represents quantification of IHC data thus figure legend and result section should be appropriately modified.

Figure 2
•	Authors observed discrepancy in results from TCGA and Kaplan-Meier Plotter database for RFS and OS. Please comment on it in discussion section.

Figure 4
•	Quantification of colony formation assay data does not correlate with the actual effect observed in provided images. Please provide images from all the replicates in supplementary. Also, number of cells in control well for ZR-75-1 seems to be less than that for MDA-MB-231.
•	Invasion assay for ZR-75-1 should be repeated.

Figure 5
•	Figure legend is missing
•	Western blot result for p-PI3K is not very clear. Please provide better quality image to support any conclusion drawn


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: CLPP REGULATES BREAST CANCER CELL PROLIFERATION, INVASION AND APOPTOSIS BY MODULATING THE SRC/PI3K/AKT SIGNALING PATHWAY
Review round: 1
Reviewer: 2

Output:
Basic reporting: Generally, I found the manuscript to be written clearly. However, there were occasional lapses and mistakes that could have been avoided if the authors have had the manuscript read and edited by someone whose native language is English. E.g. In their abstract (line 20), they written “Case in hydrolytic protease (ClpP)…”, clearly it was meant to be “Casein in hydrolytic protease (ClpP)…” Another example early on in the manuscript would be at line 47, “…support cell growthy by different mechanisms to the surround tissues.” This sentence does not make any sense and I attribute it to a language error. I would therefore suggest the authors enlist the help of someone in future revisions of the manuscript to avoid such mistakes.

Recently, there was a published study in Cancer Cell on ClpP, see (https://doi.org/10.1016/j.ccell.2019.03.014). It would be good if the authors can cite and discuss the study in their manuscript and perhaps discuss their findings in light of this recent study.

*Note* The title of Figure 4 in their submitted manuscript is wrong (page 23 of submitted manuscript). It was titled, “Correlation analysis between ClpP expression levels…” I believed that is mistake as that is the title of their Table 1 (page 29 of manuscript).
Experimental design: With regards to their clinical results, I find that the data that ClpP is over-expressed in breast cancer to be convincing. However, I do not find the prognostic value of ClpP to be convincing. Firstly, the authors did not discuss the discrepancies of their findings from TCGA data and KM-plotter. Furthermore, the prognostic value of ClpP seems to be modest. There might be other clinical variables that affect the prognostic value of ClpP. The authors should therefore look deep into that to perhaps identify other co-variates influencing survival.

Concerning their functional studies, I would suggest the authors perform some gain-of-function studies, given that ClpP was identified to be over-expressed in breast cancer. Furthermore, in their loss-of-function studies, they only demonstrated results using 1 si-RNA while they had showed 3 effective siRNAs that can knockdown ClpP levels. It would be good for them to demonstrate the same effect with a 2nd siRNA and also perform rescue experiments to show specificity of ClpP to the phenotypes in questions.
Validity of the findings: Finally, I think that the authors did not clearly discuss their hypothesis or how they linked ClpP to the Akt signaling pathway. Was there any evidence to suggest Akt has a functional relationship to ClpP? If so, I seem to be missing the discussion in the manuscript. It seems to me that the authors just jump straight into looking at Akt signaling without demonstrating a relationship between ClpP and Akt. Is there protein-protein interaction or gene expression regulation? I would want the authors to further clarify and present data discussing the relationship.
Additional comments: No other comments beyond what is mentioned 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: CLPP REGULATES BREAST CANCER CELL PROLIFERATION, INVASION AND APOPTOSIS BY MODULATING THE SRC/PI3K/AKT SIGNALING PATHWAY
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: Authors have addressed all my concerns to satisfaction


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: CLPP REGULATES BREAST CANCER CELL PROLIFERATION, INVASION AND APOPTOSIS BY MODULATING THE SRC/PI3K/AKT SIGNALING PATHWAY
Review round: 2
Reviewer: 2

Output:
Basic reporting: No comments
Experimental design: No comments
Validity of the findings: No comments
Additional comments: The authors have tried their best to address my concerns within the time constraints. Further investigations would be outside the scope of the current 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: EFFECTS OF DIVERSITY AND COALESCENCE OF SPECIES ASSEMBLAGES ON ECOSYSTEM FUNCTION AT THE MARGINS OF AN ENVIRONMENTAL SHIFT
Review round: 1
Reviewer: 1

Output:
Basic reporting: 1.	The language used in this manuscript is clear and unambiguous, with profession English used throughout the document
2.	The literature cited is generally sufficient, but I think the manuscript would be improved with a slightly more in depth discussion of the effects of salinity on biological communities. For instance, explain how salinity affect communities through direct and indirect impacts would make it easier to follow. In addition, the study is about coastal ponds, but the authors do not explain their importance to the reader. As these unique ecosystems due to their biodiversity? Position in the landscape? Biogeochemical importance in the cycling of a select nutrients? Are they a good model system? This can easily be fixed.
3.	The article is structure correctly. However, I think the figures could be improved
a.	Figure 4 and 5 – There are a total of 6 PCoA figures, but only a total 2 axis one values and a total of 2 axis 2 values. I would expect to see axis values for each PCoA ( a total of 6 axis 1 values, and a total of 6 axis 2 values). Maybe I am missing something, but I think the authors could clarify this discrepancy.
4.	Tables and Figures:
a.	The circles and triangles look a bit pixelated, placing boarders around the icons would help, and potentially averaging the treatment groups to one point might help clean the figures up. In addition, I personally like the figures style in in Werba’s master thesis better then these figures ( figures 2-4, regression lines with confidence intervals, no data points). I find the trend much easier to follow, and seeing as you are providing all the raw data any reader could take the data points and plot them. Just a suggestion.
b.	Figure 2 - Not sure that running a linear regression is the most meaningful way to interpret these results. If you do decide to keep the regression in, I would think it would be important to report the slopes and assess how different the slopes are from one another – if your goal to perform some type of prediction. However, I could see you still using a GLM and just running an ANOVA on these results. While you wouldn’t get the predictive slope formula, it would highlight the differences between treatment groups, which might be more appropriate for these types of analyses.
c.	Figure 7 – are you sure this isn’t a unimodal or “bell curve” response? That would be a very interesting result, suggesting that intermediate levels of microbial richness have the greatest rates of carbon mineralization.  You could speculate that at these levels community members have synergistic relationships, but as the richness becomes saturated negative interactions and competitions reduce rates of carbon mineralization.
5.	Raw Data
a.	The authors have done a great job of providing the raw data from this project via github
Experimental design: 1.	The research is original to the best of my knowledge, and conforms to PeerJ Aims and Scopes
2.	The researchers clearly state they objective in line 49-51, “ i.e. how secondary salinity + mixing fresh and salt taxa affect diversity and composition of zoo. and bac. and downstream ecosystem functions” I wonder if this is really representative of the experiment they performed, or if the authors could craft/ edit this question to be more representative of their 1) study system, 2) study design, and 3) results. I think the first place to start would to be to include the idea of coastal ponds and “overwashing” into your objective, as your experiment is very tailored to this phenomenon. Also, I think your native vs. non native liter decomposition results are very interesting, maybe you would have a main objective and then 2-3 hypotheses that would either support or disagree this objective. I think the authors could make the knowledge gap more apartment by simply relating this to coastal ponds – what is going to happen to these “unique?, diverse?, important?” systems.
3.	Methods – methods are pretty thorough, but could use some clarification/ addition information in order to make them replicable.
a.	Line 97 – where did you collect these samples from? Water column ( top, middle bottom) did  sediments make it into your samples?
b.	Line 100-102, peat moss and sand, were these purchased or collected from the environment? Did you sterilize before adding to the microcosm? If you did not, can you address how you think the endemic populations of these substrates would/ would not affect the composition of your biological communities?
c.	General – were your mesocosms mixed any other time aside from when you collected sample?
d.	114-116 can you explain where these abiotic measurements were taken? Water column ( top middle bottom), or in the benthic substrate? Do you think sampling location would change your results ( i.e. do you believe there is any stratification in your tanks? Why/why not?)
e.	line 123-124, do you also use the integrated sampled to collect the bacteria samples?
Validity of the findings: 1.	I think most of these findings are valid, although I disagrees with the conclusion that richness is a positive relationship with co2 production, to me it looks unimodal across salinity suggesting a salinity optima. The authors could reaffirm their claim but explain how they used different models and their model was the best fit, or they should discuss how at intermediate salinities it appears CO2 is greatest, and the potential mechanisms for this finding + how it fits into the larger field of richness/function analysis in microbial/ ecosystem ecology ( maybe relate to species interactions (+,-) or intermediate disturbance hypothesis)
2.	Data appear robust and replicated, no reason that I see to question their validity.
3.	336-337 I think I understand what the authors are trying to say about HGT, but If they want to talk about HTG it should be more than one sentence. This could include but is not limited to what genes increase survivorship under increased osmotic stress, or other studies that have investigated the transfer of osmoregulation genes. Also – I think the authors have the potential to use their 16s sequencing to see if any taxa/otu in their experiment are more associated with salt system, or are potential halophiles.
4.	I think the conclusions could be greatly improved by (1) making them explicitly related to coastal ponds (2) concretely synthesizing and contextualizing their overall results in their final paragraph 359-365. Lastly, I would suggest they not end their paper on an intext citation. It would strengthen this paragraphs to being with that sentence ( we are answering the call to study taxonomic groups and functions across disturbance events)
Additional comments: Why are there no DO, NH4, PH data presented? If you aren’t going to show data then don’t talk about it in methods.
Present zoo plankton community data (abundance, diversity), you say that zooplankton functional groups are understood at the functional level ( lucky! I wish I could say the same for bacteria), so I think this should be a part of this paper. As is, you do not discuss this at all. Even if there is no change in functional groups of zooplankton that is still a very interesting finding.

Disagree with increased richness increases co2 production. While I agree it looks non linear, to me it appears that you have highest rates of co2 production at intermediate levels of microbial richness. I think this should be a much stronger component of this paper as it is a very interesting results. The authors should look for other papers which find a similar result to support their findings, or explain how their system is unique enough to present a different relationship with richness and co2 production.

I think you might want to reframe how you talk about CO2 production, as you don’t measure production over the course of the experiment, you only measure if at the end. Can you justify why this is appropriate? If I was the authors, I would make the argument that looking at the PCoAs ( figure 4 + 5)  – the communities remain essentially unchanged throughout the experiment, and thus the communities at the final point are probably pretty representative of all sampling communities

Source tanks (a) – one think to consider is that by using these source tanks, you will like have selective for non-natural communities that are likely much less diverse than the true “ over-wash” communities. I understand that logistically traveling to collect samples from coastal ponds before each treatment day might not have been possible, but can you give any sort of details on how your “source” communities might relate to the natural communities? Do you have any community metrics for the natural communities? Maybe you could make the argument that while less diverse, the “source” communities were still comprised of the same dominant members and thus we feel the response of this source community is pretty representative of natural communities?

Source tanks (b) – do you have any metric of communities found in the source tank? Curious if they would match the treatment tanks or if they would separate on an ordination.

Terminology – The authors use the word dispersal twice in the abstract, setting the reader up to think this will be a paper about dispersal. However, in the actual text of the manuscript it only appears once. The research addressed, and the literature cited by the authors, indicate this is a paper that focuses on salinity effects on community structure and function rather than community member dispersal mechanisms.

Decomposition - I think your decomp results are some of your most interesting results and should be discussed more. There is a large debate in aquatic systems if decomp is faster at salt sites than fresh sites, and I think these results could contribute to that conversation. I also found it interesting that the mixed community was better at decomposing spartina than the salt community. If you can do C:N on the litter used in this study that would be very interesting. If that is not possible, the three plant species you chose are very commonly used and described, I am sure you could pull their C:N values from some papers. That might be interesting to think about when interpreting these results.