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: REASSESSING PUBLIC OPINION OF CAPTIVE CETACEAN ATTRACTIONS WITH A PHOTO ELICITATION SURVEY
Review round: 1
Reviewer: 2

Output:
Basic reporting: In general, the use of English language, grammar and sentence structure was very good in this paper. The referencing itself was well organised and extensive, and the raw data was provided (although analyses would be very hard to replicate as there are many values without explained units or how they were calculated).

The style of the paper needs to be significantly improved. I found many examples of poor scientific writing style, where for example emotive or imprecise phrases were used (e.g. “…identified as not keen to visit such attractions roughly correlates to…”, Line 444). This was also linked to the tone behind the writing, which I felt had an agenda to discussing the literature and results in light of opposing captive cetacean practices (e.g. “Those promoting the education, conservation and welfare benefits of SWTD… should… take note”, Line 391).
It was my understanding that although the authors self-identified as “anti-captivity”, they wanted to avoid the bias seen in previous studies and conduct a balanced study on the topic. I have made suggestions using the comment boxes on the PDF where I believe that counter-explanations for results should also be provided. It may sound like I am on the pro-captivity side (I assure you I’m not, I work on both “sides” because I focus on the animal’s welfare), but I have played Devil’s Advocate and made these suggestions in order to help the authors produce a clear, well-balanced paper where the results speak for themselves. As it is, I feel that the study’s interesting results get a bit lost among the frequent reference to the controversial debate and purported claims.

The authors clearly explained the background and associated issues of survey studies and methodologies, which will be appreciated by the less knowledgeable readers.  I felt there was literature lacking regarding the measurement of dolphin welfare in captivity, for which there have been a lot of studies published over the last 5 years. Farm animal welfare techniques allow us to understand what animals are feeling, and focus on “animal-based measures”, i.e. the behaviour, health etc of the animal. Although not the main point of this study, such studies on dolphins should be listed to give the readers an idea about what dolphin welfare is and how it can be recognised.

To summarise the findings on dolphin welfare so far: their cognitive bias has been measured, showing that some were in good and some in poor welfare, and that it was related to their social bonds. They have been found positively anticipate non-food trainer interactions, and that social play is a good welfare indicator. There has also been a full assessment proposed which can objectively measure dolphin welfare. In light of the authors’ comments on “research by those working at captive cetacean attractions”, although these publications do indeed usually include an investigator from a dolphin facility, this is expected as the research needs long-term access to the dolphins. There are nearly always collaborating non-industry scientists and the research is peer-reviewed so can be considered objective.

Brando, S., Broom, D. M., Acasuso-Rivero, C., & Clark, F. (2017). Optimal marine mammal welfare under human care: Current efforts and future directions. Behavioural processes.

Clegg, I. L. K., Rödel, H. G., Boivin, X. & Delfour, F. (2018). Looking forward to interacting with familiar humans: dolphins’ anticipatory behaviour indicates their motivation to participate in specific events. Applied Animal Behaviour Science. 22, 85-93

Clegg, I. L. K. & Delfour, F. (2018). Cognitive judgement bias is associated with frequency of anticipatory behaviour in bottlenose dolphins. Zoo Biology, 37, 67-73

Clegg, I. L. K., van Elk, C. E., & Delfour, F. (2017). Applying welfare science to bottlenose dolphins (Tursiops truncatus). Animal Welfare, 26, 165-176.

Clegg, I. L. K., Rödel, H. G. & Delfour, F. (2017). Bottlenose dolphins engaging in more social affiliative behaviour judge ambiguous cues more optimistically. Behavioural Brain Research, 322, 115-122.

Clegg, I. L. K., Borger-Turner, J. L., & Eskelinen, H. C. (2015). C-Well: The development of a welfare assessment index for captive bottlenose dolphins (Tursiops truncatus). Animal Welfare, 24(3), 267-282.

Makecha, R. N., & Highfill, L. E. (2018). Environmental Enrichment, Marine Mammals, and Animal Welfare: A Brief Review. Aquatic Mammals, 44(2), 221-230.

Serres, A., & Delfour, F. (2017). Environmental changes and anthropogenic factors modulate social play in captive bottlenose dolphins (Tursiops truncatus). Zoo biology, 36(2), 99-111.
Experimental design: The research described in this paper is well-designed and executed, and certainly within the scope of the Journal. It addresses the need to understand tourist opinion on the subject in this area of the Caribbean, given the recent law changes and proposed developments. It also has wider implications for understanding general public feeling to captive dolphins and killer whales, although I would suggest that the authors acknowledge more clearly the limitations regarding how representative their results are of the general population. The methods were described clearly and thoroughly, with only a few comments where I thought they could be clarified or rephrased. The surveys were carried out ethically and a good sample size of respondents was obtained.

I also do not understand why there were two figures made available to me showing the 6 photo grid: one was Fig.S1, which was mentioned in the text, and then the other was a similar grid with slightly different photos and the child’s face blacked out, but it was not mentioned in the text. This file was labelled: “cc_photo_representatives”. Could you clarify its purpose?
Validity of the findings: The dataset itself is extensive and was treated appropriately in preparation for analyses. Suitable statistical tests were used for the analysis and were in line with other similar social science work. I commented on the p-value reporting, where I don't see the need to report the different values below 0.001 (simply put p<0.001), and there was one instance where the p-value seemed to have been used to discuss effect size, which should be corrected.

In my opinion, the discussion section has a good foundation but much work is needed to improve the style and make the discussions more well-rounded. Alternative explanations for the findings should always be discussed, and I felt that again the tone was leading towards those with “anti-captivity” opinions. The majority of the readers of this paper won't have strong pro or anti captivity opinions, and the repeated statements bringing up the debate won’t lend to their engagement and appreciation of the paper. At the moment, the flow is disrupted and your valuable findings are being lost in translation because they are constantly being framed within this debate. If you write objectively and scientifically, where all inferences are backed up by peer-reviewed research, your results will have a much larger impact.

A few areas of the discussion would really benefit from expansion, and I have commented specifically on these in the PDF. Again, I think it’s important to mention the progress that is being made into measuring cetaceans welfare, where last year a study found that some dolphins in a group were objectively in good welfare in captivity, as measured through their cognitive bias. Given that your respondents often did not support SWTD on welfare grounds, how might new welfare research impact this? I realise this is not the main discussion of the paper, but I think the discussion will really benefit from including studies from adjacent disciplines, as this is what is likely to be informing the tourists’ responses.

Further discussion on the reasons for the different findings for killer whales and dolphins would also be valuable, as I think this is one of the most interesting results. Smaller dolphins (e.g. Tursiops) are thought to be more adaptable and fare better in captivity than killer whales, mainly due to their less aggressive tendencies, their fission-fusion groups (as opposed to rigid family structures), and their smaller size.

As mentioned earlier, the limitations of the research should be better outlined, and speculation over the findings should be written as such and positioned appropriately- for example, the current last sentence of the discussion negates the study’s approach, should be rephrased more cautiously and put earlier on when evaluating the general methodology.
Additional comments: This study looking into the opinion of TCI tourists to captive cetacean facilities fills a current gap and will contribute to our general understanding of the public’s opinion into this practice. The methods were appropriate and well-thought out, well executed and the data was handled correctly. The use of English and grammar was very good, with some comments on parts that need clarification, but more importantly the authors need to make major improvements to write in a more scientific style throughout the paper. They should focus on writing a well-rounded, balanced study of this topic, where arguments and counter-arguments are given for each point, where appropriate of course. In this way, the flow of writing will be improved and the paper’s results will reach a wider audience and be more readily accepted. I hope the authors decide to make the revisions and resubmit.


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: REASSESSING PUBLIC OPINION OF CAPTIVE CETACEAN ATTRACTIONS WITH A PHOTO ELICITATION SURVEY
Review round: 2
Reviewer: 1

Output:
Basic reporting: A couple of minor suggestions for the introduction:

For the introduction Miller et al., 2013 is used as evidence that dolphin shows and interaction programs gave educational and conservation benefits. However, there was no statistically significant difference between those tourists who had actually viewed or interacted with dolphins and the (control) group of park visitors that had not, in terms of knowledge, attitudes towards conservation or conservation intentions - therefore being able to see captive cetaceans actually had no observable effect on education or conservation-oriented behavior. It is more likely that changes in awareness were due to signage and other non-animal materials that tourists were exposed to at the park, rather than the animals/animals shows per se.

Jiang et al., 2007 is used as a citation (in the introduction & discussion) that marine parks are educational, although the authors say that they tested whether tourists were "aware of educational opportunities" or "whether they felt" that they had been education, but did not test whether knowledge had increased. It's a subtle difference, but an important one.

Wild captures for marine parks, especially in China and Russia are rather larger than outlined in the introduction, e.g. this hot off the press story:  https://www.reuters.com/article/us-china-marineparks-insight/tidal-wave-of-chinese-marine-parks-fuels-murky-cetacean-trade-idUSKCN1M00OC
Perhaps quantify the huge number of facilities in China that are opening, and being stocked by wild captures?

Denham & Parsons (in Tourism in Marine Environments, in press) has a recent survey of attitudes to cetaceans in captivity, including by types of facilities (primarily US & India participants - if you contact Whitney or Chris they could probably supply you with a copy of the paper).

The added Clegg et al. studies are very controversial - they have been cited as evidence that dolphins "are happy" and show signs of great welfare by have been heavily criticized because of over-interpreting results. For example, the studies to show anticipatory behavior towards trainers - as is seen in many domesticated animals - but there is a big gap between this and saying that they have good welfare or "are happy" as was stated in the press release for this paper.

One good measure of welfare is mortality rates, it might be worth mentioning the Jett and Ventre found that captive orca mortality rates were poor compared to wild populations https://onlinelibrary.wiley.com/doi/abs/10.1111/mms.12225 . Might be worth inserting this study as it has thoroughly reviewed science.

Comparisons of bottlenose dolphin mortality to wild populations are rather controversial at the moment as the best-studied wild population for mortality rates is not doing well (because of pollution, oil spill impacts etc etc), so saying that captive animals do as well as Sarasota dolphins (or starving, so to go extinct southern resident killer whales) is faint praise indeed. It's like comparing human health against a control population from Haiti...

Line 826: "Big Changes at Sea Sworld. "
Experimental design: No further revisions suggested.
Validity of the findings: No further revisions suggested.
Additional comments: No further revisions suggested. Really interesting 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: REASSESSING PUBLIC OPINION OF CAPTIVE CETACEAN ATTRACTIONS WITH A PHOTO ELICITATION SURVEY
Review round: 2
Reviewer: 2

Output:
Basic reporting: This has been improved with the author's revisions, thank you.
Experimental design: Methods have been made clearer.
Validity of the findings: Conclusions have been toned down, and the findings better aligned with the literature, thank you.
Additional comments: Thank you for your revisions and your responses. I find the manuscript a lot clearer, and the discussion much better.

I still have some comments- added directly onto the manuscript- on the use of language and also regarding a few statements where I still would suggest toning down to make the points more objective, and wouldn't be happy recommending publication until they are altered.

You have done a great job so far with the revisions so I am confident you can amend these last few things!


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: REASSESSING PUBLIC OPINION OF CAPTIVE CETACEAN ATTRACTIONS WITH A PHOTO ELICITATION SURVEY
Review round: 3
Reviewer: 1

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


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

Input:
Title: REASSESSING PUBLIC OPINION OF CAPTIVE CETACEAN ATTRACTIONS WITH A PHOTO ELICITATION SURVEY
Review round: 3
Reviewer: 2

Output:
Basic reporting: All fine- see previous reviews.
Experimental design: All fine- see previous reviews.
Validity of the findings: All fine- see previous reviews.
Additional comments: I agree with all the last changes you made, and applaud you for your diligence in improving 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: CHONDROGENIC DIFFERENTIATION OF ADIPOSE-DERIVED MESENCHYMAL STEM CELLS INDUCED BY L-ASCORBIC ACID AND PLATELET RICH PLASMA ON SILK FIBROIN SCAFFOLD
Review round: 1
Reviewer: 1

Output:
Basic reporting: Poor English
Experimental design: Well presented
Validity of the findings: It is novel
Additional comments: The manuscript entitled “Chondrogenic differentiation of adipose-derived mesenchymal stem cells induced by L-ascorbic acid and platelet rich plasma on silk fibroin scaffold” is a poorly written manuscript. It is riddled with syntax errors and spelling mistakes (some of them have been highlighted in the minor changes) which makes it difficult to understand this manuscript. However, this manuscript has potential data which can be published, provided authors correct this manuscript’s English and incorporate following Major and minor changes.
Major questions:
1)	All growth curves should be plotted as % viability than just optical density (OD) values.
2)	ADSC differentiation to chondrocytes must be validated by gene expression studies for markers of chondrocyte differentiation (like: collagen II, Runx2, and collagen X). If these results are in line with Alcian Blue staining, it will be a solid validation for differentiation.
Minor comments:
Few examples of spelling errors:
The MSC characteristics were plastic adherence, spesific cell surface marker expression using flow cytometry analysis, and multipotency test for spesific mature cell differentiation (adipocytes, chondrocytes, and osteocytes) by extracellular matrix staining- Spelling is wrong and sentence makes no sense.
Example of Syntax error:
Articular cartilage is avascular tissue, which is different from other connective tissues with the absent of nervous and lymphatic system. Please rephrase this statement like- Articular cartilage is avascular tissue, which is different from other connective tissues due to absence of nervous and lymphatic system.
Clarification:
Figure 5- Scaffold was made from 12%w/v silk fibroin and had 500μm pore size (unpublished data)- ???


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: CHONDROGENIC DIFFERENTIATION OF ADIPOSE-DERIVED MESENCHYMAL STEM CELLS INDUCED BY L-ASCORBIC ACID AND PLATELET RICH PLASMA ON SILK FIBROIN SCAFFOLD
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript entitled "Chondrogenic differentiation of adipose-derived mesenchymal stem cells induced by L-ascorbic acid and platelet rich plasma on silk fibroin scaffold" reports an improved method using specific concentration of L-ascorbic acid and Platelet rich plasma to stimulate Adipose derived stem cells toward chondrogenic differentiation. I believe the manuscript still requires some minor revision before further consideration for publication.
Experimental design: The experimental design and methods used in this manuscript are enough for publication.
Validity of the findings: Overall, this manuscript demonstrates the ability of Silk fibroin to induce Adipose derived stem cells differentiation in the presence of 50μg/mL of L-ascorbic acid or 10% of Platelet rich plasma induction medium. The methods of assay are sound, the use of in vitro model is adequate, and the reported data appear to make the case that the L-ascorbic acid or Platelet rich plasma play a key role in chondrogenic differentiation.
Additional comments: General Comments for the author:

1.	There are grammar errors in the manuscript and the tenses are confused. Therefore, the manuscript should be thoroughly edited.
2.	Figure 13 which shows Graph of glycosaminoglycan (GAG) content in ADSC cultured on scaffold is 50μg/mL L-ascorbic acid. Whereas the authors have mentioned only 50µg in the text? Please explain it.
3.	Statistical analysis are needed for the Figure 03, 04, 09, 10, 11, 12, and 13. The significant difference in each groups should discuss in the “Result section” and the symbol should be mentioned in each “Figure and Figure caption section”.
4.	The authors mentioned pore size “500μm” is Figure 05, 06, and 07. However, there is no data in the manuscript that can show the pore size is 500μm. The authors need to add the data or remove them from the manuscript.
5.	In “Figure caption section” more detail description are needed to add for making clear easily follow.
6.	I advise the authors to correct the grammatical errors because there are a large number of grammatical mistakes or odd turns of phrase, and too many for a reviewer to list.


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: CHONDROGENIC DIFFERENTIATION OF ADIPOSE-DERIVED MESENCHYMAL STEM CELLS INDUCED BY L-ASCORBIC ACID AND PLATELET RICH PLASMA ON SILK FIBROIN SCAFFOLD
Review round: 1
Reviewer: 3

Output:
Basic reporting: Barlian et al show that culturing adipose-derived mesenchymal stem cells on silk fibroin scaffold along with L-ascorbic acid or platelet rich plasma induced chondrogenic differentiation. The multipotency of the cells was confirmed by staining for adipocyte, chondrocyte, and osteocyte markers. The authors analyze the morphology and proliferation of these cells over multiple days.

Although the authors present a relevant study useful in tissue engineering and clinical applications, unfortunately the current manuscript severely lacks novelty, diligence, and quality of the write-up.  Owing to numerous grammatical errors, spelling mistakes, incoherent writing, and lack of adequate experimental design, the study is not suitable in the current form for publication. If English is not the native language of the authors, it is highly desirable to get the manuscript corrected by a colleague.

In addition to major concerns regarding grammatical/spelling errors, lack of details about replicates, and non-rigorous interpretation, following are some of the minor concerns:
1.	In addition of staining, it would be useful to confirm the differentiation status using gene expression study.
2.	In Figure 1, Y-axis is not labelled. It is not mentioned how the gates were decided or what was the control used. In panel C, the 61.33% positivity for CD105 is confusing. Panel C is not labelled properly.
3.	Figure 2: It would be useful to show the staining when differentiation condition was not included. Scale bars are missing. The label D is placed on panel C.
4.	Figure 3: For all the graphs, inclusion of trendline is distracting. Was the starting number normalized? In figure 3 and 4 some values are high at day 1 itself. It is desirable to normalize the value and present it as %. The significance needs to be calculated.
5.	The conclusions made from SEM images are conjectures. It is difficult to agree to the claim that monolayers and aggregates are two distinct populations.
6.	Authors need to clearly show that culturing cells on scaffold had an advantage with respect differentiation.
7.	The cell number used is inconsistent throughout.
8.	Was the pore-size constantly 500um? Was there a range?
9.	Some selected issues with grammar/spelling are:
•	Absence instead of absent (line 48)
•	Lack of ‘the’ at many places
•	Line 62-63, 66 needs fixing
•	Delete ‘be’ in 71, 72
•	*Mammalian (76)
•	Many sentences in methods section written in future tense
•	*Specific (114, 157)
•	*Supernatant (130, 132)
•	Inconsistency in space after units
•	Inconsistency when writing decimals (comma/periods)
•	*Overcome, *Damaged (329)
•	*inconsistent (340)
•	*Stationary (365)
Experimental design: The experimental design lacks novelty The data is not robust and lacks several controls. The number of replicates is not explicitly mentioned. Conclusions are factual observations and lack inference. The article fails to match the minimum quality of professional English expected. The references are inadequate.
Validity of the findings: Some conclusions require further confirmation of observations using additional experiments such as gene expression analysis. The proliferation assay data is not sufficient to justify the claims made.
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: CHONDROGENIC DIFFERENTIATION OF ADIPOSE-DERIVED MESENCHYMAL STEM CELLS INDUCED BY L-ASCORBIC ACID AND PLATELET RICH PLASMA ON SILK FIBROIN SCAFFOLD
Review round: 2
Reviewer: 1

Output:
Basic reporting: Article has potential, but still written in a horrible English. It has to be corrected before it is accepted
Experimental design: ok
Validity of the findings: no comments
Additional comments: This manuscript is a potential one. However, it is written in a horrible English. Some of the mistakes have been corrected by the authors but still it needs major revision for its English.
Some of the examples are highlighted below:

Abstract line 25: Biocompatibility and cytoxicity evaluation was done using MTT assay to optimize silk fibroin concentration and pore size.
Cytotoxicity spelling is wrong.
Abstract: Line 59: The result showed that the ADSC could adhere on plastic, express spesific cell surface markers (CD73, CD90, dan CD105), and be differentiated into three types of mature cells.
Specific spelling is wrong.
Abstract: line 60-63: As the result, silk fibroin scaffold made from 12% w/v concentration formed 500µm pore diameter (SEM analysis), is shown by MTT assay to be biocompatible and facilitate cell growth.
It should be: As a result.


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: INFLUENCING FACTORS AND HEALTH RISK ASSESSMENT OF MICROCYSTINS IN THE YONGJIANG RIVER (CHINA) BY MONTE CARLO SIMULATION
Review round: 1
Reviewer: 1

Output:
Basic reporting: English could be improved, especially in the introduction, to enhance the flow of the manuscript.

Basic structure is ok, figures and tables are clear.
Experimental design: I cannot judge the quality or interpretation of the statistical analyses and the risk assessment part, as this is beyond my expertise. Having said that, I find the approach taken an interesting one.

Some comments on the parts that I could review:

1) The analytical method employed is not very specific, it only relies on retention times. As seen in Figure 1, there is a retention time difference between MC-LR standard and what is assigned to be MC-LR in a sample. As the other two compounds show no retention time shift, additional data (e.g. standard addition of a sample) should be taken to show that MC-LR is correctly identified. As the data are shown now, the last peak in figure 1B might as well be another MC. In addition, I would like to see some more information on the analytical method, e.g. recovery and limit of detection/quantification.
Validity of the findings: 1) MC-RR and MC-LR occur in similar concentrations. MC-RR is generally acknowledged to be about ten times less toxic than MC-LR (confirmed by authors in line 196). Therefore, it is surprising to me that the authors find that MC-RR poses the highest health risk. This needs to be either explained or rectified. In the abstract, it should also made clear which health risks (carcinogenic or non-carcinogenic) are discussed.

2) The correlation of MCs and environmental factors is discussed, but interpreted as causation (e.g. line 342). This should not be done! Phytoplankton is known to influence pH (dense blooms increase pH) and DO (dense blooms enhance the daily DO fluctuations). So in these types of study, causation can not be proven, at best correlation can be identified.
Additional comments: Please see the attached pdf for additional small 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: INFLUENCING FACTORS AND HEALTH RISK ASSESSMENT OF MICROCYSTINS IN THE YONGJIANG RIVER (CHINA) BY MONTE CARLO SIMULATION
Review round: 1
Reviewer: 2

Output:
Basic reporting: Use of the English language should be improved to ensure your international audience can clearly understand your text. I suggest you have a native English speaking colleague review your manuscript, in particular the discussion section. In this section it is difficult to follow the development of ideas and arguments. Some examples where the language could be improved include lines: 43-44, 104-105, 161-165, 178-187, 226, 323-326, 328-331, 332-338.
The references cited are from academically appropriate sources, mainly reviewed journals. However, it is important to avoid citing indirect references. The main problem with the references in this paper is that many of them are not accurate or relevant to support the stated argument. Some examples where references lack relevance and may be replaced by more accurate ones include lines: 45, 46, 54, 112, 118, 309, 311-312, 314.
Format of in-text citations and references should be also revised. Some examples: lines 54, 61, 211. In particular, the reference list should include the full list of authors with initials.
The structure of the article conforms to the standard format suggested by the journal.  However, I suggest that section “3.1 Analysis of MCs by HPLC” (lines 209-215) be included in sub-section “2.4 Determination of MCs” within section “2. Materials and Methods” as it describes the conditions and not the results of the analyses.
Figures are relevant to the content of the article and they have sufficient resolution. In the axis labels, please consider writing the units in brackets, i.e. (µg  L-1) instead of using backslash-unit  “/µg  L-1”. In the description of Figure 2, please consider clarifying that TMCs is the sum of individual totals (intra and extracellular) MC-LR, MC-RR and MC-YR. For figures 3, 4 and 5 please see specific comment in the manuscript (line 260).
Regarding the tables, in general they are clear and well described. When possible, It would be helpful if the author showed the monthly microcystin concentration with the associated standard deviation. Please see some specific comments in lines 221 and 260 of the manuscript.
Regarding the data, I thank you for providing the raw data; however, your supplemental files need more descriptive metadata identifiers to be useful to readers. For example, for supplemental data No. 1 it would be useful if you identified the data set by monitoring station. Also, in supplemental data No. 2, it is important that you write the dates when the environmental records were taken.
Experimental design: This research is within the Area of Environmental Sciences; as such, it is within the aims and scope of the journal. In relation to the research question, the paper clearly defines the research gap.
Regarding the research gap, this research is relevant and meaningful for the geographical study area. It contributes information on the presence, concentration, temporal variability and risk assessment of algal toxins (microcystins) in a river which is the source of water for the city of Nanning. These types of studies, where concentrations of algal toxins are associated to environmental factors, have been carried out worldwide. In this case, the importance lies in its local value, as it seems from the international literature that it is the first time that these types of toxins and their risk to human health are evaluated in this area.
In relation to the performance of the investigation, this investigation addresses two main ideas. The first idea is the identification and quantification of three types of microcystins (LR, RR and YR) in river water and the evaluation of their temporal variability in relation to environmental factors such as water temperature, pH, etc. The second idea of this paper is related to evaluating the risk of the presence of these toxins on human health by using a simulation technique (Monte Carlo Simulation). In relation to the first idea, the article (with some methodological weaknesses described below) demonstrates the presence of these toxins in water and its association with environmental parameters. The main point to be improved in this idea is the lack of clear acknowledgment by the authors that algal toxins are produced by algae and consequently the concentration of toxins in water depends mainly on algal abundance which, in turn, is regulated by environmental factors. Even though there is some association between toxin concentrations and environmental factors (reflected in the correlation coefficient), these factors are not necessarily the cause of the variability of toxins in water but mainly factors that regulate algal growth. It would improve your introduction and discussion if you acknowledge that the abundance of toxins depends on the presence and abundance of toxic strains within the cyanobacterial population and that environmental factors are important in controlling expression of the toxin synthetase genes.
 A more rigorous investigation should have included some indicator of algal abundance (or biomass) such as chlorophyll-a concentration or algal cell counts. To evaluate how environmental factors affect the toxin levels in a natural environment, it would be more accurate to correlate for example the toxin quota (i.e. the concentration of toxins per cell or per unit of biomass) with the environmental factor. Also, data on the type of algae (genus) present in the water would have been useful, in particular to support some arguments in the discussion section.
If no indicator of algal biomass was measured, then this should be clearly acknowledged and considered in the discussion. Please see comments in lines: 321-331, 334-336, 342.
The second idea of this paper is related to evaluating the risk of the presence of these toxins on human health by using a simulation technique (Monte Carlo Simulation). As this is not my field of expertise, I cannot comment on the technical quality of the investigation regarding this point. However, I cannot help wondering whether this assessment is necessary considering that the concentrations of toxins (MC-LR) found in the river water are well below (range: 0.0341-0.2663 µg L-1) the guideline value suggested by the WHO in drinking water (1µg L-1) and by the USEPA (ten-Day Drinking Water Health Advisories : bottle-fed infants=0.3 µg L-1, school age children and adults=1.6 µg L-1). Maybe some more background and discussion clarifying this idea would be helpful. Lastly, there are no ethical issues to be addressed in this research.

Regarding the methods, as I mentioned earlier, the paper addresses two main ideas which are interconnected; however, each of these requires a different methodological approach. Regarding the methodology of the first idea: both sampling and water analyses need to be better referenced (please refer to comments in the manuscript). I highly recommend the authors to contact the laboratory which performed the analyses and ask for the methodology and cite the methodology. The cited references are not relevant to describe the methodology. The methodology for microcystin detection, on the other hand, has been described in greater detail. Nevertheless, I recommend the authors to have the English revised as it difficult to follow. Also, the reference cited for microcystin detection is not in the reference list. Please see specific comments in the manuscript (lines 112, 115 and 118).
Regarding the statistical analyses performed: The use of Pearson’s correlation and linear regression requires a validity check for certain assumptions (e.g. linearity, normality). I recommend the authors to mention whether they checked the assumptions or whether they performed some kind of variable transformation before applying the statistical methods. In general, environmental variables do not present normal distribution.
Regarding the methodology of the second idea (Monte Carlo Simulation): as this is not my field of expertise, I cannot comment on technical details of the method. However, the description of the methods (line 137-201) is difficult to follow mainly due to faulty English and typos.
Validity of the findings: I thank the authors for providing the raw data.  A valuable aspect of the microcystin data analysis is the use of triplicates to calculate a monthly value. However, the data concentration presented in Fig. 1, Table 1 and the supplemental material No. 1 have some inconsistencies. First, data presented in supplemental data No. 1 do not match the data presented in Fig. 1 and Table 1. Microcystin concentration values in the supplemental data are 1000 times higher than those presented in Fig. 1 and Table 1.
Second, the concentrations of microcystins presented in Fig. 1 and Table 1 are below 1µg L-1. The detection limit of the technique used by the researchers has not been mentioned; however, to my knowledge, the detection limit of microcystins using HPLC-UV is generally 1µg L-1, therefore values lower than 1µg L-1 would not be detectable. I assume the authors did some calculation to account for the concentration step during the pre-treatment of the samples (i.e. they calculated the final concentration value applying a dilution factor). These two problems lead me to believe that there may be a calculation problem. I recommend the authors to verify this.
I also recommend the authors to consider the significant digits when reporting the concentrations based on the precision of the equipment and the inclusion of the SD
This is important, in particular, when comparing concentration levels. It should be clear that the differences between values are not due to the uncertainty of the measurement but due to real differences. As the authors used triplicates for the estimation of the monthly value I would recommend them to include standard deviations. Regarding the discussion and conclusions, they are linked to the original research questions; however, the English should be revised as language misuse makes it difficult to fully grasp the meaning. Please refer to earlier comments and my comment in the manuscript (line 378).
Additional comments: No comment


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 EMERGING VIRAL PATHOGEN TRUNCATES POPULATION AGE STRUCTURE IN A EUROPEAN AMPHIBIAN AND MAY REDUCE POPULATION VIABILITY
Review round: 1
Reviewer: 1

Output:
Basic reporting: I found the manuscript to be written clearly and concisely, the authors provide sufficient citation of previous work, and the figures and tables are easy to read understand.

The hypotheses are clearly stated and justified with prior work with Bd.
Experimental design: Generally, I found this study to employ a unique data collection strategy (measuring age of adult frogs using bone fragments and counting lines of arrested growth), which leads to an interesting study. The statistical analyses and modeling were also clearly presented and justified. All code is provided for review.

I do have some minor questions/comments about the statistical analyses, which can be seen in the provided code, but should be made clear in the main text as well:

1. Line 134: I believe "Sex" should be changed to "Age"

2. Is the history of ranaviral disease a simple binary? (0/1)

3. Was the random effect of source population applied to the intercept, the slopes, or both?

4. Related to the above, I believe table 1 should include estimates of the slope coefficients for the best models, so that the readers can understand trends in the positive or negative direction. Alternatively, these could be provided in the supplement.

5. Line 147: The residual variation was fixed to 1. Is this a convention in the literature? If so, could a citation be provided? If not, how sensitive are the results to such an assumption?

6. Why were only 2 chains used in the MCMC? I strongly encourage at least 3 chains to assess convergence and the lack of divergent likelihood profiles in the sampler.

For the population matrix model simulations, (line 232), could the authors comment on how often it might occur that there is an adult die-off event and there is zero recruitment in the same year? Has this ever been documented for this frog species? It seems like a very extreme event.
Validity of the findings: I do have some concerns with the conclusions of this manuscript, as currently presented in the text.

1. My main concern is that the age structure, which clearly differs between the ranavirosis-positive and negative sites, cannot be directly linked to ranaviral disease, as this is a correlative study. However, no alternative hypotheses or explanations are provided, and not enough information is given about these field sites to adequately assess how clear the link is between ranavirus die-offs, which occurred at least 10 years ago, and current age-structure.

Specifically, the authors allude to a study that shows that ranaviruses are likely present in many sites, but this does not always lead to disease. In other words, ranavirosis has some determinants other than the presence of the virus. Because of this, it leads me to wonder: (1) were ranaviruses ever found at any of the ranavirosis-negative sites? and (2) if so, what differs between these sites that might influence disease and that might, therefore, influence the age-structure of the frogs, independent of the disease?

Due to this issue, I believe the authors should provide sufficiently more detail about their field sites and what biotic and abiotic aspects might differ between sites that could explain the age-structure difference, either in combination with or independently of historical ranavirosis.

In addition, in line 9 of the abstract, the authors state that the populations "differed only in their historical presence or absence of ranavirosis". This exemplifies my point, as, surely, differences exist between sites other than ranavirosis history.

2. My second concern is with the population viability simulations. Lines 165-168 suggest that the authors somehow changed the data from Biek et al. (2002) to substantially increase the egg contribution from very old adults (10 years old). First, I think the authors could clarify this sentence, as I was confused as to what exactly the authors mean. Did the authors assume some sort of linear relationship between age and egg count? How exactly is this different from Biek's work? I bring this up because of the authors' results that environmental stochasticity and disease combine to greatly affect population viability. I'm wondering how sensitive these results are to the authors' assumption of very large egg counts of the very old individuals that die due to virus? I do recognize that the authors do a good job tempering their simulation results (starting line 347).
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: AN EMERGING VIRAL PATHOGEN TRUNCATES POPULATION AGE STRUCTURE IN A EUROPEAN AMPHIBIAN AND MAY REDUCE POPULATION VIABILITY
Review round: 1
Reviewer: 2

Output:
Basic reporting: Overall the article does wonderful job of meeting criteria under "Basic reporting". I've noted a few specific instances where this could be slightly improved:

Line 16: remove the extra “of” in the middle of this line.
In line 22, please rephrase your meaning of “selection for increased juvenile survival” or add a bit of explanation/ context. This is a bit confusing as selection for traits can result in increased juvenile survival, but survival is typically not a trait that can be selected for. To further this point, study objectives stated in lines 72-78 do not suggest that selection FOR juvenile survival was examined, but rather that things affecting juvenile survival (body size, growth rate) were examined.
Line 50: I think there are some more recent studies that demonstrate ~ 100% mortality at the population level. I believe the following literature may be useful:
•	 Wheelwright NT, Gray MJ, Hill RD, Miller DL (2014) Sudden mass die-off of a large population of wood frog (Lithobates sylvaticus) tadpoles in Maine, USA, likely due to ranavirus. Herpetol Rev 45:240–242
•	Petranka JW, Murray SM, Apple Valley MN, Kennedy CA (2003) Response of amphibians to restoration of a southern Appalachian wetland: perturbations confound post-restoration assessment.
•	Todd-Thompson M (2010) Seasonality, variation in species prevalence, and localized disease for ranavirus in Cades Cove (Great Smoky Mountains National Park) amphibians. Master Thesis, University of Tennessee, Knoxville. http://trace.tennessee.edu/utk_gradthes/665 .
Line 52-53: This statement needs a citation.
Line 95-96: I think there is a grammatical error or a word omitted. Perhaps it should read, “…consistent with ranavirosis SUGGESTED continued disease.”
Line 127: missing “and” after the comma.
Line 160-161: It looks like part of the line of text is missing (the “S” is left off of “Supplementary methods”). Perhaps there was an error during conversion from a Word processing document to a PDF.
Experimental design: Solid experimental design.
The population projection modeling seems like a wonderful way to potentially identify areas or scenarios where populations may be at a greater risk of extinction associated with Rv.
The authors do a great job of explaining the limits of their work (e.g. line 351-355). A couple minor things to address:
(1) Lines 135-137: Looking at Table 1, I believe the modeled interaction is not Sex, as stated in line 134, but rather Age. I think this is likely just a type-o.
(2) I think this article may benefit from a more detailed description of the assumptions the authors make in regards to the disease status of a pool. An important aspect is to discuss if any lab verification (pathology, PCR, other diagnostic techniques) or other methods used to determine that the causal linkage between Ranavirus and symptoms. I believe other amphibian diseases could (perhaps in concert) cause symptoms that are similar if not indistinguishable from Ranavirosis. Providing any additional information about this linkage (or lack thereof) would be useful to clarify what it means for a pool to be “Ranavirosis-positive” – even if it’s just to say that causation is assumed and no testing leading to verification of Rv infection occurred for these study pools. It would be similarly useful to note if any past testing had or had not detected in Rv in the “disease free” pools actually had Rv present? (I.e., detectable yet not causing observable disease)
Additionally, even though no mass mortality events were detected in “Ranavirosis-positive” pools within the last decade, it may be helpful to describe the continued pathogen and disease presence by providing some summary statistics about incidence of disease even if it didn’t result in a mass mortality event. E.g., Frequency of years that diseased individuals been detected? How long since the last detected diseased individual? # of diseased individuals detected? Etc.
Validity of the findings: One quick comment:
Line 246: they reference persistence of Rv in the presence of secondary host species. Were there any secondary host species identified in the study pools? Knowing this would make this comment in the discussion more relevant.
Additional comments: I believe this paper is a great contribution to the literature relevant to understanding how Rv impacts amphibian communities. I really enjoyed reading this as it was well-written and presented timely information.


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: SOIL MOISTURE DYNAMICS UNDER TWO RAINFALL FREQUENCY TREATMENTS DRIVE EARLY SPRING CO2 GAS EXCHANGE OF LICHEN-DOMINATED BIOCRUSTS IN CENTRAL SPAIN
Review round: 1
Reviewer: 1

Output:
Basic reporting: The article generally reflects the existing literature, is written clearly, and has nicely designed graphics. The hypotheses and results are conveyed clearly.
Experimental design: The experiment is well-designed and neatly circumscribed. The research questions are interesting and provide a moderately novel insight into biocrust lichen CO2 fluxes. With two caveats (described below) the investigation is carried out with sufficient technical proficiency. The methods would be relatively straightforward to replicate.

My first methodological concern regards how the dark respiration was measured. I have serious reservations about considering these measurements 'dark' measurements. In my experience, there is a 'dark-acclimation' period of at least several minutes prior to which biocrust carbon fixation appears to continue. I would appreciate if the authors are able to justify the immediate measurement of CO2 flux (with data) or conduct the very simple assay of measuring CO2 fluxes on a diacapsis specimen at different intervals after imposing darkness, for instance, 0,2,5,10 15 and 30 minutes afterward.

My second methodological concern is that the order of the watering treatment and the measurements may actually skew the results toward the desired conclusion. If the authors had measured 5 hours after the watering treatments, or anything other than 1 hour after the watering treatments, is it possible that the results would have been different? This is a speculative question, but if I understand correctly, the watering is done from the top, ensuring that the biocrust lichen was definitely wet immediately after watering. However, the lichen may have been equally dry, or even drier, several hours later, and fluxes may have been suppressed. This consideration might moderate the conclusions presented, and I think somewhat changes the effective experimental design. Can you somehow verify that the 1 day watering treatment actually stayed wetter than the 3 day treatment?
Validity of the findings: Generally the data and statistical analysis appear to be sound. However, the statistics and figures 2 and 3 don't visually correspond very well, and I am concerned that the statistical analysis is not conveyed accurately. Specifically, on lines 198-201 you describe significant differences in the text which really are not apparent from figure 2b. For the most part the intervals seem to overlap pretty substantially, and even the means seem quite close. Can you please verify that you are indeed comparing the values across all dates and times since watering? Additionally, in figure 3, middle panel, I am skeptical that the statistics here represent the same data and analysis as is displayed in the graph. It is hard to imagine how the dark respiration one day after watering is actually different between the two plots. the intervals entirely overlap, and the means are very close.
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: SOIL MOISTURE DYNAMICS UNDER TWO RAINFALL FREQUENCY TREATMENTS DRIVE EARLY SPRING CO2 GAS EXCHANGE OF LICHEN-DOMINATED BIOCRUSTS IN CENTRAL SPAIN
Review round: 1
Reviewer: 2

Output:
Basic reporting: Please see comments for the author
Experimental design: Please see comments for the author
Validity of the findings: Please see comments for the author
Additional comments: This is a well-written research article presenting interesting information about the physiology of a representative lichen of biocrusts. The study of the effect of factors determining biological activity in drylands, such as rainfall patterns, is of the utmost importance, since predictions of climate change include altered precipitation regimes in addition of increasing temperatures.  However, I have a few comments that I would recommend the authors to address:

1. Mean annual precipitation value is stated in methods, but since seasonal variations would be important in the effect of the physiological activities studied, Spring values should be reported, or at least explain why a water amount of 60 mm during the twelve days of study was selected, and/or why you study the differential effect of water pulses of 5 mm/day and 15 mm pulse at three-day interval, in order to know if these are representative of the environmental conditions at the studied site.

2. Evidence has shown that relative air humidity and dew could be an important water input in biocrust, with higher photosynthetic activity early in the morning than in other periods of the day, so timing of measurements should be reported and the possible effect of water vapour adsorption by biocrusts discussed.

3. Although it was specified in methods that the underlying soil was not removed to avoid disturbances, and that, therefore, measurements comprise the fluxes from both biocrusts and underlying soil, I would suggest for further experiments to add other samples in which the thallus of the lichen were removed in order to know if the CO2 exchange measurements are influenced by metabolic activity of bacteria or other organisms living in the adherent soil, or even “control” samples with sterilized soils.

4. Environmental conditions during the experiments are shown in separate Figures, and one of them (temperature conditions) included in Supplementary Fig. S3, so it is difficult to compare data, which are correlated, and it would be convenient to see in parallel. I suggest to combine both data in a figure, which could include in separate axes the different variables, as found in many papers.
In addition, regarding Figure 1, I cannot see values of 50 μmol m−2 s−1 or 2000 μmol m−2 s−1, as stated in the ranges described in the results section, please check it.

5. I was very surprised when I read that there were significant differences between treatments, because a first look of Figure 2A seems to show similar results between treatments, with almost overlapping symbols. It may be that the range of measurements on the axis is too extended, from 0 to 4 μmol m−2 s−1, since your values are close to zero, so I would suggest to change the scale on the axis in order to see the symbols better; for instance to represent data from 0 to 2 μmol m−2 s−1.

6. Evaluation of the results comparing previous results on other lichens and/or other geographic distant places has been discussed. However I found previous reports on Diploschistes diacapsis from biocrusts of another location in Spain (Pintado et al. ), in which photosynthetic activity was also studied regarding microclimatic conditions, that I think must be added and discussed.


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: SOIL MOISTURE DYNAMICS UNDER TWO RAINFALL FREQUENCY TREATMENTS DRIVE EARLY SPRING CO2 GAS EXCHANGE OF LICHEN-DOMINATED BIOCRUSTS IN CENTRAL SPAIN
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: My earlier critique of the experimental design has been adequately addressed.
Validity of the findings: No comment.
Additional comments: Line 48: If you really want to list the water inputs, listing snow is important.

Line 66: You might consider citing Darrouzet-Nardi, A., Reed, S.C., Grote, E.E. et al. Biogeochemistry (2015) 126: 363. https://doi.org/10.1007/s10533-015-0163-7 here. (I am not an author of this study.)

Figure 1: This is just an observation, but the authors might consider exploring it: It may be worth considering that the daily watering appears to have slightly lowered the maximum daily temperature during the hotter days. Respiration is exponentially temperature sensitive, while photosynthesis is not, such that a small difference on warmer days could lead to an outsized carbon imbalance. This might be an alternative pathway by which precip frequency is affecting CO2 fluxes in this system.

Figure 4: The order of the boxes (gold, blue) should not be reversed compared to the other figures (blue, gold). Further, panels should be in the order A, B, C.

Figure 4/line 238-246: This comment is in reference to the significant difference reported in figure 4 a, day 1. Since the statistics represent pairwise differences, but the boxplots are group-level differences, I think reporting in the text the magnitude of the pairwise differences is important. I have a hard time believing that this 'significant' result is substantial, and would like a quantitative estimate of the difference. In the end, I don't think it changes much about the interpretation, but as a minor statistical detail it is important.


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: SOIL MOISTURE DYNAMICS UNDER TWO RAINFALL FREQUENCY TREATMENTS DRIVE EARLY SPRING CO2 GAS EXCHANGE OF LICHEN-DOMINATED BIOCRUSTS IN CENTRAL SPAIN
Review round: 2
Reviewer: 2

Output:
Basic reporting: After re-review this manuscript, I have been satisfied with the answers and use of the recommendations I made in my first review
Experimental design: No comment
Validity of the findings: No comment
Additional comments: After re-review this manuscript, I have been satisfied with the answers and use of the recommendations I made in my first review


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

Input:
Title: ENHANCEMENT OF A PROTOCOL PURIFYING T1 LIPASE THROUGH MOLECULAR APPROACH
Review round: 1
Reviewer: 1

Output:
Basic reporting: The authors used cleat language to describe their design rationales. Figures are well labeled and described, the main text is well referenced.
Experimental design: Methods are described in detail.
Validity of the findings: The findings are valid with robust data presentation.
Additional comments: The purification of GST-tagged T1 lipases suffered from low yield and cumbersome 3-step purification steps. Using rational design, the authors changed the PI value of the GST tag and shortened the purification to two steps, thereby increasing the overall yield quite significantly.

This is a very nice showcase of the power of rational design to improve protein engineering, and fits well with the theme of this journal. I highly support its publication if the following minor concerns can be addressed satisfactorily:

•	Line 219, the subheading should be changed to be more informative.
•	Figures 1 and 2 are not significant enough to be in the main text, I recommend moving to the supplements.
•	Supplemental figures are missing figure captions. I recommend moving supp. Fig. 1 to the main text since it very nicely shows the overall workflow of this paper.
•	Figures 3-5, the gel images should show better contrast for better readability. Lines with different colors should be labeled in the figure legends.
•	On a similar note, font sizes on the X- and Y- axis in the panel (a) of Figures 3-5 should be increased.


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: ENHANCEMENT OF A PROTOCOL PURIFYING T1 LIPASE THROUGH MOLECULAR APPROACH
Review round: 1
Reviewer: 2

Output:
Basic reporting: I think the figure displaying in the paper is not so satisfying, some figures have occupied too much space while providing limited information. Like Figure 2, which I think can be moved to the supplementary data.
Experimental design: No comment
Validity of the findings: No comment.
Additional comments: This manuscript depicted a new protocol for T1 Lipase purification by mutating the GST tag. The English language used throughout the context is clear and professional.  The experiments are well designed and right conclusions are obtained. The idea of changing the PI value of GST tag to improve the purifying process will provide new information for this field. However, I have some concerns about this paper.
1.	Since the purification of T1 Lipase is a well-established method, this paper should put more emphasis on the comparison between the traditional method and the modified one. For example, in the result part, the difference between two strategies should be discussed in detail. And in table 2, why the data of GST-T1 Lipase was adopted from a published paper instead of your own data? I think it will be more persuasive to use your own data.
2.	As far as I know, peptides can be separated using RP-HPLC based on their hydrophobic character. If this is the case, T1 Lipase will still be able to get purified from GST without mutating the tag. What do you think is the advantage of IEC over RP-HPLC for Lipase purification?
3.	In Figure3-4, there are multiple lanes for the same sample, what’s the difference between them?  Parallel samples? It should be stated clearly in the figure legend.
4.	In Figure4, though there was some GST eluted together with T1 Lipase, the yield of T1 Lipase still looks pretty high; the yield should be stated with WT GST.
5.	Quality of gel image is low in Figure3 and Figure4, the ladder is smear.
6.	Figure 2 can be listed in supplementary data.


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: BEADPLEXR: REPRODUCIBLE AND AUTOMATED ANALYSIS OF MULTIPLEX BEAD ASSAYS
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: The authors address the need of having open environment for integrative analysis of data from different instruments.

I think there is a little need of automated population detection in common beads assays but I understand that manual gating in R is cumbersome and clustering is a viable alternative.
However applying clustering algorithm on every single sample is not very transparent or efficient. Also since the default algorithm "clara" uses downsampling such approach is not entirely reproducible.
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: BEADPLEXR: REPRODUCIBLE AND AUTOMATED ANALYSIS OF MULTIPLEX BEAD ASSAYS
Review round: 1
Reviewer: 2

Output:
Basic reporting: * Overall, this paper needs much more thorough editing as there are many unclear sentences and grammar mistakes. For example the sentences starting on line 50, 108, 109 were hard for me to understand. Line 306 should include the word ‘clustering’ rather than ‘cluster’. I found too many such examples to list explicitly.
* The paper should provide more background and context, and cite both the commercial tools currently available for multiplex bead assay analysis, as well as the most similar open source tools for analyzing other types of bioassays, such as cellHTS and bioassayR. If any of those tools can be used for multiplex bead assay data the methods should be briefly compared and contrasted with the methods used here.
* It was mentioned that the examples analyze unpublished data. This data should be included in the R package, or swapped out for already published data, to make this work reproducible. Ideally, the full code and data to produce the examples and plots in the paper should be provided as a supplement, or as part of the documentation for the package.
* Figures 2-4 should include some context: (1) what data is visualized here? (2) What scientific interpretation or information can be learned from these plots?
* Throughout the paper, R functions in this package and other packages are referenced by name only. These should include a description of what the function does, and why it is used. It is essential that users be able to understand why each step was performed in the analysis workflows they perform based on this paper. For example, the use of ‘clara()’ on line 121.
* Please provide more detail on the meaning of ‘forward and side scatter properties’ as used on line 40.
* It found it very helpful for potential users that example R code is included directly in the manuscript, however the code examples don’t have enough context to be understood from the manuscript alone. I suggest adding code comments or a detailed description describing the commands in more detail, including the purpose of each option or setting when non-obvious.
* Since this package makes use of other Bioconductor packages (e.g. flowCore), have the authors considered distributing this via Bioconductor rather than CRAN and possibly providing more integration with related Bioconductor packages? This is just a suggestion, and should not be a requirement for publication.
* All R packages mentioned in the paper should be cited as references.
Experimental design: It was not clear exactly what statistical methods are used for the analysis here, and what the scientific justification for these methods is. The authors should include at least one new paragraph describing the scientific/mathematical purpose of each analysis step, how parameters are chosen, and justifying why this method is used over alternatives. Are any alternative statistical methods ever appropriate here?
Validity of the findings: The paragraph starting on line 119 mentions that finding the right clustering method is 'a matter of trial and error.’ Can the authors clarify why this is, for example explain why making a rigorous choice based on understanding the properties of each method in relation to the experiment would be fundamentally impossible? When doing a trial and error approach, how should the user/reader evaluate the performance and results of one method over another?
Additional comments: The authors report an open source R package for the analysis of multiplex bead assays, which fills a need within the scientific community. The package appears to be well designed, and includes documentation, examples, and unit tests. Substantial work is needed to clarify the manuscript in a way that will make it easy to understand for readers and potential users. Additionally, the paper seems to present an analysis of novel experimental data that is not explained in detail, nor provided to the user, which violates PeerJ guidelines. This data should be provided and explained, or else replaced with a different dataset.

As a reviewer, I would like to clarify that I have not used bead assays personally, so I can't speak to how well this package meets the specific needs of experimentalists performing these assays.


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: BEADPLEXR: REPRODUCIBLE AND AUTOMATED ANALYSIS OF MULTIPLEX BEAD ASSAYS
Review round: 1
Reviewer: 3

Output:
Basic reporting: Literature should be referenced appropriately throughout the paper, for instance Lines 23-24 would benefit from a reference to ELISA. Please make sure to reference the other multiplex systems for lines 33-39.
Experimental design: In line 52, the authors have mentioned that the other available software allows analysis of only a limited number of beads. I believe that this article would benefit from getting additional details on each of the available software and compare that to beadplexr in a tabular form highlighting the contributions of this R package that are perhaps lacking in the others.

Also, what is the maximum number of samples that can be analyzed at a single time and how long does it take to load the FACS file?
Validity of the findings: In the line 108, thought I understand that it would take a bit of trying to get the settings correct, but I believe that the paper would benefit from clarifying or rephrasing this sentence.

In the line 127, perhaps we could have an example to support for cases where mclust() is a better option.
Additional comments: I commend the authors for creating an open source tool for automated analysis of multiple bead assays. In addition clear commands to follow a workflow were also given. However, I wonder if the authors have considered creating a GUI for this tool using the R package Shiny https://shiny.rstudio.com/ so this package could become more user friendly.


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: BEADPLEXR: REPRODUCIBLE AND AUTOMATED ANALYSIS OF MULTIPLEX BEAD ASSAYS
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comments
Experimental design: No comments
Validity of the findings: No Comments
Additional comments: I am satisfied by the changes made to the manuscript after the revisions.


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: SEROTONIN 5-HT1A RECEPTOR BINDING AND SELF-TRANSCENDENCE IN HEALTHY CONTROL SUBJECTS—A REPLICATION STUDY USING BAYESIAN HYPOTHESIS TESTING
Review round: 1
Reviewer: 1

Output:
Basic reporting: Identical work is put online https://www.biorxiv.org/content/early/2017/12/22/226092. Can authors explain?

No caption in all the tables and figure.
Experimental design: This work is a replication of the previous work from the same group that already published in 2003. The number of subjects has increased from 15 to 50. The quantity is sufficient to make the statistical sound, but the selection of subject is still considered too narrow with only single gender in certain age group. Bayesian approach is used here to proof the correlation between the serotonin binding and self-transcendence. It was concluded with no correlation was found. In general, the study is too vague to jump into such conclusion. Bayesian approach in biological or medical used is quite a common approach in modelling. But thorough experimental design and details questionnaire will be needed in order to to test the hypothesis and make a reliable conclusion. Self-transcendence is very subjective. Can authors defined self-transcendence since it is a very subjective behavior ? How authors define the scoring for self transcendence?
Validity of the findings: No comment .
Additional comments: The current form of the work is not ready for publication.


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

Input:
Title: SEROTONIN 5-HT1A RECEPTOR BINDING AND SELF-TRANSCENDENCE IN HEALTHY CONTROL SUBJECTS—A REPLICATION STUDY USING BAYESIAN HYPOTHESIS TESTING
Review round: 1
Reviewer: 2

Output:
Basic reporting: The writing is good. Unfortunately, it was not clear to me what an inverse correlation is. Do the authors mean a negative correlation? If so, please just write negative correlation, otherwise please clarify.
Experimental design: No idea about the Aims and Scope of the journal, but it was clear that the authors tried to replicate their previous result as closely as possible, which is admirable.
Validity of the findings: As is written on line 128, an unaware reader might misinterpret the replication hypothesis, where it is stated that H_{r} is the original correlation. It’s true that Josine’s R-code uses the original observed correlation r_{ori} and n_{ori}, but it does not mean that the alternative hypothesis is specified as the point r_{ori}. Instead, a whole range of population correlation rho’s is specified as the alternative hypothesis, see Figure 2 (in fact, the code provided in this review). This aforementioned whole range is the posterior on rho informed by the data of the original study. It is correct that this posterior is peaked at r_{ori} and its concentration depends on n_{ori}; the larger n_{ori} the more peaked it is. As n_{ori} is not extremely large it is definitely not a point hypothesis. In other words, the replication Bayes factor uses the posterior based on data of the original study as a prior for the replication attempt. Moreover, in Ly, Etz, Marsman, & Wagenmakers (2017), see

https://psyarxiv.com/u8m2s/

it is clarified that the replication Bayes factor quantifies the evidence within the data of the replication attempt given the data of the original study. Perhaps the following references might help the reader with the interpretation of the Bayes factor. Though that’s fully up to the authors.

Jeffreys, H. (1961). Theory of Probability

Ly, A., Verhagen, A. J., & Wagenmakers, E.-J. (2016). Harold Jeffreys’s default Bayes factor hypothesis tests: Explanation, extension, and application in psychology.

Ly, A., Verhagen, A. J., & Wagenmakers, E.-J. (2016). An evaluation of alternative methods for testing hypotheses, from the perspective of Harold Jeffreys.
Additional comments: Unfortunately, I was unable to access the data, as the file

	~/Dropbox/PET studie/NenR orig&repl.xlsx

isn’t uploaded onto the OSF. It would be nice to have this available as I would then be able correct Figure 2 of the manuscript. The following script requires the author to download (today 01-03-2018)

https://github.com/AlexanderLyNL/jasp-desktop/blob/development/JASP-Engine/JASP/R/common.R
https://github.com/AlexanderLyNL/jasp-desktop/blob/development/JASP-Engine/JASP/R/correlationbayesian.R

and source them. I highly recommend putting “common.R” and “correlationbayesian.R” on the OSF repository, as the code will be modified in the near future. I’m not fond of the name “default posterior”, but it’s up to the authors. Lastly, as the authors have the original and the replication data at hand, they can much easier calculate a replication Bayes factor, perhaps after a location shift. I’m quite sure that the authors of Ly, Etz, Marsman, & Wagenmakers (2017) are willing to share this code.

myWd <- "~/Dropbox/PET studie/"
setwd(myWd)

source("common.R")
source("correlationbayesian.R")

# Fill in the original and replication result
nOri <- 12
rOri <- -0.06

nRep <- 50
rRep <- -0.19

bfObject <- .bfCorrieRepJosine(nOri=nOri, rOri=rOri, nRep=nRep, rRep=rRep)

rComb <- bfObject$combined$r[2]
nComb <- bfObject$combined$n[2]

myFirstPriorLine <- .priorRhoMin(rho=rhoDomain)
myPosteriorGivenDOriLine <- .posteriorRhoMin(n=nOri, r=rOri, rho=rhoDomain)
mySecondPriorLine <- myPosteriorGivenDOriLine
myPosteriorGivenAll <- .posteriorRhoMin(n=nComb, r=rComb, rho=rhoDomain)

maxY <- 1.05*max(myFirstPriorLine, myPosteriorGivenDOriLine, myPosteriorGivenAll)

par(cex.main=3, mgp=c(3.5, 1, 0), cex.lab=2.5, font.lab=2, cex.axis=1.3,
    mar=c(5, 6, 4, 7)+0.1, bty="n", las=1)
plot(0, 0, xlab=expression(rho), axes=FALSE, ylab="", ylim=c(0, maxY), col="white")
axis(1)
axis(2)
lines(rhoDomain, myFirstPriorLine, lwd=3, lty=3, col="grey")
lines(rhoDomain, mySecondPriorLine, lwd=3, lty=2, col="dimgrey")
lines(rhoDomain, myPosteriorGivenAll, lwd=3)

points(0, mySecondPriorLine[zeroIndex], pch=21, cex=2.5, bg="grey")
points(0, mySecondPriorLine[zeroIndex], cex=2.5, lwd=3)

points(0, myPosteriorGivenAll[zeroIndex], pch=21, cex=2.5, bg="grey")
points(0, myPosteriorGivenAll[zeroIndex], cex=2.5, lwd=3)

legend("topright", c(expression(paste(pi["-"], "(",rho, ")")),
                     expression(paste(pi["-"], "(",rho, "|d"['ori'], ")")),
                     expression(paste(pi["-"], "(",rho, "|d"['comb'], ")"))),
       lwd=c(2, 2, 2), lty=c(3, 2, 1), col=c("grey", "dimgrey", "black"),bty='n', cex=1.3)


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: SEROTONIN 5-HT1A RECEPTOR BINDING AND SELF-TRANSCENDENCE IN HEALTHY CONTROL SUBJECTS—A REPLICATION STUDY USING BAYESIAN HYPOTHESIS TESTING
Review round: 2
Reviewer: 1

Output:
Basic reporting: The conclusion in the previous round to reject the paper was and is, in my opinion, unfair and preposterous. As a result of this, I decided not to review for this journal again. Fortunately, the authors appealed and I’m glad that they got the opportunity to resubmit the manuscript, which made me decide to review again. The current manuscript addresses all the concerned raised previously and I believe that it should be published.
Experimental design: Good
Validity of the findings: Good
Additional comments: Very minor remarks:
- Line 76: Please remove "a" and make it plural. "Recently replication Bayes factors"
- Line 123: Please write Bayes factors instead of Bayes Factors.
- Line 128: It would be more clear if the authors would write "... original study, assuming a uniform prior before seeing the data of the original study"
- Line 136: Please add the subscripts to the Bayes factor and elaborate that the Bayes factor is a relative measure of evidence. For instance "A BF01 below 3 indicates weak or anecdotal evidence...... strong evidence in favour of the null against the alternative."
- Line 137: Etz & Vandekerckhove, 2016 are great, but Harold Jeffreys (1961) should be credited for this.
- Line 158: Before this paragraph it might be good to give the overall conclusion that all Bayes factor favour the null over the alternatives.
- Line 252: Is a bit unclear to me
- Table 2 description:
+ H_{r}: Posterior of \rho given the original study
+ In their response the authors noted that they did not do a directional test, but the notation BF01 remained. In addition, my personal preference is denote a replication Bayes factor as BF01(d_{\rep} | d_{\orig}) to make explicit that one conditions on the previous data. The code I provided gives Bayes factors and replication Bayes factors for both directed as well the undirected tests. Thanks for spotting the error in my code.
- Figure 2 description:
+Please change "The posterior of the default BF test" to "The posterior based on a uniform prior on \rho".
+H_{r}: Posterior of \rho given the original 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: SACCADES AND HANDEDNESS INTERACT TO AFFECT SCENE MEMORY
Review round: 1
Reviewer: 1

Output:
Basic reporting: The authors present the results of a single experiment that investigates the effects of both handedness and eye-movements on a STM and LTM task. It was found that when EMs were made prior to the STM task, then a relationship between handedness and performance was observed. However, EMs prior to recognition testing had no effect and was unrelated to handedness. This experiment was well conducted and explored some important issues. I have some comments to make that I think could be addressed in a revision. I have placed these below on a section-by-section basis.

Introduction
The authors provide a good and wide-ranging introduction that covers relevant existing research on SIRE and handedness effects on memory.  Although I believe this to be good, I would like to suggest some revisions.

1. Line 67. I think the sentence could be modified slightly – thus:
“Strong right-handedness, which is associated with decreased interhemispheric interaction, . . .”
 TO
“Strong right-handedness, which is argued to be associated with decreased interhemispheric interaction, . . .”
I say this in order to indicate the provisional nature of the claim.

2. Line 71. The authors appear to indicate that mixed handedness is associated with superior implicit memory as measured by WFC. In actual fact, if the corrected scores are analysed then handedness did not influence WFC (Propper eta l., 2005).

3. The sentences covering line 82 to about 86. I think this could be revised and made clearer – thus:
 “A study of both recall and recognition with strongly right-handed (SR) and non-strongly right handed (nSR) subjects found that eye movements made little difference or could even be detrimental in nSR subjects. This finding supports the hemispheric interaction hypothesis but with the caveat that eye movements could be harmful for nSR individuals (Lyle et al. 2008a).
TO
“A study of both recall and recognition that compared strongly right-handed (SR) to and non-strongly right handed (nSR) subjects found that eye movements largely benefited the former whilst was shown to be somewhat detrimental to the latter (Lyle et al. 2008a). This finding was taken to support the hemispheric interaction hypothesis

4. Lines 109-111. The authors mention a recognition task that demands a high degree of right-left activity. Can I suggest that they indicate that this was old-new recognition and was compared to forced-choice recognition. For the former, they could say that this purportedly depends on right-left interaction.

5. For the final part of the introduction the authors note that the present concern is with both working memory and long-term recognition memory. I think that at this juncture it would be good to elucidate to the reader the potential relationships that could exist between WM and LTM and then consider this from the perspective of SIRE/handedness. I appreciate that this work is exploratory but I think it could be useful. This is just a suggestion for the authors and it could also be later reflected upon in the discussion.

6. As I noted, coverage of relevant material is good but I think that the introduction could benefit from a little restructuring in order to improve the presentation of the background work and their ideas.

For example - maybe consider using labelled subsections and (i) providing separate parts on SIRE and handedness effects prior to considering them together (ii), providing a separate section dealing with various problems of the cited work and the hemispheric interaction account, (iii) introduce the top-down control ideas and how this is related to certain experiment findings such as Lyle & Martin (2010) and Lyle & Edlin (2015).
Experimental design: Here I have commented upon the methods and results.

Method
1. I think that the design section could be presented in a clearer and more concise manner. For example: “The predictor variables were the eye-movement task (fixation vs. saccade) and placement of the EM task (before WM or before recognition). Both were between-subjects and the number/descriptives of the subjects in each group were . . . etc. The criterion variables were . . .  etc
I used the terms predictor and criterion variables here given that regression analyses were performed.
2. What was the degree of visual angle for the EM task?
3. For the recognition task, were subjects required to respond with the 2 seconds that the picture was on the screen?

Results
Was there any rationale for using regression for the analyses? Previous work has always used ANOVA. Was this to avoid treating the handedness score as a dichotomous variable?
Perhaps the authors could also indicate why only some of the DVs were explored in the presented analyses.
Validity of the findings: The results are evaluated in a thorough manner and relate clearly to the results and findings. The conclusions follow logically from the findings. I have just a few points that relate to the discussion.

Line 449. At this point the authors note that the subjects may have used a familiarity-based strategy to perform the recognition test. They could cite work that has shown EM effects to be more beneficial for remember/recollective responses or tasks that demand recollection for accurate responses rather than familiarity (e.g., Parker, Relph & Daganall 2008 and  Lyle, Hanaver-Torrez,  Hacklander, and Edlin 2012).

In relation to the above, if subjects were required to response rapidly (e.g., within a 2 second window) then this might have fostered the use of a familiarity-based strategy.

Line 457. Small suggestion = perhaps the sentence could be reworded
“The findings showed that neither the eye movement nor fixation conditions elicited significant improvement, . .”
TO something like
“The findings showed that none of the eye movement conditions enhanced WFC performance compared to the fixation condition” This was taken to indicate saccades do not enhance implicit forms of memory that are likely reflective of intra-hemispheric activity (Christman et al. 2003).

For the recognition task, each picture appeared on the screen for 2 s followed by an ISI of 2 s. As there were 200 trials, this equals 800 secs overs = 13. 33 mins. This is quite a long time and I wonder if the effects of the EMs may have reduced across this time interval. Perhaps worth a discussion point?
Additional comments: Overall, some interesting issues were explored in this experiment. It’s a pity that the EM manipulation didn’t influence recognition, but maybe this is an example of a boundary condition for SIRE effects. I have indicated a major revision - but please do not let that put you off. The main reason I clicked on this option was simply related to the range of comments I have made (NOTE - many of these are very small indeed and doable in next to no time).
I believe the revision should not be in any way onerous and I reckon the authors could do it rather easily and in a very short space of time!! The largest job (should the authors agree) - relates to some restructuring/reorganisation in the introduction.


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: SACCADES AND HANDEDNESS INTERACT TO AFFECT SCENE MEMORY
Review round: 1
Reviewer: 2

Output:
Basic reporting: I believe this manuscript would benefit from a thorough rewriting.  The authors clearly wish to interpret effects of saccade execution memory in terms of interhemispheric interaction.  This approach is outdated.  In reviewing the literature, the authors do not provide a single piece of evidence supporting the idea that saccade execution affects memory (or any other form of cognition) by increasing interhemispheric interaction.  On the contrary, the authors cite evidence that weighs AGAINST the idea that interhemispheric interaction is at the root of saccade-execution effects (lines 93-96, 117-119, and 129-131).  Nonetheless, the authors' primary conclusion (lines 490-491 and also stated in the abstract) is that scene processing does not depend on interhemispheric interaction and this is why they failed to find saccade-induced retrieval enhancement.  It is difficult to see how this conclusion follows from what has come before.  I would also point out that this conclusion says nothing about why saccade execution HARMED scene memory.  I would encourage the authors to think about what scene processing DOES depend on (versus focusing on what it DOESN'T depend on) and then consider why saccade execution HARMED scene memory.  The authors have some potentially interesting findings here but I don't think they do them justice.
Another important consideration is that prior research has been primarily concerned with differences between inconsistent and consistent individuals.  The authors, in contrast, seem more interested in strong right-handedness versus its absence (see, for example, statements made in the abstract).  I myself was originally interested in the strong right-handed versus not distinction but the literature has advanced past that point.
Experimental design: I have no serious concerns about the experimental design but I think the authors must do a better job of acknowledging how their methodology differs from standard practice in studies of handedness and saccade execution.  One important difference is that the authors used a different handedness inventory than is used in the labs that have generated most of the research that the authors cite.  I am thinking of Christman's lab, Propper's lab, Parker and Dagnall's lab, and my lab.  The inventory used in those labs is described in Lyle, McCabe, and Roediger (2008).  I am not suggesting that the authors' use of a different inventory invalidates their findings.  I have nothing of the sort in mind.  I am only saying that the authors should acknowledge the difference and discuss its implications.  Also, the authors do not report the visual angle subtended by the left and right discs in the eye-movement task.  This is critical information.  The labs mentioned above have all used the same visual angle.  Furthermore, the authors had subjects count the number of times the disc changed positions or colors.  To my knowledge, that requirement has not been imposed in any previous studies.  Again, I think the authors must acknowledge this difference, as they acknowledge other important differences (lines 471-478).
Validity of the findings: No comment.
Additional comments: My comments under Basic Reporting and Experimental Design will no doubt be discouraging for the authors.  I therefore wish to be clear that I think the authors have the basis of a potentially publishable paper here.


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

Input:
Title: SACCADES AND HANDEDNESS INTERACT TO AFFECT SCENE MEMORY
Review round: 1
Reviewer: 3

Output:
Basic reporting: -	Lines 97-101: citations should be provided for points 1 and 2

-	Lines 129-131: the authors should cite a study by Propper et al. that found that eye movements had significant effects on interhemispheric coherence in the gamma band:

Propper, R.E., Pierce, J., Bellorado, N., Geisler, M.W., & Christman, S.D. (2007). Effects of bilateral eye movements on interhemispheric gamma EEG coherence: Implications for EMDR therapy. Journal of Nervous and Mental Disease, 95, 785-788.

-	Lines 146: the authors may be interested in citing an unpublished conference presentation that showed that eye movements before encoding hurt subsequent memory performance:

Christman, S.D., & Butler, M. (2005). Bilateral eye movements impair the encoding and enhance the retrieval of episodic memories. Presented at the 46th Annual Meeting of the Psychonomic Society, Toronto.

-	Line 151: it is not clear what “a fixed load of 5” refers to. Five what?

-	Lines 465-467: what were the results of the Brunye et al. (2009) study?
Experimental design: -	Lines 204-206: given that participants’ eye movements were monitored by the experimenter, it is not clear why the details about eye tracking equipment were provided in the previous paragraph
Validity of the findings: This manuscript presents a single experiment looking at how eye movements and handedness interact in influencing working memory and long-term recognition memory for complex natural scenes. The two most valuable aspects of the study is (i) extending the meagre existing literature on how eye movements affect different handedness groups differently, and (ii) extending this paradigm to nonverbal stimuli.

My biggest concern centers on the dependent variables used to assess memory performance. It appears that the authors are simply using percent correct as their d.v.  However, such a procedure confounds accuracy with response bias. To illustrate an extreme case, if a subject in their study responded that they recognized every single stimulus, that subject would have a 100% hit rate but also a 100% false alarm rate. To control for this, it is imperative that the authors use some sort of corrected accuracy score. I highly recommend performing signal detection analyses, allowing for independent examination of accuracy (d’) versus response bias (beta). However, the simpler “Hits minus False Alarms” might be sufficient. As it stands now, it is impossible to precisely determine the effects of eye movements and handedness on memory accuracy because the authors’ current analyses make it impossible to examine the effects of response bias.

The authors also need to provide more information about the revised version of the Edinburgh Handedness Inventory that they used. They provide a citation to Williams, 2010. However, the citation info in the reference section is incomplete, lacking a journal title, volume number, and pages. Being a very active handedness researcher, I was surprised that I was not aware of this Williams study; the authors need to provide the full citation info. I was particularly concerned by one of the two sample items mentioned by the authors: “using a computer mouse”. I have never seen this item on the EHI before, and need more details about how the “EHI-R” used by the authors was constructed and validated. I recommend the authors read the following article on EHI revisions:

Edlin, J.M., Leppanen, M.L., Fain, R.J., Hanaver-Torrez, S.D., & Lyle, K.B. (2015). On the use (and misuse?) of the Edinburgh Handedness Inventory. Brain and Cognition, 94, 44-51.

Another issue involving handedness is how the EHI-R scores were used. The authors used the raw EHI-R scores in their regression analyses. However, given the growing emphasis on degree of handedness (strong/consistent versus mixed/inconsistent), many recent handedness studies convert raw EHI scores into absolute values. This gives a scale that ranges from mixed to strong (instead of from left to right). I highly recommend that the authors perform additional regression analyses on absolute value EHI-R scores.
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: SACCADES AND HANDEDNESS INTERACT TO AFFECT SCENE MEMORY
Review round: 2
Reviewer: 1

Output:
Basic reporting: I would like to thank the authors for taking on board the revisions based on my previous set of comments. Overall, I think they have done a commendable job and the paper reads much better and is structed in a more coherent manner compared to the first submission. In this context I have just a small range of minor points for the authors to consider.

Minor Points:

Line 60: After “everyday events” there should not be a full stop before the Christman citation.

Line 61: Maybe just acknowledge the first use of the term SIRE by Lyle and Colleagues.

Line 72: Part of this sentence is incorrect. We found effects for horizontal eye-movements not vertical.

Lines 131- 132: I have just suggested a slight change to a sentence to make the description of the findings more precise.

Thus, rather than:
“Increased match detection accuracy was found on the within-hemisphere trials suggesting saccades enhance intrahemispheric processing but not interhemispheric interaction.”

How about

Increased match detection accuracy was found on the within-hemisphere trials as a function of pre-task eye-movements suggesting saccades enhance intrahemispheric processing but not interhemispheric interaction.”

Line 128: After “brain hemispheres” there should not be a full stop before the Lyle & Martin reference.

Line 628: There is a full stop after “ . involve words” that is not needed.
Experimental design: Just a couple of points:

Working Memory Section: From which serial position were the positive probes selected? Was this also just random?

Recognition Memory Section: Were any of the “old” stimuli previously used as positive probes?
Validity of the findings: The discussion of the findings has been revised since the original submission and takes into account the comments of the other reviewers to acknowledge the differences between the present and past experiments (e.g., in terms of methods). This I believe has helped and I have no further comments to make.
Additional comments: As noted above, I think the revised submission is much superior to the original. I feel that my comments have been addressed and the paper has a more coherent feel to it. Some of the ideas outlined and discussion points made would profit from future work and investigation.