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: CITIES MAY SAVE SOME THREATENED SPECIES BUT NOT THEIR ECOLOGICAL FUNCTIONS
Review round: 1
Reviewer: 2

Output:
Basic reporting: This is a very interesting study with broad implications for the conservation of biodiversity within cities. The authors provide an excellent introduction to the focus of the paper and the biology of the species of interest. The writing is generally very well done, with nice cohesive paragraphs and excellent use of references. I do identify some shortcomings with respect to the scientific foundation for the study. Though, I believe these can be remedied with revision.
I have included some suggestions for added referencing below.
line 55-57: awkward wording - suggest rephrasing.
line 62-64: indeed, there will be a shift in functioning and services, but could be the case that they'll offer new services or disservices in urban environments. See: Potgieter, L. J., Gaertner, M., Kueffer, C., Larson, B. M., Livingstone, S. W., O’Farrell, P. J., & Richardson, D. M. (2017). Alien plants as mediators of ecosystem services and disservices in urban systems: a global review. Biological Invasions, 19(12), 3571-3588.
Granted, this is for alien plant species, but many of the same principles apply for a shift in the distribution of native and/or threatened species to urban areas.
line 74-78: This is really interesting. On a philosophical tangent: Do we think about our pets as providing ecosystem services (e.g. cultural appreciation)? or do they cease to provide those services once they've been domesticated?

My main criticism of the study is in the lack of hypotheses that would otherwise guide analysis and discussion. The final paragraph of the introduction is the place to do this, but the authors, oddly, instead choose to highlight findings of the study. This final paragraph needs to be re-written to include hypotheses related to each line of inquiry in the analysis. This is where you should clearly state the hypotheses guiding the study and the general methodological approach, with more detailed methods following in the next section. I do believe this is possible to do with a revision.
Experimental design: - would recommend not using wikipedia as a reference.
line 131: "habitat use by parrots" - these "metrics" (also relative abundance in relation to habtiat, conservation threats, seed dispersal) should be introduced, with hypotheses, in the final paragraph of your introduction, then defined in the methods section.

For the habitat assessment, it is unclear how all this data is being synthesized. Perhaps a couple sentences on what you did with this data.

line 154-165: Would you expect parrot density to be significantly affected (positively or negatively) by proximity to roads? Probably need to comment on that.

line 167-180: This method/section would do well to reference some social-scientific approaches (really should have been used at the onset to develop your methods, but at least you can cite the scientific approaches that should have been used. (i.e. stakeholder analysis). See:
Reed, M. S., Graves, A., Dandy, N., Posthumus, H., Hubacek, K., Morris, J., ... & Stringer, L. C. (2009). Who's in and why? A typology of stakeholder analysis methods for natural resource management. Journal of environmental management, 90(5), 1933-1949.
&
Prell, C., Hubacek, K., & Reed, M. (2009). Stakeholder analysis and social network analysis in natural resource management. Society and Natural Resources, 22(6), 501-518.
Validity of the findings: The authors present some compelling findings regarding the distribution and density of these parrots in different habitats throughout the region. Again, these findings have significant implications for the future of biodiversity in cities, in general. The discussion is very well developed, with many interesting points regarding ecological function, the role of rare species and the potential for non-native species to take on the role of endemic species that are in decline.

Again, my main criticism is that the study needs to driven by scientifically-grounded hypotheses, and that these findings should be discussed in relation to those hypotheses.

Regarding the social aspects of the study, hypotheses may be difficult, but certainly a more formal framework/method for analysis is needed.

- line 218: Is this data including those parrots identified in homes? please clarify. If so, this definitely stands to affect much of your discussion.

-line 221: How did you decide which homes to sample? Was there a systematic approach? unclear.

-line 238: This line of inquiry should have been introduced earlier.

-table 1: check format
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: CITIES MAY SAVE SOME THREATENED SPECIES BUT NOT THEIR ECOLOGICAL FUNCTIONS
Review round: 2
Reviewer: 1

Output:
Basic reporting: After revisions, this paper, and in particular the hypotheses, are much more clear. Overall the paper is well written with sufficient background provided and reference to the relevant literature.
Experimental design: In this version of the manuscript, the methods are explained more clearly and the choice of methods is better justified.
Validity of the findings: Data is robust and statistically sound. Conclusions are well stated (and not over-stated).
Additional comments: I am happy with the revisions in this version of the manuscript and am pleased to give my support to the publication of this paper. I agree that it contains information important to the conservation of parrots.


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: AMPELISCA ESCHRICHTII KRØYER, 1842 (AMPELISCIDAE) OF THE SAKHALIN SHELF IN THE OKHOTSK SEA STARVE IN SUMMER AND FEAST IN WINTER
Review round: 1
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No commebt
Validity of the findings: No comment
Additional comments: Review of Demchenko et al. ms. on A. eschrichtii ms. for PEERJ, ms. 22763.

This is a fine ms.  First let me address its importance: big amphipods that are fed upon by whales is a rate example of benthic - pelagic coupling in the form of predation.  The more we know about these big amphipods, the better.  Most work in BPC is concerned with recycling of nutrients back to the water column, but this ecosystem is more tightly coupled than most.This is direct transfer of carbon, nitrogen and energy.

This ms. is trying to demonstrate, indirectly, that the amphipods grow and reproduce in the winter rather than the summer.  The evidence is good that little is happening in the summer, based on their delightful histology.  The big question remaining is why they did not sample in the winter and spring?  They ought to tell the reader why this obvious approach was not done.  Ice?  Too  rough?  No ship?

I like their comment in the short discussion section that the diatoms get to the bottom when the water mixed in the winter but not in the summer when the water is stratified.  But could other things be going on too?  How about hypoxia in the summer due to the stratification?  Erosion?

Bottom line: this paper could be published more or less as is.  My comments above are meant to be helpful, not a detraction.

Here are some things I noted: Fig 5C, is the 'spc' on the figure actually named 'spt' in the caption?
line 230,  drop the comma
line 231, 'these greatest' should be 'of these'
line 237, change 'delayted' to 'delayed'
lin e 248, drop the comma
line 283, drop the comma
line 383, in the references, all caps in title should be lower case.


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: AMPELISCA ESCHRICHTII KRØYER, 1842 (AMPELISCIDAE) OF THE SAKHALIN SHELF IN THE OKHOTSK SEA STARVE IN SUMMER AND FEAST IN WINTER
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript as it stands lacks from structure with elements of the methods and results more suited to the introduction and discussion. For example, the methods starts with a series of predictions/hypotheses with their underlying rational which arguably should have been laid out in the introduction. The methods then leaps into a list of life history stages without the context for the list stated when the methods/dates/location relating to the collection of the animals would be been more appropriate.

The results section is quite difficult to follow in places and is a description of histology would be helped if put in the context of the study and have a narrative to aid the reader through. Some of the results section could be rewritten in an easier to read format (e.g. page 6 line 187) "We classified their ovaries as atrophied" doesn't refer to anything and the next sentence has intro material and not results.
Experimental design: The experimental design is quite hard to assess as the number of animals collected and used for each element of the histology is hard to determine. On that basis it is hard to determine that the conclusions reached are valid given the value of 'n' and the lack of statistical analsyses. This makes the conclusions and the title rather speculative at this stage.
Validity of the findings: As mentioned above and highlighted by the authors (e.g. page 13 line 287) "Atrophied ovaries of two FII females indicate starvation and maximum use of the content of their ovaries..........". It appears to this reviewer that their is quite a lot of speculation in this paper based on a very low sample size from which the authors have based their entire conclusions and set their title of the paper.
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: AMPELISCA ESCHRICHTII KRØYER, 1842 (AMPELISCIDAE) OF THE SAKHALIN SHELF IN THE OKHOTSK SEA STARVE IN SUMMER AND FEAST IN WINTER
Review round: 2
Reviewer: 1

Output:
Basic reporting: None
Experimental design: none
Validity of the findings: None
Additional comments: Review of (rather re-review of) ms. for PeerJ on Ampeliscid gonad status and what it means (ms. 22763v2)

I stand by my original conclusion: the ms. is now improved with more information.  This is an important subject.  It is very difficult to determine seasonality in organisms in the field.  They have some evidence of it from histology.  That is commendable.

I do not understand or agree with the second reviewer's comments.  He or she makes no mention of the importance of the observations, only that they are too few from which to make conclusions.  The earliest observations of seasonality in the deep benthos were scant but nonetheless important and now have proved to be quite valid.  So, as I said above, publish this paper.


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

Input:
Title: PSYCHOLOGICAL, PHARMACOLOGICAL, AND COMBINED TREATMENTS FOR BINGE EATING DISORDER: A SYSTEMATIC REVIEW AND META-ANALYSIS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The report is clear and concise. the authors have reported on all relevant material. The English is excellent. there are adequate references and much background and context are provided. Tables and Figures are clear.
Experimental design: The experimental design is sound. Tables and figures depict the experimental process.
Validity of the findings: I am not sure about the novelty of the results. My only real concern is that a previous meta-analysis was published only two years prior to this one. The authors claim that their meta-analysis and systematic review contains more relevant studies and is not focused only on RCTs. In this case it is worthy of publication.
Additional comments: This is a systematic review and meta analysis of psychological, pharmacological and combined treatments for BED. This study is important in the field of ED as current studies on these effects provide contradictory results.
This study is very interesting and should be published. The study is well written and provides important information concerning evidence based treatments. My only real concern is that a previous meta-analysis was published only two years prior to this one. The authors claim that their meta-analysis and systematic review contains more relevant studies and is not focused only on RCTs. In this case it is worthy of 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: PSYCHOLOGICAL, PHARMACOLOGICAL, AND COMBINED TREATMENTS FOR BINGE EATING DISORDER: A SYSTEMATIC REVIEW AND META-ANALYSIS
Review round: 1
Reviewer: 2

Output:
Basic reporting: See general comments.
Experimental design: See general comments.
Validity of the findings: See general comments.
Additional comments: This was a systematic review and meta-analysis of psychological, pharmacological, and combined treatments for binge eating disorder. Most prior reviews have focused upon only one of these approaches to the treatment of BED, and as such, the present review is comprehensive in comparison. There are also several nice design features, including a solid search strategy, assessment of bias, and the grading of evidence. The conclusions concurred with most of the previous reviews on this topic.

1.	The language was acceptable. Yet the manuscript was long, and could be revised to be more concise and economical in expression. The lines in the Discussion which refer back to the Introduction (522-540) could proabably be cut/merged with the similar info in the Introduction. The material in the Introduction from lines 64 to 75 could also be trimmed/cut—this was informative, but not immediately relevant to the aim. It is also a question of whether the Results could have been better and more succinctly summarized in a table instead of page after page of text. I defer to the authors and journal regarding this point.

2.	Most of the implications were fairly research-oriented (i.e., need for longer follow-ups, trials should include adolescents, etc.), whereas concrete clinical implications were generally lacking. It would have been interesting to include some discussion regarding how findings match current treatment guidelines for BED such as NICE and other countries, e.g., Hilbert A, Hoek HW, Schmidt R. Evidence-based clinical guidelines for eating disorders: international comparison. Current Opinion in Psychiatry. 2017;30(6):423-437. doi:10.1097/YCO.0000000000000360.

3.	There were many trials with acceptable risk of bias, but only 1 study or fewer than 100 participants, and these were not included in any of the meta-analyses. This was unfortunate, as it resulted in the exclusion of a sometimes high proportion of available studies (i.e., 13 of 24 psychological treatment trials), although some of these studies were promising.  This conservative choice was acknowledged in the discussion, but perhaps another sentence or two at line 559 is warranted to expand upon the possible implications of the methodology applied.

4.  A related point---the term “low certainty of the evidence”  or “insufficient amount of studies” should be used (lines 230 to 270) instead of “insufficient scientific evidence”.  The latter term may be interpreted as having non-significant results----and cause some confusion.

5.Table 1. I would recommend to explain all abbreviations (e.g., CBT, SMD, RD, BE, etc) in the footnote so the table stands alone, without having to refer to the text.

6. In addition to your explanation of risk difference, I would also recommend explaining (on lines 271-276) the benchmarks for interpreting  SMD, as interpretation was a bit difficult in the absence of a funnel plot.


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: PSYCHOLOGICAL, PHARMACOLOGICAL, AND COMBINED TREATMENTS FOR BINGE EATING DISORDER: A SYSTEMATIC REVIEW AND META-ANALYSIS
Review round: 1
Reviewer: 3

Output:
Basic reporting: This is a well articulated article, a pleasure to read. It explores an important area of clinical significance, looking at the psychological, pharmacological, and combined treatments for binge eating disorder. Given the prevalence of binge eating disorders in obesity. this review is timely and worthwhile.  The abstract was clear and concise and provided a comprehensive summary of entire study.  Overall, the introduction was well constructed. All salient constructs well described and there was seamless integration of concepts. The rationale and justification for the present review was made clear.  The introduction concluded with a clearly stated aim appropriate to the research methodology. However Fairburn's CBT E model needs a mention in psychological interventions. Some minor edits have been suggested in language and referencing style (in text comments).Line 123 and 119 seem to contradict each other. Lines 126-132 seem out of place and perhaps belong in the Discussion section?
Experimental design: The method was clearly written and contained all relevant information appropriate to the methodology for a systematic review and MA. Relevant information pertaining to study design, eligibility criteria, data collection and data analysis were all clearly described. Again some in-text comments have been provided for minor edits.
Validity of the findings: Generally the results were very well presented. There was a very good summary of the limitations of the study.
Additional comments: This review has demonstrated a good level of analysis as well as potential applications back to the real-world and clinical settings in its comparison of psychological, pharmacological, and combined
treatments for binge eating disorder.Well done ! Some minor edits suggested in in-text 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: ANALYZING MIXING SYSTEMS USING A NEW GENERATION OF BAYESIAN TRACER MIXING MODELS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript is well written and I could not identify any major flaws or shortcomings.
Experimental design: Sound experimental design, good use of case study to illustrate the capabilities of the new mixing model formulation and platform.
Validity of the findings: As discussed in the article, mixing model analyses are becoming very common in ecological studies, however, the multitude of formulations complicates their use and interpretation. This article attempts to resolve some of the major issues in the field and provides a way forward.
Additional comments: Line 53 and throughout: The use of stable isotope “signatures” refers to the stable isotope composition of a significant reservoir like the geological mantle, air, ocean, lakes or a major part of the system being studied, not to the isotopic composition of individual samples. Most commonly, stable isotope composition of samples are referred to as stable isotope values. Consider revising.

I recommend this reference for stable isotope terminology: https://figshare.com/articles/Common_Mistakes_in_Stable_Isotope_Terminology_and_Phraseology/1150337

Line 148: No sure if the # is needed prior to (1). Revise if needed.

Line 151: Sort of a personal preference, but I suggest avoiding the use of and/or, as the / symbol should be relegated to mathematical equations. In most cases simply using “and” or “or” will work.

Line 153: Unless dissolved organic carbon and particulate organic matter is referenced in subsequent text there is no need to introduce the acronyms (DOC) and (POM).

Lines 155 and 156: See comment for line 53 regarding the use of “isotopic signatures”.

Line 165: Change (.) to (,) and remove # prior to (2).

Line 173: Not sure what “IID” means, not defined prior.

Line 175: Insert “,” after thus.

Line 176: See comment for line 53 regarding the use of “isotopic signatures”.

Line 181: Change (.) to (,) and remove # prior to (3).

Line 193: Not sure what “IID” means, not defined prior.

Line 212: See previous comment regarding “and/or” usage.

Line 226: Insert “,” after thus.

Line 235 and 245, throughout: Remove “/” in “uninformative”/generalist

Line 264: Insert “,” after equation before (4) and remove #.

Line 684: Citation for Nifong et al. (2015) used in the case study is not present in the References


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

Input:
Title: ANALYZING MIXING SYSTEMS USING A NEW GENERATION OF BAYESIAN TRACER MIXING MODELS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Well written and informative.
Experimental design: No comment.
Validity of the findings: The methodology is well explained and results are robust - with good discussion of the pitfalls.
Additional comments: A few general comments and suggestions:

Although I am enthusiastic about making Bayesian models more widely available and applicable, there are pitfalls, some of which are outlined in the manuscript, that will be difficult for researchers who are not familiar with Bayesian modeling to diagnose, let alone remedy. In that case, there is little substitute for experience. E.g., when is a lack of convergence due to mis-specification of priors, prior-data conflict, data issues, model-misspecification etc? This is often hard to diagnose, and perhaps it's worthwhile stating that reaching out to modelers (perhaps by mentioning the MixSIAR facebook, or pointing to github issues) is the best way to get over these hurdles. That may make it more appealing for people to pick up the tool. Issues such as those described in Brett (2014) could then be discussed and brought back to the information content of the data and prior choice.

L. 60: This fundamental mixing equation does not hold for fatty acid compositions if Y is the observed tracer value, as the measurement process for fatty acids leads to compositional data. Although the underlying (latent) mixing process may well conform to the equation, the observed outcomes do not. Given that the observed data for fatty acids is quite different from stable isotopes, I would suggest pointing out that the assumption of normality is not suitable for fatty acids as tracers, and that other software would need to be used (QFASA, fastinR). The ability to have covariates is also available in our fastinR package for fatty acids and stable isotopes (Neubauer & Jensen 2015), though admitted it has not been thoroughly tested (and hasn't been updated for a while).

L 264: The Dirichlet prior scaling: I think this is very difficult in practice – Fig 3 shows that although the unscaled prior from the actual observed prior sample size places very little weight on very small (near-zero) proportions for fish, the re-scaled prior places a lot of weight in that region, and comparatively little weight in the region of highest probability density of the original prior. This may lead to undesirable outcomes in practice. The text suggests the re-scaling provides a powerful tool and advocates running sensitivities to explore the impact of priors – although I generally agree, running sensitivities only seems useful if one understands what the prior assumptions are. Does MixSIAR provide ways to visualise the prior so that practitioners can understand what they are assuming for sensitivity runs? A sensible way to do this (and to deal with difficulties for linear model priors for mixing proportions) may be to let practitioners run their model without data to understand what the joint prior entails for mixing proportions. This may be especially relevant for models with covariates and/or random effects, the effects of which are not intuitive after transformation.

L338: Informative priors were discussed in the previous section.


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: STARCH BIOTRANSFORMATION INTO ISOMALTOOLIGOSACCHARIDES USING THERMOSTABLE ALPHA-GLUCOSIDASE FROM GEOBACILLUS STEAROTHERMOPHILUS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The authors describe the application of a moderately thermostable Bacillus strain with alpha-glucosidase possessing transglycosidation activity. The manuscript shows the certain potential of the enzyme to be used in sugar industry for isomalto-oligosaccharides (IMOs). The data described in this paper provide important factors which affect the enzyme activity and production efficiency of IMOs.
However, the experimental settings, formats of data presentation and some methods in statistical analysis should be improved before publication to clarify the author’s statements.
Experimental design: The authors describe the application of a moderately thermostable bacillus strain with alpha-glucosidase possessing transglycosidation activity. The manuscript shows the certain potential of the enzyme to be used in sugar industry for isomalto-oligosaccharides (IMOs). The data described in this paper provide important factors which affect the enzyme activity and production efficiency of IMOs.

Some descriptions and experiments  should be added as follows:

1. The origin of the strain used in this study should be stated in method section. For example, it was purchased from a XXX culture collection, isolated elsewhere (show references), or isolated in this study (show isolation method and origin of location and environment).

2. The thermal stability of the enzyme in this study and the other commercial enzymes should be compared. Because the authors referred to the thermal stability which is a bottleneck for this kind of enzymes in the introduction.

3. In Table 3, the description of experimental settings was not clear. More specified way should be employed to make the readers possible to conduct reproducible experiments.
Validity of the findings: The experimental settings, formats of data presentation and some methods in statistical analysis should be improved before publication to clarify the author’s statements.
Here are my opinions on specific points.

1. In Table 2, 7 9 and 10, The data should be showed with standard deviation from multiple experiments.

2. In Table 4 and 5, the data should be calculated in a statistical way and presented in text format in main manuscript, not in table format.

3. In Table 6, the description of the state of system is vague. The table should be removed, instead express in brief descriptions in the text.

4. In table 9, enzyme activity should be standardized though out a set of comparative study to demonstrate the efficiency of each enzyme.

5. In figure 5, please indicate the compound of the spot.

6. Experimental settings for enzyme evaluation in comparison with the commercial enzyme are not comprehensive. Please clearly state whether the experiments were conducted using immobilized enzymes or free liquid form enzymes.
Additional comments: The authors presented possible alternatives for commercial enzymes for IMOs. I think that the data presented here are significant to the reader for opening the way for further development of the same kind of the enzymes.
After appropriate revise according the suggestions, the paper can be published to promote the related research area.


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: STARCH BIOTRANSFORMATION INTO ISOMALTOOLIGOSACCHARIDES USING THERMOSTABLE ALPHA-GLUCOSIDASE FROM GEOBACILLUS STEAROTHERMOPHILUS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The English is understandable though some grammatical mistakes should be rectified. For example, line 85, “and 5 L- and 20 L-scale fermentations were also carried out”； line 206, “previous”; delete: line 293, 303, 307, 313, 321 “The effect…immobilization”.
Fig. 3b, the figure abscissa description was pH? According to the context, it should be time.
Fig. 5: the isomaltose points should be clearly indicated on the figure.
Experimental design: The HPLC method should be described in detail. Line 211, What were the "minor modifications"?
Validity of the findings: Conclusion section, line 390-395, “The molecular mass…. The effects of pH and temperature on enzyme activity and stability…. The optimum temperature…65°C”. These results were not shown and discussed in the manuscript.
Additional comments: This manuscript reported the application of a thermostable alpha-glucosidase from Geobacillus stearotheriophilus for the transformation of starch into isomaltooligosaccharides. Generally, the techniques involved were useful for the industrial preparation of IMOs. However, the statements should be improved as follows:

1)	The manuscript lacked comprehensive discussion of the results, especially the comparison with current IMOs production procedures in terms of thermostable alpha-glucosidase and immobilization of enzymes. The thermostable property of the investigated enzyme should be highlighted after some discussion and comparison with other known related enzymes.
2)	Line 237, “However, glucose affected the yield of alpha-glucosidase.” The current results did not support this claim. It is recommended to add some data on the enzyme yield or cite some literatures if this is widely acknowledged.
3)	Line 273, The results of fermentation experiments were in fact not described. The authors had only stated the fermentation process and conditions which should be described in the Materials and methods section. In addition, table 5, the enzyme activities in the 20 L-fermentation batches were not listed, described and discussed.
4)	Line 342, what is the "comprehensive consideration"? The reason for the opt of enzyme dosage of 20 U/g and liquefaction time of 12 min should be stated more clearly.
5)	Line 363, the HPLC results were not sufficiently described and discussed.
6)	The purification of the thermostable alpha-glucosidase was not provided.
Other mistakes that need revision:
1)	Line 22, 81, 406, “B. stearotheriophilus”, according to the microorganism used in the study , it should be Geobacillus stearotheriophilus (G. stearotheriophilus).
2)	Line 24, “Chisomaltooligosaccharide” should be isomaltooligosaccharide.
3)	Line 102, “p-NPG”, the full name should be given out in its first appearance.
4)	Line 374, “Fig. 6(A), 5(B) and 5(C)”, I guess it should be “Fig. 6(A), (B) and (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: STARCH BIOTRANSFORMATION INTO ISOMALTOOLIGOSACCHARIDES USING THERMOSTABLE ALPHA-GLUCOSIDASE FROM GEOBACILLUS STEAROTHERMOPHILUS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The manuscript have been revised properly according the reviewers comments.
Experimental design: The manuscript have been revised properly according the reviewers comments.
Validity of the findings: No comment
Additional comments: The manuscript have been revised properly according the reviewers comments. The paper will contribute to the progress of the related fields.


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: STARCH BIOTRANSFORMATION INTO ISOMALTOOLIGOSACCHARIDES USING THERMOSTABLE ALPHA-GLUCOSIDASE FROM GEOBACILLUS STEAROTHERMOPHILUS
Review round: 2
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: The Conclusion section only described what had been done in this study, while the main findings were almost missed.
Additional comments: 1.	The manuscript still lacked comprehensive discussion of the results, especially the comparison with current IMOs production procedures in terms of thermostable alpha-glucosidase and immobilization of enzymes. The thermostable property of the investigated enzyme should be highlighted after some discussion and comparison with other known related enzymes.
2.	Section 3.4.1, the reason for the opt of enzyme dosage of 20 U/g and liquefaction time of 12 min should be stated more clearly. The authors did not make a substantive revision.
3.	Section 3.4.2, the HPLC results were not sufficiently described and discussed, which actually was not revised by the authors according to the reviewer’s 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: AN INTEGRATIVE TAXONOMIC ANALYSIS REVEALS A NEW SPECIES OF LOTIC HYNOBIUS SALAMANDER FROM JAPAN
Review round: 1
Reviewer: 1

Output:
Basic reporting: The interesting paper reveals the phylogenetic structure of a group of Hynobius salamanders from Japan, resulting in biogeographic inferences and the description of a new species. The study is novel and original, and the topic is attractive to PeerJ. The basic presentation of the manuscript however needs improvements before acceptance can be considered. Below are the main points that caught my eye:

1. While the language is of sufficient standard to enable comprehension of all lines of arguments, the entire text still needs to become polished for example by an experienced native speaker. Many sentences contain little grammatical errors and awkward phrases which are not picked up by a spell checker. One example is the frequent lack of the article “the” connected to respective nouns – see e.g. line 20, which should read “…..that cover almost the entire range of the H. kimurae – H. boulengeri complex….”, and not ““…..that cover almost entire range of H. kimurae – H. boulengeri complex….”. There are many similar passages, and generally many similar examples of phrasing which needs to be polished. Also be consistent with the spelling of important terms (e.g. “egg-sac” vs. “egg sac”; use the latter).

2. Parts of the manuscript are arguably too long, and not all information is necessary to convey the main take home messages of the work. The > 1000 lines of text (excl. references) are not fully warranted. Because so many taxon-specific details are presented, the current style of the manuscript often resembles a paper for example in Herpetological Monographs, and findings of general relevance are getting a little lost in between taxon-specific details. Aspects which could become shortened are the detailed taxonomic history of related Hynobius species (not everything is fully relevant for the present work), the natural history details linked to the species description (most of the presented facts are already published elsewhere), and somewhat repetitive parts in the Discussion and Conclusion sections.

3. The main lines of arguments throughout the Introduction and Discussion are not well aligned to each other – it is always advisable to raise a list of topics in the Introduction before revisiting them again in the Discussion. While bio- and phylogeography plays an important part in the Discussion, such topics are not covered al all in the Introduction. Related to this, the start of the Introduction straight goes into the taxonomy and distribution of Hynobius, whereas initially covering a more general framework of the study (e.g. on phylogeny or biogeography) would attract a wider audience to the work.

4. Some important terms needs to be treated with more care. Given the obvious, demonstrated morphological differences between the new species and existing taxa (also figure visualises these marked differences), is it really appropriate to refer to it as “cryptic” in the title? This term is generally used for species which are difficult or impossible to identify based on morphology alone. I am also a little uncomfortable with the term “species complex” for the taxa under study – which encompassed only a pair of species prior to the present work, which were also historically not always assigned to a single grouping.

5. The figures are of particularly high standard – it is very evident how much work went into preparing them. Nevertheless it is a little questionable whether all 21 display items (14 figures and 7 tables, some of them very large) are really necessary in the main body of the paper, and whether some of them could be moved to a supplement/appendix. This might bring the key messages across in a more concise way.
Experimental design: I am not an expert with all the analytical pathways applied, but the research question is well designed, and the Methods are described in sufficient detail. The data analysis follows established procedures, and appears overall sound. I only have the following two comments:

1. The sample size is on the low size for some of the inferences. While sample sizes do not appear to violate any of the conclusions drawn, low numbers should become more acknowledged throughout the paper. For example, while Hynobius boulengeri plays an import part of the work (is one of the members of the “species complex” as termed by the authors), whereas actually only three individuals were available. For the morphological analyses, a range of parametric approaches was used (t-tests, ANCOVA), and I failed to find any information on whether data based on low sample sizes were normally distributed. Also, as far as I understand it, sufficient data to discriminate between males and females were only available for a subset of populations – how did this affect the overall analyses given that a fair degree of sexual size dimorphism was found? Given the extent of the manuscript I also might have missed the information provided.

2. In the Methods chapter, morphological aspects are described before genetic aspects and analyses, whereas in the Results chapter genetics is covered before morphology. It would be better if the order would be identical in both chapters.
Validity of the findings: I have no major criticism here. The conclusions are overall well stated, but (as outlined above) a little repetitive and not fully linked to the research question as outlined in the Introduction, where phylogeographic inferences are not well covered.

The case in support for the description of a new species comes convincingly across, and all formal requirement for species descriptions appear to have been adhered to.
Additional comments: No further comments needed.


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

Input:
Title: AN INTEGRATIVE TAXONOMIC ANALYSIS REVEALS A NEW SPECIES OF LOTIC HYNOBIUS SALAMANDER FROM JAPAN
Review round: 1
Reviewer: 2

Output:
Basic reporting: High quality, but too verbose, see below.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: This is a thorough and valuable integrative taxonomic analysis of Hynobius kimurae-boulengeri species complex. The study has clearly defined goals, is well justified, and makes a convincing case for the species status of H. fossigenus and provides a comprehensive taxonomic description of this species. The work is obviously based on impressive material and years of expertise. I don’t have any serious criticism regarding quality of science, but I feel that a major limitation of the paper is its length. While with online-only publication the length of the paper is not an issue from a technical/publishing side, it is still a problem from a point of view of the reader. In the case of this paper a rather straightforward message is communicated in an excessively verbose manner with large amount of descriptive material in the text. That imposes a heavy burden on the reader.
Specific comments
Abstract is too long and contains unnecessary details, such as: the length of sequenced DNA fragments, details about statistical and phylogenetic methods, sample sizes for individual analyses etc. Briefly, I would suggest what you did and what you found while limiting methodological details. Time of divergence estimates values with two decimals make false impression of precision of the order that is not achievable with molecular clock analyses.
l. 68-95 this history of research and a plethora of names makes a rather tedious read and disrupt the flow of the ms. Could you please consider moving it to an appendix or supplementary materials?
l. 150 a single nuclear gene is a very weak (weakly informative) marker of gene flow, especially as only a single individual of H. boulengeri was used; please make sure that you discuss limitations of using only a single nuclear marker
l. 242-46 ratios are rather questionable taxonomical tool. I have impression that you put too much emphasis on them Why don’t you rely mainly on PCA, which takes all the variables into account simultaneously
l. 258 ml -> ul
l.314-320 here you describe the procedure to deal with heterozygous positions but later in results (l. 348, should “heterogeneous” be “heterozygous”?) you say that there were none
l. 346 what you mean by “conservatie”? not variable?
376-392 please shorten this part, perhaps this information could be added to the figure showing the distribution
l. 402-420 this part is too long, and I don’t think that interpreting these results as mito-nuclear discordance is warranted with only a single nuclear marker of low variability
l. 435-454 most of this descriptive material could be moved to tables
781 brakes -> breaks
840-918 this comparison is descriptive and very long, it relies heavily on ranges of morphological indices which is questionable from both theoretical and practical point of view

Measurements, i.e. raw data should be in supplementary tables, not in the main text


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: AN INTEGRATIVE TAXONOMIC ANALYSIS REVEALS A NEW SPECIES OF LOTIC HYNOBIUS SALAMANDER FROM JAPAN
Review round: 1
Reviewer: 3

Output:
Basic reporting: In an attached annotated PDF, I have provided additional minor corrections to grammar, spelling, and typos, and suggest some word changes and rephrasing. Throughout the manuscript, there are numerous minor grammatical errors (e.g., omissions of "the") that I assume are due to nonnative English language. But I strongly believe that academic publishing should be globally inclusive and as accommodating as possible to scientists whose native language is not English, so I do not suggest the authors hire a proofreader or spend an excessive amount of time correcting very minor errors that do not in any way hinder clarity or understanding of the manuscript. Therefore, I did not mark any of those extremely minor errors; I primarily made corrections/suggestions for errors or phrasing that made the authors' meaning unclear. Overall, I was quite impressed with the writing!

Minor but still important comments & suggestions:

- Would it be preferable to include the new species name Hynobius fossigenus in the title?
- Abstract: too much detail. Abstracts should be short and concise.
- L. 39: reword to omit "basal" -- this misuse of the term "basal" is very common in the phylogenetics literature, unfortunately. I suggest something like "The H. kimurae - H. boulenteri species complex is sister to all other Hynobius except H. retardus." (To compare: Table 3 is a correct use of "basal" because it is referring to ancestral nodes, not lineages or extant species.)
- L. 442-454: Is it necessary to present the same data here and also in the new species diagnosis?
- L. 472-506: I'm not familiar enough with papers that include new species descriptions to determine what information belongs in this section vs. the Discussion below, and what information (if any) should be duplicated and presented both here and in the Discussion. Some of this seems repetitive, but it's A LOT of information, so it's hard for me to follow and really determine what is repetitive or not.
- Fig. 2: it is very difficult to see gray vs. white node markers. I suggest completely eliminating the circle markers on unsupported nodes and changing the gray circles to white (i.e., black = strong support, white = moderate support). Also, specifically define the cutoffs you use for strong vs. moderate support.
- Fig. 3: Does the gray shading on the inset paleogeographic reconstructions indicate above-water land? This should be added to the legend.

Very minor comments & suggestions:

- L. 90: define the abbreviation "mtDNA" at its first use.
- L. 231-232: "presence of the whiptail-like structure (WT) and the following five characters were recorded" - confusing wording. Why is WT listed separately from the other 5 characters?
- L. 256: "mtDNA" already defined above
- L. 342-344: confusing wording
- L. 354 and forward: Seems strange to explicitly state e.g., "Results of phylogenetic analyses are shown in Fig. 2." Usually, figures and tables are referred to parenthetically within the sentence discussing results shown in that figure/table.
- L. 389: italicize species name.
- L. 394-395 and caption for Fig. 2: reword. I don't think you mean to say you calculated genetic distance between 16S and cytb.
- L. 418: reword. The data don't just "suggest a possibility" of this; they do show mito-nuclear discordance.
- L. 435-454: It's cumbersome and a bit confusing the way these populations are referred to in this section. I suggest using either only the locality name (e.g., "the Mt. Hinode population") or "western clade" and "eastern clade."
- L. 456-457: I've most often seen PCA factors referred to as "PC1" and "PC2." The terms "F1" and "F2" in biological literature usually refer to offspring generations.
- L. 576 and forward: Seems strange to always spell out the full genus name of Hynobius fossigenus instead of abbreviating to H. fossigenus as appropriate, especially outside of the species description/diagnosis. I suggest changing this unless it is standard practice in papers that include a new species description.
- L. 597: Is it normal for genetic diagnoses to be this vague and subjective? I.e., does more specific information from the Results section need to be repeated here or not? I am not a nomenclature expert...
- L. 795-796: confusing wording. Do you mean the range of H. fossigenus (which would not make sense), or the combined ranges of all species in the genus?
- L. 827-832: This is a confusing run-on sentence that should be split into 2 or more complete sentences.
- L. 840-843: confusing wording.
- L. 1013-1016: awkward run-on(?) sentence.
- L. 1029-1035: This is just restating information already presented in Results and Discussion and doesn't need to be repeated here.
- Fig. 10: "egg sacs" is hyphenated throughout the body of the manuscript but is not hyphenated in the legend for Fig. 10. I have most often seen the term as two words, not hyphenated, but this is a very minor issue.
- Table 4: I suggest changing the headings "Min-Max" to "Range" to clarify that this should not be interpreted as the maximum subtracted from the minimum, and also because the values in those columns are referred to as "range" in the figure legend. Use of "Min-Max" alongside "Mean±SD" is a bit confusing.
- Tables 5-7: Should these tables be moved to Supplementary Information?
Experimental design: Major issue:

L. 90-94: I'm confused -- Weisrock et al. 2013 does not show H. kimurae to be sister to H. boulengeri, but instead sister to H. hirosei, and H. boulengeri is quite distantly related. In contrast, Nishikawa & Matusi 2014 show H. kimurae sister to H. boulengeri, and H. hirosei is more distant. (I don't have access to Larson et al. 2003.) As far as I can tell, Weisrock et al. 2013 and Nishikawa & Matusi 2014 both included H. hirosei from Shikoku Island, H. boulengeri from Kii Peninsula, and H. kimurae from Shiga (within western clade [H. kimurae sensu stricto] in this manuscript). The only difference is that Weisrock et al. 2013 sequenced 12S-16S and ND2-COI, whereas Nishikawa & Matusi 2014 sequenced cytb. Is there another explanation for the discordance between the two phylogenies? A brief discussion of the conflicting phylogenies from Weisrock et al. 2013 and Nishikawa & Matusi 2014 should be mentioned, especially since Weisrock et al. 2013 does not show H. kimurae to be sister to H. boulengeri. Also, I think it is important to include separate BI phylogenies for cytb and 16S, in addition to the concatenated data set, since these prior publications show very different phylogenies. The figures for phylogenies of cytb alone and 16S alone could be added to Supplementary Information, and a brief statement added to the Results...and to the Discussion if it turns out the two phylogenies are not concordant. Though, even when lotic/lentic is plotted on the phylogeny from Weisrock et al. 2013, the statement on L. 941-945 that stream-breeding adaptations have evolved multiple times still holds.

Minor but important comments & suggestions:

- L. 236: Please explain why only this 1 population.
- L. 288-289: Why were these additional sequences for H. kimurae and H. boulengeri included? E.g., were they samples from unique localities?
- L. 292-294: Please explain here the purpose of this analysis with an expanded data set. From the current wording of this paragraph, it is not entirely clear that this is a separate data set and separate analysis from the data set and analysis described above in L. 289-290.

Very minor comments & suggestions:

- L. 295-301: Confusing wording. I assume you first concatenated the data, then ran PartitionFinder, then determined from PartitionFinder results what your partitions should be. The phrases/sentences here should be reordered.
Validity of the findings: Minor but still important comments & suggestions:

- L. 730-731: "clearly corresponds to a species level of differentiation" -- be careful how strongly this is worded. Determining the level of genetic differentiation sufficient for elevating to species status is essentially entirely subjective, so I don't think "clearly" is an appropriate word here.

Very minor comments & suggestions:

- L. 357-359: It is often unclear what is meant by "high resolution" in phylogenetic context. Better phrasing is to note that phylogenetic relationships among major lineages were strongly supported.
- L. 363-367: Where does this information fit in with the current study? Were these species once considered part of H. boulengeri? Meaning of "former members of the H. boulengeri species complex" is unclear.
- L. 374-375: Reword. There was either moderate support or there was not. Trees don't "suggest" levels of support; the bootstrap/bpp data either support or don't support particular clades.
Additional comments: This is an interesting study on Hynobius salamanders in Japan. The authors use genetic and morphological data to show that the eastern clade of "H. kimurae" should be elevated to a new species, and they provide and thorough diagnosis and description of this proposed new species, Hynobius fossigenus. This study used only mitochondrial genes and 1 nuclear gene, but within their focal species complex the mitochondrial and genetic data agree that H. fossigenus is distinct from H. kimurae (despite mito-nuclear discordance regarding relationship to H. boulengeri), and their morphological data provide additional support for elevation of the eastern clade of H. kimurae sensu lato to species status as H. fossigenus. My only major concern with this study is regarding expanded analysis and discussion of phylogenetic relationships of other Hynobius species, and ecological conclusions based on that phylogenetic inference. This study will be an important addition to the salamander literature once the concerns below are addressed.


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

Input:
Title: FISH SPECIES RICHNESS IS ASSOCIATED WITH THE AVAILABILITY OF LANDSCAPE COMPONENTS ACROSS SEASONS IN THE AMAZONIAN FLOODPLAIN
Review round: 1
Reviewer: 1

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

I reviewed the manuscript "Landscape components and flood pulses drive fish species richness in Amazonian floodplain lakes", which brings evaluations among how taxonomic and functional species richness, measured in high and low-water periods in Amazon lakes. The authors suggest that the total species richness was more sensitive to variations in the landscape areas than number of species within guilds and the spatial extent of the wetland class of shrubs was consistently the more influential on fish species diversity. Authors provided careful samplings and a satisfactory analytical protocol. I have some minor comments that I believe that authors should discuss in their manuscript.

Specific comments and suggestions:

Line #88
Inform the size of lakes

Line #114
"…we quantified the areas of
landscape variables (m2) in 500, 1,000 and 5,000 m (radius)… "

Explain how the size of the buffers (500, 1,000 and 5,000 m) has been determined and whether there is any relation to the size of the ponds.

Not a question that would justify the use of different buffers is shown.

Line #118
“…11 standardized floating gillnets 15 m long and 2 m deep with
varying stretched mesh sizes (30, 40, 50, 60, 70, 80, 90, 100, 110, 120 and 130 mm).”

Comment on whether these nets are floating or at the bottom of the river. This may reflect on sampling and specie group colleted.

Line #120
“ … remained in the water for 12 hours in Ananá, Araça, Baixio, Iauara, Maracá, Poraqué, and Preto lakes; and for 48 hours in Cacauzinho, Calado, Camaleão, Camboa, Central, Padre, Santo Antonio and Sacambu lakes.”

There is some reason for the differences in the time of exposure of nets in the lakes, How this was controlled in the analyzes.

Line #122
“Sampling effort among lakes were standardized as the product of the number of samplings and sampling time (hours)”

You need a better explanation. Is this a CPUE? It is confusing because it is mentioned that only the richness of species was used.

Line #126
“While sampling frequency varied among lakes, each lake was sampled at least once during both high and low water
periods (Fig. S1).”

What was the effort for each point in the two seasons? And how this effect was controlled.

Line #132
“…buffer for high and low-water periods. We first modeled total species richness as response variables and the are…”

What is the reason to use only the number of species and not the species composition?

Line #139
“…we included in the model species abundance as an independent variable. Models fitted to the low-water data were constrained to the…”

I believe you need to make clear what is being said about species richness, in here you used abundance.

Line #147
How it was worked with the autocorrelation that occurs between the different sizes of buffers since the buffer of 500 is inside the 1000 and this one is inside 5000.

Line#160
“A total of 178 species was collected.”

I suggest to present in supplementary material the list of species, trophic category, migration, and presence/absence by lake.

Line#169

“Omnivores species richness was, again, positively related with shrub cover but just in the small-scale (buffer of 500m) (Table 2, Fig. 3e).”

This information had not been mentioned yet.

Line #199
“… flood-pulses (Fernandes, 1997; Castello, 2008). The observed rise in resident species (e.g. Osteoglossum bicirrhosum, Cichla monoculus)…”

I would suggest a list of species in Supplementary Material.

Line #212
"The significance of flooded herbaceous areas as refugia for several prey species during the high-water could not be clearly quantified as several groups of herbivores, carnivores, and migratory species did not have any significant relationship with the extent of this landscape variable. We note that herbivorous fishes, and possible migratory species, have previously been shown to have strong relationships with forest cover (Arantes et al., 2017), but we were not able to assess this."

Paragraph loose in the text.


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: FISH SPECIES RICHNESS IS ASSOCIATED WITH THE AVAILABILITY OF LANDSCAPE COMPONENTS ACROSS SEASONS IN THE AMAZONIAN FLOODPLAIN
Review round: 1
Reviewer: 2

Output:
Basic reporting: Dear author of the manuscript “Landscape components and flood pulses drive fish species richness in Amazonian floodplain lakes”,
I really like your research question and I think these data can result in a good paper. Furthermore I like your way of writing, as it is mostly clear and easy to understand. Only in one section of the MATERIALS AND METHODS some improvement is needed to clarify the methods.
Line 113-115: Could you please mention that the landscape variables in your circular buffer are the four landscape variables defined by Hess et al. (2003). I find this section confusing.

In the tables and figure I found some mistakes, but as I also recommend a new data analyses, the tables and figures need to be renewed anyway.
Table 1: Santo Antonio: 1229?
Table 2: -0.018#?
Figure 3: figure fuzzy; why do you have different dots in the omnivorous graph?
Figure 4: figure fuzzy; labeling of the figures wrong
Experimental design: The idea to calculate the species richness from the gillnet data is great, but I have some concerns about the experimental design:
Why did you use floating gillnets? Why not benthic gillnets? Or other fishing gear? Please discuss that.
In which depth did you set the gillnets? What is the morphology of the sampled lakes? Did they differ in mean depth, maximal depth and size? That might also influence your findings. Please integrate this in your study, if available. Otherwise you should at least clarify that your sampling lakes didn’t differ in these variables.
You compare the different feeding types and migratory/resident species in your manuscript. I recommend testing for differences between benthic and pelagic species as well.
For your data analyses you should use a multivariate correlation to get better results.
Validity of the findings: The findings of the authors show differences in species richness between high-water and low-water season. Moreover the landscape variables seem to influence the species richness. These are good results, but nevertheless the data should be analysed in a more appropriate way, e.g. with a multivariate correlation. The new analyses might lead to better/different results and therefore validity of the findings has to be challenged.
Additional comments: I hope you revise this manuscript in a proper way, because these are great data, that should be published!


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: FISH SPECIES RICHNESS IS ASSOCIATED WITH THE AVAILABILITY OF LANDSCAPE COMPONENTS ACROSS SEASONS IN THE AMAZONIAN FLOODPLAIN
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Dear author of the manuscript,
I like this a lot better than the first version. However, there are a few mistakes in grammar etc.

line 87: Herein, we tested......

line 91: (i.e., high- and....

line 161: and 2 m high with varying.....

line 173: time (hours; S1) and the.....

line 326: in this system. Including these..... There are 2 spaces in a row!

Please make sure, that you doublecheck your manuscript again for mistakes like that. Having a manuscript without mistakes supports the validity of your findings!


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

Input:
Title: AAQUETZALLI IS REQUIRED FOR EPITHELIAL CELL POLARITY AND NEURAL TISSUE FORMATION IN DROSOPHILA
Review round: 1
Reviewer: 1

Output:
Basic reporting: The article is well written and only contains few typos and sentences that should be corrected/improved.
line 31-32: “aqz encodes pioneer proteins with a conserved domain.” is vague and it would be better that the abstract clearly states the findings of the article: “aqz encodes proteins  that harbor a domain with significant homology to a proline-rich conserved domain of nuclear receptor co-activators.”
line 91: “RNAi injected in developing embryos sport defects…” should be replaced by “RNAi injected in developing embryos show defects…”
line 146: “deoxycytidine 5’-trisphoshpate” should be corrected to “deoxycytidine 5’-triphosphate”
Line 466:”…differentiate to ganglion mother cells, r differentiate later, a rationale…” should be corrected to ”…differentiate to ganglion mother cells, or differentiate later, a rationale…”

Figure 1 legend states that the LD47990 was used as a probe for aqz-RA while LD02060 is used for RB, RC and RD. The location of LD02060 is indicated on the figure  (showing it cannot detect RA transcripts) but the location LD47990 is missing to confirm that the probe only detects the RA transcript.

The material and method section for Northern-blot is in disagreement with figure 1 by stating that probes were from LD47990 and the aqz 5’ region instead of LD02060 (line 145).

The description of the aqzRescue construct is not provided in the material and method (cloning procedure, injection, transgenic strains) or indicated on Figure 1. Figure indicates rescue on the map that corresponds to a BAC construct that contains many transcription units that would not allow the authors to conclude that the lethality and neurogenic phenotypes are caused by the CG9821 transcription unit.

Figure 3G and 3H genotypes are incorrectly reported: the GFP allele is not homozygous in the rescue genotypes and appears located on 2 different chromosomes (using ; instead of ,). The rescue construct is on the 2nd (53B2) and the aqz allele on the third (85B2). The genotypes should be aqzRescue/+; aqzGFP (1 copy rescue) or aqzRescue;aqzGFP(2 copies rescue). Homozygous genotypes should also be written aqzGFP and aqzRescue (no need for /).

Figure 3H (and supplemental Figure 3H) is very confusing and hard to understand. It appears as almost 100% of the wild-type control die as adult. Bar graphs showing the lethality at each stage (3 bars) as % of previous stage would greatly help.
Experimental design: The authors needs to provide more details on how the Northern-blot and in situ probes were made (clone used and fragment used for multi prime labelling). The amount of RNA used for the Northern-blots is also missing.
Validity of the findings: It is pretty rare that a gene is poorly documented on FlyBase and that the nature and number or transcripts/proteins solely result from computer predictions. The authors finally provide experimental data that clearly show the inaccuracy of the computer predictions regarding the size and number of transcripts. The use of the Northern-blot technique provides a much more accurate examination of the locus that does not involve any PCR or reverse transcription steps that can easily distort the results. The authors should however indicates (and ideally provides in supplementary data) that the probe has been confirmed to only detect transcripts from the aqz locus (the probe used is not strand-specific) by using single-stranded probes or showing absent/reduced northern signal on RNA isolated from mutant alleles.

The rescue experiments with the aqzRESCUE construct are the most conclusive data that the neurogenic phenotype of the aqz1 and aqzGFP alleles are caused by an alteration of the CG9821 transcription unit. The complementation data (Table 1) show that the lethality phenotype is complemented between aqz1 and aqzGFP (confirmed by fig 3H and sup Fig 3H: most lethality occurs in larvae with aqzGFP while most lethality occurs in pupae with aqz1). This observation implies that aqz1 and aqzGFP cause lethality by altering different genes. It is confirmed by deficiency complementation: aqzGFP lethality is not complemented by the deficiencies (therefore the alteration is located between 85B1 and B6 as stated in Table 1 legend) while aqz1 lethality is complemented therefore indicating that the defect causing the lethality is not located between 85A5 and 85C2. The authors did not test the rescue of the legality of the 2 alleles similarly (no wild-type control and no rescue with only one copy of aqzRescue) but it seems that the pupal lethality is comparable between homozygous aqz1 and the rescue genotype (~50% larvae die and 100% of the 50% larvae that pupated die, comparable to ~90% pupal lethality in homozygous, larval lethality is likely due to the use of 2 copies of aqzRescue as observed in Figure 3). It is therefore most likely that the aqz1 strain has 2 different alterations: one outside of the aqz region that cause pupal lethality and one within the region that is not strong enough to cause larval lethality (or very weak considering that the larval lethality appears a bit higher than the wild-type control used in aqzGFP rescue in Figure 3) but do cause neurogenic phenotypes. It is critical for the validity of the findings that the authors describe the aqzRESCUE construct used to show that it only contains the aqz transcription unit. The rescue construct shown in Figure 1 (BAC) contains many transcription units and would not allow concluding that the neurogenic phenotypes are caused by the CG9821 transcription unit.

It is unfortunate that the authors were unable to obtain antibodies. The authors do not have any experimental data to demonstrate that CG9821 transcription unit encodes more than one kind of protein. The abstract (line 31-32) should say that the locus encodes a putative protein (no plural).
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: AAQUETZALLI IS REQUIRED FOR EPITHELIAL CELL POLARITY AND NEURAL TISSUE FORMATION IN DROSOPHILA
Review round: 1
Reviewer: 2

Output:
Basic reporting: Results are clearly presented and well explained except at some places like
1. Fig.5, it would be more clear if you also provide the separate channel images along with the merged one.
2.There are some typo and spacing errors, one again a thorough reading will solve that.
3. Fig.8 has lots of discrepancy in labeling.
Experimental design: 1.Expression pattern of Aqz would be more clear with co-immunostaining for specific neuroectodermal, peripheral nervous system or mesoderm in  Figure 4. Can show with any one of them which shows the best expression.
2. What about the Aqz expression in Aqz mutant, can show with alpha- Aqz antibody staining.
3. Fig.8, Mutant embryos are showing more intense expression of GFP-Aqz as compared to control embryos, is it really the case or just because of merging of multiple stacks during processing in case of mutant or if there is more intense expression then why it is so.
Or It would be more better to use Aqz antibody instead of GFP.
Validity of the findings: no comment
Additional comments: This article further enhances our understanding about the role of Aqz during the  development specially in the embryonic ectoderm, and ectodermally derived tissues. Moreover, this study indicates toward its even more major involvement in various important developmental processes by altering the expression of polarity proteins and that would be even more interesting to study.


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: BIODEGRADATION OF CRYSTAL VIOLET DYE BY BACTERIA ISOLATED FROM TEXTILE INDUSTRY EFFLUENTS
Review round: 1
Reviewer: 1

Output:
Basic reporting: In this manuscript, the authors proposed the concept of utilizing bacterial to degrade organic dyes/pollutants (crystal violet as a sample). They have optimized the conditions of pH, temperature, and reaction time. Overall, this is an interesting paper and could has impact in the near future. Some points need to be considered before the acceptance of this manuscript.
1.	I strongly suggest the authors provide the absorption spectra of crystal violet at different degradation times. This will help the readers to understand more clearly about the degradation level at a specific reaction time.
2.	Also, I suggest them to provide the photograph of bacteria at different degradation times. If the bacteria maintain their original color (for example, white), this means that the de-colorization of crystal violet solution is truly from the degradation by bacteria. Otherwise, the de-colorization of crystal violet solution could also happen when the crystal violet is adsorbed on bacterial.
3.	Because the degradation time is 72 hours, the authors also need to prove that after such a reaction time with crystal violet, the bacteria are still alive. This will help the readers to fully believe that the degradation of crystal violet is from bacteria themselves.
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: BIODEGRADATION OF CRYSTAL VIOLET DYE BY BACTERIA ISOLATED FROM TEXTILE INDUSTRY EFFLUENTS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Introduction part need complete some degradation data of references with this study.
Experimental design: It is presents well and a smart design.
Validity of the findings: A good ideal for degradation of dye with CV-S1.
Additional comments: 1. Why the degradation rate is highest at pH 6.5?
2. What is the lifetime of bateria CV-S1?


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: BIODEGRADATION OF CRYSTAL VIOLET DYE BY BACTERIA ISOLATED FROM TEXTILE INDUSTRY EFFLUENTS
Review round: 1
Reviewer: 3

Output:
Basic reporting: 1.	The title should be reworded. The following two titles have been suggested:
i.	Biodegradation of crystal violet dyes by bacteria isolated from textile industry 	effluents.
ii.	Characterisation of crystal violet degrading bacteria from textile industry effluents.
2.	Comprehension of the introduction section of this manuscript is difficult without thorough editing and recasting of several statements. Some areas have been highlighted in the manuscript and suggestions made.
3.	Line 114-118: The objective should be recast ‘the present study aimed to isolate and characterise crystal violet degrading bacteria from textile industry effluents for potential use in industrial bioremediation process’.
4.	The figures and tables are not properly referenced in the text.
5.	The methods described under abstract does not adequately described the work done. The statements should be recast.
Experimental design: 1.	References were not cited for some of the methods used in the experimentation.
2.	There are several instances where assertions were not substantiated with references. This has been noted in the appropriate sections of the manuscript.
3.	There are several sections that are unnecessarily included under methods (section 2.2,2.7, 2.6).
4.	The results should be preferably separated from discussion.
Validity of the findings: 1.	I’m concerned about the quality of the discussion.  The work was poorly discussed. Also, comparison with results of others was poorly done. This is a major concern because as it is currently presented, the discussion is not interesting.
2. a suggestion has been made on how to improve the conclusion.
Additional comments: The authors investigated the efficiency of a newly isolated and characterised bacteria in the bioremediation of industrial effluents containing crystal violet dyes. While the finding is exciting as the isolated bacteria may find useful role in bioremediation, the report was poorly written and sections of the same results repeatedly stated. Some other areas of concerns are highlighted below:


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

Input:
Title: COMPARISON OF THE TOXIC EFFECTS OF DIFFERENT MYCOTOXINS ON PORCINE AND MOUSE OOCYTE MEIOSIS
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: This is a very interesting study that is additive to our knowledge of different mycotoxins impact on porcine and mouse oocyte meiosis as well as has provided basic data for the further studies on mammalian oocyte research. The authors isolated oocyte from antral follicles of pigs and mice and exposed those in culture to different concentrations of different mycotoxins. They determined the different sensitivity pattern between mouse and porcine oocytes. In manuscript, the grammar and expression of English would be better to get a major revision to make readers' easy understanding. There are also minor comments to address:
1. Since dosing is done in vitro, the authors need to provide a justification for the doses selected.
2. Were all of the porcine and mouse oocyte collected and cultured at the same time? How many oocytes did they collected used for statistic?
3. 206, 209,223,229=10 μM, not 10μM. Please recheck and correct the related contents.


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

Input:
Title: COMPARISON OF THE TOXIC EFFECTS OF DIFFERENT MYCOTOXINS ON PORCINE AND MOUSE OOCYTE MEIOSIS
Review round: 1
Reviewer: 2

Output:
Basic reporting: 'no comment'
Experimental design: 'no comment'
Validity of the findings: 'no comment'
Additional comments: The manuscript entitled “Comparison of the toxic effects of different mycotoxins on porcine and mouse oocyte meiosis” submitted by Lu et al. describes a study about the effects of mycotoxins (Aflatoxin B1, Deoxynivalenol, HT-2, ochratoxin A, Zearalenone) on porcine and mouse oocyte maturation. The results showed that all of these mycotoxins compromised the porcine and mouse oocyte maturation. The authors conclude that porcine oocytes were more sensitive to Aflatoxin B1, Deoxynivalenol, ochratoxin A and Zearalenone than mouse oocytes except HT-2 toxin. The objective of the study is clear and this manuscript contains sufficient new information, although information concerning the method, and interpretation of results shows some weakness. This reviewer only has some specific remarks for the improvement of the paper before its publication in Peer J.

Major comments
1. The authors subject experimental data of oocyte maturation rate to two-tailed unpaired student’s t-test. However, experimental data shown in Figures 1 to 5 have to analyze using one-way ANOVA and the post hoc test. In addition, please add significant markers in Figures.
2. From Figure 1 to 5, the table repeats the same data as the concentration-response curves. Please remove this table, or you can show this table in supplement data.
3. In each part of results, the author descripted “the rate … of oocyte polar body extrusion was lower than …”, but no significant analysis was carried out.
4. Titles of figure 2 to 5 were not matched with the figure legend and results. Please check and rewrite.

Minor comments
Line 45-46: If mycotoxins are “important” in agriculture? Please, revise this lines.
Line 49: Please change “exists” to “exist”.
Line 51-52: What is “mitochondrial permeability transition DNA damage”? Please, revise this lines.
Line 54: Please change “induced” to “induce”.
Line 83: Please change “two” to “twice”.
Line 106: Please delete “purchased”.
Line 109: If “2 to 8mm antral follicles” was used in your study? Please make sure of this. Because 3 to 6 mm antral follicles were usually used.
Lines 221, …: In vivo, in vitro and ex vivo should be written in italic.
Line 211: Please delete the comma.
In Figure 3 and 4, there are radix point after the number of HT-2 and OTA concentration, please revise these figure.


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

Input:
Title: COMPARISON OF THE TOXIC EFFECTS OF DIFFERENT MYCOTOXINS ON PORCINE AND MOUSE OOCYTE MEIOSIS
Review round: 1
Reviewer: 3

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: In the manuscript entitled “Comparison of the toxic effects of different mycotoxins on porcine and mouse oocyte meiosis”, the authors performed a systematic investigation of different concentrations of AFB1, DON, HT-2, OTA and ZEA in oocyte maturation, using both mouse and pig as the in vitro model, focusing on the first polar body extrusion rate.

Overall, the manuscript is well written and technically sound, the results are clearly demonstrated as well. It’s also interesting and significant as this is the first study that systematically compared the sensitivity of mouse and porcine oocytes to AFB1, DON, HT-2, OTA and ZEA for mycotoxin research. However, there are several minor issues based on the current manuscript and comments are outlined below.

1.	In the body, the drug or chemical needs go through several layers of cells to work on oocytes, for example, theca cells, granulosa cells and cumulus cells (when follicle is grown up), and maybe even stromal cells. Authors are suggested to discuss, whether these 5 mycotoxins, AFB1, DON, HT-2, OTA and ZEA, are the final metabolites in vivo?
2.	Please explain why use different maturation medium. It seems mouse oocytes can also be cultured/matured in TCM199?
3.	Please add more details. For example, “from prepubertal gilts purchased at a local slaughterhouse”, name and address; “in a thermos bottle”, temperature?
4.	It is suggested to put all 5 mycotoxins as Keywords (may use “X and X” to decrease the number).
5.	“The most agriculturally important mycotoxins known today are aflatoxins (AF), Deoxynivalenol (DON), T-2, ochratoxin A (OTA), Zearalenone (ZEA)” needs reference(s).
6.	Authors are suggested to carefully go through the manuscript and correct minor grammatical errors, for instance, “effects including reproductive system on animals and humans.”; “previous studies reported that several components of mycotoxins impaired mammalian oocyte quality. However, different effective concentrations were reported in the oocytes of different animal models”.


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

Input:
Title: COMPARISON OF THE TOXIC EFFECTS OF DIFFERENT MYCOTOXINS ON PORCINE AND MOUSE OOCYTE MEIOSIS
Review round: 1
Reviewer: 4

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: There are a few comments for the improvement:
1. The English language should be improved.
2. In “Toxin treatment” of Materials and Methods, the details of treatment were missing.
3. The authors should mention the standard for the “……significantly affected……” of these mycotoxins in Results or Discussion.
4. In “Effects of AFB1 on mouse and porcine oocyte maturation” of Results, the authors described the effects of 100 μM AFB1 treatment in mouse oocytes and 50 μM AFB1 treatment in porcine oocytes, but they mention “Our results showed that 10μM AFB1 affected porcine oocyte maturation instead of 50μM AFB1 in mouse oocytes.” in Discussion. Please explain.
5. Discussion needs to be improved.


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

Input:
Title: PLANT-INSECT INTERACTIONS PATTERNS IN THREE EUROPEAN PALEOFORESTS OF THE LATE-NEOGENE—EARLY-QUATERNARY
Review round: 1
Reviewer: 1

Output:
Basic reporting: Your paper will be pretty important for the paleobotany and plant-insect interactions field of study. It's clear, with good data and relevant results.
Experimental design: You need be more specific about what is your main goal and hypothesis. You have really good data. By your introduction the reader gets the idea that you will just describe the damages, in a qualitative way.
Also, you can improve the description of your analysis.
Validity of the findings: You presented strong results and an interesting discussion. I think you can improve your conclusions when you specify your hypothesis in the beginning.
Additional comments: Despite of the lack of a clear question, I believe that your paper will provide a significant contribution to the study of fossil plant–insect interactions. See my suggestions in the attached document.


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

Input:
Title: PLANT-INSECT INTERACTIONS PATTERNS IN THREE EUROPEAN PALEOFORESTS OF THE LATE-NEOGENE—EARLY-QUATERNARY
Review round: 1
Reviewer: 2

Output:
Basic reporting: Please see attached pdf with all comments.
Experimental design: Please see attached pdf with all comments.
Validity of the findings: Please see attached pdf with all comments.
Additional comments: Please see attached pdf with all 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: PLANT-INSECT INTERACTIONS PATTERNS IN THREE EUROPEAN PALEOFORESTS OF THE LATE-NEOGENE—EARLY-QUATERNARY
Review round: 2
Reviewer: 1

Output:
Basic reporting: I think your manuscript really improved since last review. It's much more clear and direct to the point. I have just some minor suggestions.
Experimental design: Your goal and hypothesis are much clear now. And your methodology properly helps to answer your questions.
Validity of the findings: You have really interesting results. I just have some suggestions to improve your discussion (see document attached)
Additional comments: Despite of my suggestions, I believe that your paper will provide a significant contribution to the study of fossil plant–insect interactions.


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: HOW MANY FISH? COMPARISON OF TWO UNDERWATER VISUAL SAMPLING METHODS FOR MONITORING FISH COMMUNITIES
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript presents data from two different underwater sampling methods (strip transects and line transects) on rocky reefs in the Aegean Sea to investigate the performance of each in documenting associated fishes. I commend the authors on sampling a larger number of stations, however the manuscript could benefit from some additional information, clarity in the methods, and interpretation of the results.

1. Line 39 This sentence would read better if “last” was replaced by past.

2. Line 40 I suggest re-wording this sentence for clarity, e.g., Selecting the most suitable sampling method…

3. Line 46 The majority of relevant literature uses the abbreviation “UVC” (underwater visual census) instead of UVS. In fact, you use UVC in line 349. It might be worth adopting this abbreviation for consistency.

4. Lines 39 – 52 This study deals with two different underwater visual assessment methods. I would suggest keeping the focus here on underwater methods rather than discussing non-observational techniques. For example, the five techniques in paragraph two could be discussed in more detail (pros and cons).

5. Line 58 The authors need to explain why these two methods were selected over the other three for this study.

6.  Line 70 While this might be an assumption, I don’t think anyone really assumes this is the case in reality. Clearly there are species that are difficult to detect as you have pointed out in the subsequent sentences. I suggest that you provide a reference to support this statement and maybe remove the word critical.
 Most studies assume that sampling is not perfect. Replication, transect parameters, and survey method is therefore selected to maximize accuracy and increase the probability of recording the majority of the individuals in the sampling area. Furthermore, it would appear that most of these factors that influence fish detection discussed in the subsequent sentences for strip transects would also apply for line transects.

7. Line 94 Is there an accepted level of precision? e.g., nearest mm, cm, 5cm, etc.,?

8. Line 99 The authors need to discuss the tradeoffs associated with both methods and when each method would be preferred over the other.

9. Line 114 More detail is needed here on the specific aims of the study. E.g., what metrics are being tested? Also, you have a pre-selected group of fish in your study. Is this specific to reef health, fisheries, or another reason?

10. Line 122 How were the stations independent of each other within each site? They appear to be two site-level replicates as there was no replication at a transect level.

11. How were the sites selected and was there any criteria for selection that is important to the study?

12. Line 127 suggest replacing “at a” with “where”
and “off” with “was”

13. Line 133 and 133 Replace “cluster” with “school”

14. The authors need to give more detail on how the two methods were conducted within each station. How far apart were the transects, was there the possibility of one survey influencing the other, was the habitat similar between the two, etc.,

15. Is there a reason why these twenty fish were selected? Please note this.

16. For a reader that is not familiar with the “line method” it would be useful to provide some additional information on the process of conducting this technique. How does the observer use a measuring tape to estimate the distance for one fish without influencing nearby fish behavior? How does the observer deal with mobile fish?

17. Line 220 What are the variance estimates for each of the values? Is site a factor in the model? I would assume that variables associated with each site (habitat complexity, water visibility) would influence the detectability?

18. Line 220 Why are there not figures for all species (Figure 2)?

19. Line 225 – 229. Can you confidently state that detectability for each of your species is dictated by active avoidance? Could this be linked to feeding behaviour, mobility, etc.,

20. Line 232 Was D. vulgaris observed in both methods within the same sites? For Figure 3, it would be informative to know if occupancy was similar between methods within a site.

21. For clarity, use “species” instead of “cases”

22. Line 249 It is unclear why you have presented two tables (Table 3 and 4) and a figure (Figure 5) for fish density, and why you have presented CI on one and SE on the other.

23. Line 269 How were the stations selected for analysis inclusion? Line 271 It would be useful to include this into the supplementary information. While the figure may benefit from less stations, all stations should be included into a formal analysis.

24. Line 272 It is unclear how you came to the conclusion that the two methods present similar species composition. What analysis supports this statement? The study should include some analysis to support these statements (e.g., ANOSIM).

25. Line 277 This result appears out of context as it is not related to the aims of the study. I suggest that you remove this.

26. Line 285 This suggest that a width of 5m provides perfect detectability. Obviously this would vary depending on the species of fish and water visibility, and not the fish community.

27. Line 288 It is unclear what “on the line” means

28. Lines 289 – 292 While shy fish may flee the observer, if they were originally within the bounds of the transect parameters then shouldn’t they still be counted? It shouldn’t matter that they then swam outside the transect or that they fled a greater distance. Fish observers are generally looking and recording fish ahead of them within the transect, and not directly to the sides of them. In addition, I would assume that a species reaction to an observer would be consistent for both methods?

29. Line 297 transect widths are often dictated by the targeted fish species (size, behaviour, cryptic nature) and environmental variables. Often the width of the transect cannot just be extended. Factors like water visibility and habitat architecture can mean that transect widths often need to be kept narrow.

30. Lines 300 – 306 I would assume that fish behavior and shyness is consistent among methods?

31. Line 303 “>0” this is not very informative

32. Lines 306 – 311 This appears to contradict itself. Especially as the peak (0.7 – 2.2m) is within the strip transect dimensions

33. Lines 329 – 337 An important aspect that needs to be stressed for surveying fish is time. Time equals money, but is also a significant limitation when using scuba. This would result in less bottom time, which would reduce the number of sites/replicates. What is the difference in sampling time for the two methods?

34. Lines 347 Please provide some references to support this statement

35. Lines 344 – 353 There are many tradeoffs associated with this. It would be interesting to know how long it took to complete each method as this is always a concern for someone designing a sampling protocol.

36. Line 371 this is repetitive

37. Line 373 In addition, a single strip transect can be conducted with two different widths to account for different fish species. A larger width for larger, mobile, shy species, and a narrower width for small, benthic, cryptic fishes.
Experimental design: 38. There is no replication at a station level. There is only one transect at each station for each method

39. It appears that a large proportion of the differences between the two methods could be attributed to the different sampling areas (see lines 283 – 285, 306, 312 - 328). Strip transects had a width of 5m (area 375 m2) while line transects has a width of 16m (area 1200 m2). A standardised sampling area for both methods would have reduced the bias between the two. While I appreciate that the sampling cannot be repeated, it might be useful to test the proportion of variance attributed to sampling area.

40. It appears that this study pooled all the stations from each of the two methods together to make the comparisons. To accurately assess the two methods I would assume that a pair-wise design would be more suited and account for differences among sites.

41. Some basic statistics are missing from the results. E.g., line 250, 258, and for community comparisons (nMDS). Line 274, the authors could use a SIMPER analysis to show what species are resulting in the observed difference. This could then be linked back to the distance sampling results. The authors should provide support for these statements.
Validity of the findings: 42. It is unclear how much of the variation between the two methods is driven by the actual observational methods or the difference in the surveyed area (see comment 39). In addition, factors like time need to be considered in order to make a case that one method is preferable to another. The conclusions appear to suggest that two methods suit different groups of fishes (cryptic vs conspicuous) see lines 33 – 35, however it appear that most of the species in this study could not be categorized as cryptic. The authors should recommend the method that suits the fish group that was targeted in this study best.
Additional comments: 43. Overall, more information is needed in the table and figure captions.
In addition, Figure 6 could be labeled differently to better illustrate the data. Many of the symbols look similar. E.g., instead of symbols on the plot, just have the site number. These can be colour coded to represent the observation method. It is also not obvious what the lines and circles represent.