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: PHYSIOLOGICAL RESPONSES OF OXYRRHIS MARINA TO A DIET OF VIRALLY INFECTED EMILIANIA HUXLEYI
Review round: 1
Reviewer: 3

Output:
Basic reporting: Yes on all accounts.
Providing the raw data was extremely helpful in better assessing this manuscript.
Experimental design: Clear and unambiguous, professional English used throughout.
Yes

Literature references, sufficient field background/context provided.
Yes

Professional article structure, figs, tables. Raw data shared.
Yes. Having the raw data was very helpful to further assess their results and conclusions!

Figures should be relevant to the content of the article, of sufficient resolution, and appropriately described and labeled.
Yes

All appropriate raw data has been made available in accordance with our Data Sharing policy.
Yes

Self-contained with relevant results to hypotheses.
Yes
Validity of the findings: The overall rationale to conduct these experiments is interesting and valuable to investigate. These types of experiments should give important insights into the complex interplay of virus-host-grazer interactions. However, the experimental set up and analyses, overall, need some major improvement or justification to convince me that virally-infected E. hux are actually resulting in higher growth rates in O. marina. In particular, they need to address the possible contribution of bacterial grazing and bacteria to C and N measurements. More important though is showing and addressing that grazer growth rates appear to fluctuate daily (and potentially ingestion rates as well), calling into major question their major conclusions about infected Ehux resulting in stronger grazer growth.

Details on Major issues
1) It was unclear to me from the methods how O. marina growth rates were measured and over what time periods. I assume that these were calculated over the periods indicated in Table 1 (i.e. Tfinal vs T0). A simple line that these were calculated based on t=0 and the final time point (which is what I assume was done) would help clarify. However, the authors also then state in the Methods (lines 170-173) that the periodic addition of prey made it difficult to make direct measurement of prey and predator cell concentrations, which would impact calculation of growth and ingestion rates. I appreciate that the authors clearly state that any cell loss through viral lysis in the Eh-infected conditions makes it hard to actually measure ingestion rates (line 314-320) and therefore may overestimate these rates. But, can we therefore really trust the reported ingestion rates? Which one is it, yes we can reliably measure growth and ingestion rates or can’t we? I would also add that it seems that one could still accurately account for changes in O. marina cell numbers, by accounting for the slight dilution events that occurred when volume was added during periodic prey additions, so it seems like they should be able accurately calculate predator growth rates. Perhaps they did this in the supplemental tables provided, but that wasn’t clear to me.

What I found really helpful was the time vs E. hux cell number plots from experiment 1 in Fig. S2. Why are these not shown, even as supplemental data, for the other experiments as well? Likewise, it would be valuable to see O. marinus numbers plotted over time to get a better overall sense of the results of these experiments, especially in terms of how ingestion rate seems to drop off after the first few hrs in Exp. 1 and how it may vary over days in Exp’s 2-4.

So, this was intriguing me, so I actually went and looked at the data available in the supplemental tables and did some quick and dirty plots. See attached and related comments below.

Related to this, the authors make a statement (lines 279-291) “Compared to experiment 1, the higher total number of ingested E. huxleyi cells, both infected and non-infected, measured in experiments 2 – 4 indicated that O. marina resumed ingestion after 6 h, as prey cells were digested.” The authors have the data (daily time points) to do this. I in fact re-analyzed the data they provided and see that grazer growth rates at least fluctuate daily. One could do this for the ingestion rates, but it wasn’t clear to me from the two table provided which were the appropriate number to look at it.

Similarly, there is the following sentence (lines 281-282): “Also, the relatively low standard deviation values indicated daily ingestion rates were fairly constant from day to day in experiments 2 – 4.” This statement is presumptive and not substantiated. Again, one could calculate these from their data. In theory, the rates in each experiment could vary wildly from day to day, but still the ‘bulk’ ingestion rate (which again I assume is calculated from t=0 and Tfinal [3,5,or days]) could all be very similar between these three experiments.

The grazer cells numbers suggest that ingestion rates probably fluctuate daily (see below). This was nagging me so I plotted daily O. marina abundances and they fluctuate day to day between the treatments, suggesting day variation in grazer growth rate. I did a quick analysis of these growth rates ( ln(Tx/T(x-1)) ) for Exp. 3, and they do in fact fluctuate. So depending on when you ended the experiment, the ‘bulk’ grazer growth rate could be higher or lower for Ehux or infected Ehux. (Note: that there are two tables reporting cells abundance in their supplemental tables. I’m not sure what is the difference between them, so I plotted the data for both.) This fluctuation day to day throws their overall conclusions about differences in grazing rates between non-infected and infected cells into question. I predict that the daily ingestion rates vary daily as well.

2) The time vs cell number plots in Fig. S1C and S2 suggest that the E. hux prey cells used appear to not actually be growing in exponential phase as reported in the methods section. In Fig. S1C, non-infected cells go up briefly then go down and plateau. This suggests that they are actually in stationary phase or were at best harvested in late-log, just before stationary phase. Likewise, in the non-grazing treatments of E. hux in Fig. S2, E. hux slowly declines over time suggesting that the cells are in stationary phase. Or were they diluted and this is some strange effect on the cells from dilution? These data are in conflict with what the authors state about using cells in log phase. From their experience with these conditions (light, temp, media) at what concentrations does E. hux hit stationary phase (i.e. what does a typical growth curve look like)? I think it is important to conduct these experiments in log phase because cell physiology can be altered in stationary phase. At the very least, the authors should explain these odd patterns and revise their statement that the cells are probably in late-log phase or stationary phase.

Again I was curious about this,  so I actually plotted the Ehux abundance for the non-grazing controls. For Exp. 1,2, and 4 the Ehux controls are flat or decline, again indicating that the cells are not growing exponentially. This is a major problem here to address.

3) The final major complicating factor that the authors have not addressed is that the cultures are non-axenic. I fully appreciate that it is difficult (and sometimes impossible) to generate axenic cultures of phytoplankton, but it should be discussion at the least. Bacteria are not much smaller than O. marina, and other studies show that O. marina can ingest and grow on bacteria (Quick literature search found this: Roberts et al 2011 "Feeding in the dinoflagellate Oxyrrhis marina: linking behaviour with mechanisms” J. Plankton Research 2011). At the very least, the authors should address in the discussion how growth on bacterial grazing may affect their results and conclusions. In my opinion, they really need to determine bacterial counts to properly assess any potential difference between the virally-infected and non-infected E. hux cultures in terms of bacterial abundance and grazing. Specifically, it is plausible that viral infection releases organic matter that fuels bacterial growth which then increases O. marina growth. This in fact may precisely explain the perplexing results that ingestion rate of E. hux is lower in +virus conditions but O. marina growth rate is higher.

In addition when setting up the stocks of E. hux for the grazing experiments, the Eh+virus contains E. hux lysate (to inoculate with viruses) but this lysate (<0.45 µm) also will contain cell debris that will fuel bacterial growth, and the –virus E. hux is given the same volume of sterile f/2 to make the E. hux concentrations equal. What is the volume of lysate volume added? Even if it is a small volume, the lysate could be chock full of tasty organic material and sufficient to stimulate the bacteria which then subsequently feeds the O. marina. Also, there were daily additions of E. hux cells to maintain the grazer:prey balance, so the addition of E. hux infected cells could inject additional bacteria and/or lysates to fuel bacterial growth.

4) Similarly, the C and N measurements probably reflect those of E. hux cells and bacteria (GF/F filters catch bacteria). These results are suspect as well and probably are not just C and N content of E. hux.

5) If the reason for increased O. marinus growth rate on Ehux+virus cells really is increased nutrition of infected E. hux due to increased N, can the slight increase in N content account for the increased grazer growth rate, even with the decreased ingestion rate based on cell quotas? It seems like one could do a back of the envelope calculation based on cellular N content of O. marinus and E. hux with the measured ingestion and grazing rates. This still doesn’t address where the C is coming from to fuel increase O. marina growth. The C and fatty acid data don’t support higher C content in infected E. hux cells, so the authors don’t have a plausible explanation for how this works mechanistically.

Again, overall, I think the direction and goals of this study are very interesting and important, but the methods and measurements need some major revision, repeating of the experiments, or strong justifications and explanations to account for my concerns above.

Another positive aspects of the study
Lines 420-422. This is a sound and important conclusion, to look again at the Evans and Wilson study.

Other less important issues.
Line 177 “We postulated a starting population size of 6,000 O. marine cells” Didn’t the authors measure the original grazer populations. Perhaps they mean “For these calculations, we set the starting population size at 6,000”

Line 411-413: “Furthermore, several studies have shown that O. marina responds in a similar way to other microzooplankton taxa to various experimental stimuli (Strom et al. 2003a; Strom et al. 2003b; Tillmann 2004).”

This syntax is confusing, I think the authors mean this: “Furthermore, several studies have shown that O. marina responds to various experimental stimuli in similars ways to that of other microzooplankton taxa (Strom et al. 2003a; Strom et al. 2003b; Tillmann 2004).”
Additional comments: Again, I feel their are major issues to address here, but I welcome rebuttal to my issues, especially if my assessment of the data is incorrect. This especially applies to my re-analysis of the cell count data, so I have attached a PDF that shows as best as I could, the data I pulled and used for the plots for verification.


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: PHYSIOLOGICAL RESPONSES OF OXYRRHIS MARINA TO A DIET OF VIRALLY INFECTED EMILIANIA HUXLEYI
Review round: 2
Reviewer: 1

Output:
Basic reporting: The articles is well written and clearly presented
Experimental design: The experiments were well designed and conducted. All methods used are well described.
Validity of the findings: The data presented derived from well conducted experiments and all results appear to me well interpreted. The conclusions are thus well supported and further discussion provide future avenues of research that will take further the reported significance of the work.
Additional comments: Dear Authors,
thank you for the feedback from the earlier review and the clear improvement of the manuscript by adding a new experiment (exp 5) verifying that Oxyrrhis growth is not enhanced in the presence of bacteria, virus or other molecular by-products of infection. This validates your main findings.
I suggest a final overview of the manuscript as I detected several words that are connected lacking a space between them. Otherwise, all seems to be good.


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: PHYSIOLOGICAL RESPONSES OF OXYRRHIS MARINA TO A DIET OF VIRALLY INFECTED EMILIANIA HUXLEYI
Review round: 2
Reviewer: 2

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


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

Input:
Title: AN AFFORDABLE AND AUTOMATED IMAGING APPROACH TO ACQUIRE HIGHLY RESOLVED INDIVIDUAL DATA—AN EXAMPLE OF COPEPOD GROWTH IN RESPONSE TO MULTIPLE STRESSORS
Review round: 1
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: An affordable and automated imaging approach to acquire highly-resolved individual data - an example of copepod growth in response to multiple stressors (#33090)

The authors examined the combined effects of fish-released kairomones and copper toxicity on copepod life traits. The unique method of the automated imaging platform used for this analysis enables to view and analyze rapidly occurring changed in multiple individuals while reducing the bias originating from human interruption. The system has great potential to explain life history shifts of various species and as such would be of interest to ecologists from several fields.
I think the manuscript would benefit greatly from a figure summarizing the combine effects on copepod life-history traits. Currently, the effects are complex and not easy to follow.
Line 53: et al.
Lines 75-78: this sentence needs to be rephrased. I understand the point that the authors are trying to make, however constant observation is not required. I’ve conducted several such studies using mosquito larvae, and development rate can be calculated with 2 observations per day.
Line 95: The aim?
Line 96: sentence not clear, you mention that the system can follow a large number of individuals but do not mention that they need to be in separate wells.
Line 103: Define kairomone.
Line 137: Please expand on the kairomone treatment. What fish species? From what volume were the water taken, how many fish were placed there etc. I also understand that you used salt water. Please expand on how this was done (sea water or freshwater with additional salt?).
Line 281: AICc?
Line 287: Sex, not gender.
Line 299: you keep mixing the terms “kairomones” and “predator cues”, be constant.


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 AFFORDABLE AND AUTOMATED IMAGING APPROACH TO ACQUIRE HIGHLY RESOLVED INDIVIDUAL DATA—AN EXAMPLE OF COPEPOD GROWTH IN RESPONSE TO MULTIPLE STRESSORS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Measurements for copepod growth rate are labor intense and time consuming. The authors developed an automated imaging platform to acquire temporally highly resolved individual data and tested this platform by exposing copepods to a combination of a biotic stressor (kairomone, i.e. predator cues) and a toxicant (copper) and measured the growth response of individual copepod. The content for this manuscript is heavy and the timeframe does not allow an in-depth review. My general impression is that this manuscript is likely to get published eventually, but the current format is not ready for publish.

When I read the title for the manuscript, I thought this would be a manuscript on a new methodology or new instrument. But when I read the manuscript, it appeared that this manuscript focused on their experimental results on the impact of a biotic stressor and toxicant on copepod growth. It is not a good choice to do two things in one attempt.
Experimental design: This “new” method and instrument was briefly mentioned in the manuscript. The authors did not give enough details and I found it was difficult to understand how the instrument works.

1) Is light source operated in continuous mode or pulse mode?
2) Is the depth field adequate for the well? If not, does it mean you have to manually acquire proper image for each copepod? That could very time consuming.
3) What is the pixel resolution for the camera? Does it provide enough resolution for small nauplii?
4) Please provide an acquired image with nauplii with proper legend.
Validity of the findings: The validation of new instrument is problematic. The authors compared their measurements against the “published data”. It does not look like the published was from not the same experiment and same individuals.

1) In figure 2, in which the authors intended to present their results against published results as they stated in figure legend. But the published results are nowhere to be found.
Additional comments: I apologize for the authors that I could not deliver a good news for their efforts. It does require extraordinary efforts to develop a new method and validate it against existing methods. This manuscript clearly falls short on both ends.

Two minor comments:

The numbers in the table and text should be consistent in terms of decimal point. Abbreviations should be spelled out in the table caption.

For the experiment design, it looks like that the authors performed their experiments on different clutches, but all data were pulled together to run their GAMs. This operation is likely valid when they want to examine clutch effect but may not valid when they examined overall chemical effects. It should be proceeded more carefully.


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 AFFORDABLE AND AUTOMATED IMAGING APPROACH TO ACQUIRE HIGHLY RESOLVED INDIVIDUAL DATA—AN EXAMPLE OF COPEPOD GROWTH IN RESPONSE TO MULTIPLE STRESSORS
Review round: 1
Reviewer: 3

Output:
Basic reporting: Clear and unambiguous, professional English used throughout.

Additional literature references required

Some additional Figures would be recommended

See "General comments for the author" for detailed remarks
Experimental design: Research question well defined, relevant & meaningful.

Some expansion of the results section is required

See "General comments for the author" for detailed remarks
Validity of the findings: Conclusion are well stated, linked to original research question & limited to supporting results

Data is robust, statistically sound, & controlled.

See "General comments for the author" for detailed remarks
Additional comments: The manuscript by Heuschele et al describes development of a novel, temporally resolved phenotypic analysis platform for the analysis of copepod growth in ecotoxicological bioassays.

I agree with the authors that the automated analysis in ecotoxicology is still underdeveloped and in fact ecotoxicology is one of the least automated fields of biosciences at this moment. More importantly the analysis of temporal events in environmental toxicology is rarely taken into account that is highly surprising since the physiological effects of contaminants depend not only on their concentration but also exposure time.

The foundations of this study are thus sound and there is definitely a need for more automated imaging (and non-imaging) high-throughput phenotypical analysis platforms to acquire highly resolved temporal data in ecotoxicology. The study is in general well written with sufficient methodological, experimental and analytical rigor. The data sets are clearly laid out and discussed well.

Areas for improvement are as follows:

1)	Introduction – is a bit complex and in part a bit off the main topic (especially in the first part).
Authors should focus on:
i)	importance of the phenotypical analysis, high-throughput phenomics (as a future in ecotoxicology in general)
ii)	review of the most recent technological advanced in automation of ecotoxicological assays
iii)	finally position their system accordingly to the above and outline innovation relating to copepod bioassays performed at the moment

2)	A quick search of the web indicates some recent papers that should be cited/discussed and that in fact pioneered the concepts of automated phenotypical analysis, time resolved analysis, and even miniaturization in aquatic ecotoxicology:
-	O Campana, D Wlodkowic (2018) Environmental science & technology 52 (3), 932-946
-	O Campana, D Wlodkowic (2018) Sensors and Actuators B: Chemical 257, 692-704
-	Y Huang, O Campana, D Wlodkowic (2017) Scientific reports 7 (1), 17603
-	F Zhu, A Wigh, T Friedrich, A Devaux, S Bony, D Nugegoda, J Kaslin, D Wlodkowic (2015) Environmental science & technology 49 (24), 14570-14578
-	J Akagi, F Zhu, CJ Hall, KE Crosier, PS Crosier, D Wlodkowic (2014) Cytometry Part A 85 (6), 537-547

3)	Materials and Methods – camera system should be described in more details including resolution, type of files generated compression, codecs etc.

4)	Results – The description of the system design, validation and operating principles should be provided in details at the beginning of the results section since this is the main innovation of this work.

5)	Appropriate diagrams and flow charts of the operation of the system should be provided together with photographs of the prototype. The Figure 1 is too minimalistic!

6)	As per the above (see comment 3) the authors should describe and possible present numerical data to demonstrate the reliability and reproducibility of the XY-plotter to position the camera repeatedly over the same wells over time. How did the authors assessor that there was no drift from X-Y coordinates. Were additional sensors employed, was there an optical algorithm detecting an outline of the well employed?

7)	Exemplary micrographs generated by the system should be also demonstarted in one of the Figures.

8)	Why on Figure 1 light sources are positioned horizontally on both ends of the system. From my experience a light box with a carefully designed diffuser etc is usually needed to provide a uniform illumination of samples. Authors should discuss this in much more details. Did they use any system to distribute the light evenly over all samples? How did authors minimize the edge shadow effect due to a meniscus of media in the wells?

9)	Discussion “Our system can even quantify the behavioral variability in

populations from recorded movie sequences. “ – unlikely since the time delay the current system requires to move camera from well 1 to well x will introduce temporal gaps in data. For behavioral analysis single ultra resolution camera system is required to capture movies simultaneously from all samples.

10)	 Authors could also briefly describe costs of the construction of a similar system and its user friendliness for laboratories without any engineering inclination.


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 AFFORDABLE AND AUTOMATED IMAGING APPROACH TO ACQUIRE HIGHLY RESOLVED INDIVIDUAL DATA—AN EXAMPLE OF COPEPOD GROWTH IN RESPONSE TO MULTIPLE STRESSORS
Review round: 2
Reviewer: 1

Output:
Basic reporting: I have no further comments. Authors have addressed my previous comments in this revised version.
Experimental design: I have no further comments. Authors have addressed my previous comments in this revised version.
Validity of the findings: I have no further comments. Authors have addressed my previous comments in this revised version.
Additional comments: I have no further comments. Authors have addressed my previous comments in this revised version.


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: USING IPOMOEA AQUATIC AS AN ENVIRONMENTAL-FRIENDLY ALTERNATIVE TO ELODEA NUTTALLII FOR THE AQUACULTURE OF CHINESE MITTEN CRAB
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: This paper aimed to identify an alternative macrophyte system for Chinese mitten crab aquaculture. The authors found that the Ipomoea aquatic (IA) and Oryza sativa (OS) systems might both be suitable alternatives for Chinese mitten crab aquaculture, as both systems had similar crab yields to the Elodea nuttallii (EN) system, as well as a greater level of nitrogen removal. Overall, the manuscript is well written and the results are persuasive. I think this manuscript is worthy of publication in PeerJ. However, I have some minor comments and suggestions that should be considered by the authors.
1. The abstract is a little long and can benefit from being more concise. The less important contents may be deleted from the abstract, such as the method to estimate plant biomass.
2. Line 53: Three replicates are not enough to support your conclusion. Five or more replicates are needed in field experiments.
3. Lines 166 and 224: This content has been described twice and should be deleted in discussion section.
4. Lines 228-229: The authors stated that OS is not a suitable alternative to EN. However, in abstract, they also found that the IA and OS systems might both be suitable alternatives for Chinese mitten crab aquaculture. Please keep consistent throughout the manuscript.
5. Line 240: Why plant biomass increased linearly? Please give a reference for this sentence.
6. Lines 269-270: The authors reported that the IA and OS systems might have a higher denitrification potential than the EN system, because concentrations of NO3 were lower in the IA and OS systems than in the EN system. I cannot agree with this view, because denitrification is influenced by a number of environmental and biotic factors, including both carbon and nitrogen availability. Please refer to some published paper, such as Xiong et al. Environ. Sci. Technol., 2017: 5483–5491.
7. Lines 275-276: Nitrification potential is controlled mainly by environmental factors, although nitrification is a microbial-driven process. In many cases, gene abundance has no significant relationship with nitrification potential. Therefore, the authors should discuss this result carefully based on previous studies, such as Yao et al. RSC Advances, 2018, 8, 1875-1883.


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: USING IPOMOEA AQUATIC AS AN ENVIRONMENTAL-FRIENDLY ALTERNATIVE TO ELODEA NUTTALLII FOR THE AQUACULTURE OF CHINESE MITTEN CRAB
Review round: 1
Reviewer: 2

Output:
Basic reporting: This paper studied the water quality and the bacterioplankton community among three kinds of earth ponds for Chinese mitten crabs with different macrophyte. Overall this is an interesting study. However, many issues must be clarified before its publication. The introduction provides insufficient background. I don’t think the conclusions were well supported by the results.
Experimental design: 'no comment'
Validity of the findings: 'no comment'
Additional comments: English should be improved dramaticly. I'm not a native English-speaker, but I can find many improper expressions, such as L 8 are high quality -> are of high quality

Waterweeds -> The weed means useless. I thought aquatic plants would be better.

Second, the tile is about mitten crab culture, but the paper focuses more on water quality, and ignored the culture itself. How about the economy? are the systems economically feasible?

Third, what kinds of materials are used for the patented matrix? I see plastics in the photos, that will produce microplastics, a kind of ECs, which is harmful.

Forth, EN is a cryophilic one, but IA and OS are thermophile. The experiments were conducted mainly in summer, so it 'unfair' to EN to compare the nutrition assimilation.

Finally, the bacterioplankton was only sampled once. That is not enough to a scientific research.

Specific comments:

Title Please re-organized to make it more specific. novel ->what kind of new? alternative to what?

L18 How about the water temperature?

L21 how about other submerged macrophytes such as eel grass?

L29 functionally: what kind of function?

L50 How about the arrangement of the three groups?  Did the three duplications of one group close to each other or separated by other groups?

L67 EN hill? what does it mean?

L87 I thought DO is very important. You can compare it in different ponds in at the same time. The floating system will evidently decrease the DO.

L103 Were the bacterioplanktons only sampled on one date? How about the biomass? If there's only relative abundance, the data will contribute little to the main topic.

L178 Where are the assimilated nitrogen from? You mentioned that the patented nutritional matrix containing sufficient nutrients.

L182 NO2-N was not detectable. I thought it can be deleted from the paper.

L245 How about TN in the downstream and in the inlet?

L248 I don't think these ponds are sources of pollution. I expect the water quality of inflows.

Figures:

Figure 2 L144 indicated there's no one-way ANOVA, but the figure displayed.

Figure 4 The water quality of inlet is expected.

Figure 5 What's the unit for vertical axis?


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: USING IPOMOEA AQUATIC AS AN ENVIRONMENTAL-FRIENDLY ALTERNATIVE TO ELODEA NUTTALLII FOR THE AQUACULTURE OF CHINESE MITTEN CRAB
Review round: 1
Reviewer: 3

Output:
Basic reporting: I think the basic reporting is excellent.
Experimental design: In general, the experimental design appears robust. My main comment about experimental design concerns just one aspect - the biomass estimates used to measure assimilated nutrients. I had trouble following how biomass was estimated, and what was the purpose/implication of the trimming that was done. For example, it is stated that 1m2 of plant material was collected; does this mean all plant material fitting into 1m2, or all the material within 1m2 of area in the ponds? I also do not understand the reason for the trimming of the plants, nor how exactly this trimming was done (e.g. was it done from all plants throughout the ponds, or just the plants at the edges of the experimental areas?). If the trimming was only done at the edges, how exactly did it act to keep a 60% plant cover (line 93) throughout the experimental area? It is good that “Trimmed plant tissues were included in the biomass production estimates” (line 94), but then the biomass estimates/assimilated nutrient measurements presented here only relate to situations where the growth has been modified by trimming, which may not happen in areas where the actual aquaculture is occurring. Overall, some more clarification about the information presented in paragraph lines 91-96 would be helpful.
Validity of the findings: I think the findings will be highly valid and useful for aquaculture and environmental management applications.
Additional comments: Firstly, I commend the authors for the excellent diversity of measurement types they took, which considered together produce an effective understanding of the system. Below are some minor changes that may improve the manuscript:

1)	One aim was to find a local plant species to use during aquaculture, because the previously used Elodea nuttallii is not native and has large mortality events during high temperature - this is not highlighted in the abstract. I think doing this would improve the abstract.
2)	line 24: add "that" between "plant" and "might"
3)	line 34: Change "In consider" to "Considering"
4)	Line 61: how was this 60% measured?
5)	Line 67: This mention of "hills" was unexpected. Please provide some background about this.
6)	Line 83: change “was” to “were”
7)	Line 96: I presume that here is referring to nutrient concentrations in the plant tissues - if this is correct, could you please state where the nutrient concentrations were obtained from.
Line 136-139: The quantification of nitrification and denitrification genes is an important aspect of the analysis but the method is only discussed in one sentence. Maybe this could be expanded, and especially a reference to another study or methods paper in which this has previously been done would be helpful.
8)	Line 160: The list here contains many correlation types. I think readers will be curious to know why so many were simultaneously used? (i.e. why not just choose the one most effective?)
9)	Line 231-232: please clarify this sentence.
10)	Line 236: change to "enter"
11)	line 258: add "that" between "exudates" and "drastically"
12)	Fig. 2 legend: These error bars seem quite small - please double check that they are really Standard Deviation and not Standard Error. Also for other bar graphs.
13)	Fig. 6: pH seems to drive differences in bacterial communities among treatments (Fig. 8), so I think it may be important that a formal comparison (e.g. ANOVA) is done for this variable (it does not seem like any comparison was done, only unanalysed means were described, line 192).
14)	Fig. 7b: I think there could be more discussion about this result – e.g. what are the implications for an aquaculture system to have high or low microbial diversity? Also, are these graphs showing averages, and thus should have error bars?
15) Fig. 8b: It may be useful to have some more explanation of what the graph represents. Most is self-evident, but it would be good to know details such as: if there are links between two parts of the graph, does that mean the correlation is significant? And I guess the width of the linkage relates to a strength of correlation value, such as R2? Details such as this in the figure legend would be helpful.


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

Input:
Title: USING IPOMOEA AQUATIC AS AN ENVIRONMENTAL-FRIENDLY ALTERNATIVE TO ELODEA NUTTALLII FOR THE AQUACULTURE OF CHINESE MITTEN CRAB
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The revised manuscript has addressed my questions well. I think it can be published.


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

Input:
Title: USING IPOMOEA AQUATIC AS AN ENVIRONMENTAL-FRIENDLY ALTERNATIVE TO ELODEA NUTTALLII FOR THE AQUACULTURE OF CHINESE MITTEN CRAB
Review round: 2
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: All the changes I suggested previously have been made. I have only a few more minor changes/suggestions, mostly related to small corrections to the language (the line numbers are from the tracked changes manuscript file).

Line 25-28: this sentence is a bit confusing, maybe “and” should be added between “waters” and “were”.

Line 32: Please add a mention here about what PICRUSt is.

Line 46: change to “crab”

Line 68: as “is” between “phosphorus” and “similar”

Line 78: change to “address”

Line 108: change to “pond”

Line 128: remove “~”

Line 156: add “were” after “that”

Line 227: I could not work out why P values were Bonferroni-adjusted. Please state here the reason for this adjustment

Line 259: is it meant to be “inlet” here instead of “inflow”? The figure listed here (line 261) shows differences among treatments, but I would hope all the “inflow” is the same among treatments (i.e. the same water supply flowing into treatments with the same initial nutrients), and only after being in the treatments there are differences. Either use a correct term instead of “inflow” (line 259) or please clarify exactly what is meant by this.

Line 270: switch positions of words “different” with “among”

Line 367: is this meant to be “denitrifiers are heterotrophic”?

Line 368: add “the” after “control”

Line 385: change “this” to “these”


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: HABITAT SUITABILITY AND CONNECTIVITY INFORM A CO-MANAGEMENT POLICY OF PROTECTED AREA NETWORK FOR ASIAN ELEPHANTS IN CHINA
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment.
Experimental design: No experiment was conducted, as this study is purely descriptive. However, the methods are generally adequate and appropriate.
Validity of the findings: The results support the conclusions, so long as semantic issues are rectified (see below).
Additional comments: The authors claim to measure habitat suitability and habitat selection, which is actually somewhat misleading. Habitat suitability typically refers to how fitnesses of individuals vary across habitats, while habitat selection infers an active choice by individuals and can only be determined experimentally. The authors are actually measuring habitat associations, which are simply statistical relationships between individual occurrences and various habitat features. I see this as more of a semantic issue that is easily rectified rather than a real problem with the methods. For instance, on line 223, it is stated that “elephants prefer forest matrix habitats…”. Just because there was evidence of elephants in those habitats does not necessarily imply that those habitats are preferred and would be most suitable (i.e., where fitnesses would be highest), especially given the great mobility and movement distances of elephants. They may simply be moving through in an attempt to find more appropriate habitat. A more accurate indicator of “preferences” would be the amount of time spent in each habitat and what they are doing in those habitats. The authors allude to that beginning on line 253, but it could perhaps be clarified. I suggest rewording parts of the manuscript, being careful to avoid using “habitat suitability” and “habitat selection” (e.g., on line 234 – that is simply associations) where that wording is misleading. “Habitat selection” on line 253 is fine because the authors are referring to a concept rather than what they actually measured.
Additional minor comments follow:
Line 57: “South and Southeast Asia are global hotspots): replace “are” with “contain”.
Line 64: “umbrella species” could be clarified.
Line 94: “co-management policy” and “a strict policy” are vague in this context.
Line 107: a reference should be cited for the meteorological data.
Line 124: “recorded with at least 200 m intervals” is confusing.
Line 143: I do not see that there is an explanation of how “town” and “community settlement” differ. Perhaps I am overlooking it.
The headings “Independent variables”, “Land-cover classification”, “MaxEnt modeling”, “Association between habitat suitability and level of economic development”, and “Pathway mapping” are all subsections of “Data analysis” rather than sections that are distinct from that section.
Line 268: “community-own” should be “community-owned”.


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: HABITAT SUITABILITY AND CONNECTIVITY INFORM A CO-MANAGEMENT POLICY OF PROTECTED AREA NETWORK FOR ASIAN ELEPHANTS IN CHINA
Review round: 2
Reviewer: 2

Output:
Basic reporting: Generally, the article is concise and uses professional English. The goals, methods, results, discussion and conclusions are well-framed. There are numerous cases, annotated on the manuscript, where a sentence or phrase could be revised to make the authors' ideas clearer. Most of the suggested changes are minor in nature.
Experimental design: The study relies on a variety of sophisticated, and appropriate, techniques.
Validity of the findings: The data appear sound, and the complex techniques appear to have been used properly.
Additional comments: 1. Given the flexibility with which the parameters of the MaxEnt model can be chosen, it might be helpful to provide more detail on how the parameters were chosen.
2. The only large error I saw was in the Discussion section, Lines 238-245. The numbers identifying the connecting paths in the text do not correspond to the labels on Figure 3 or to the description of the pathways on Lines 210-215.   The discussion should be modified so that the comments refer accurately to Figure 3 and the comments in the Results and Discussion sections are consistent.
3. Several of the "Altitude" entries in the Presence Raw data show as "######", probably because the cells were designated as text. Clicking on the cell shows a number in the  box just above the spreadsheet. It might also be useful to indicate the units for the variables listed in the spreadsheets.


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: TRACKING NEONICOTINOIDS FOLLOWING THEIR USE AS COTTON SEED TREATMENTS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript is written in clear English and easy to understand.
The literature used and background are poor and not up to date on some points. I indicate below specific points that need better explanation and citation.
The only figure presented lacks data points, while error bars are missing. The soil data could have been shown in a nice figure, and the playa data are poorly presented in a table without statistics, so comparisons with previous work are difficult.
Experimental design: The design is proper for the objectives of the study.
More water sampling on the playa would have been desirable, but I guess there were budget limitations.
The analytical methods are good, but recoveries and limits of detection are not indicated in the text - limits of detection appear in some tables though.
Unfortunately, authors missed he opportunity to analyse for clothianidin residues in both plant and soil samples; this metabolite of thiamethoxam was only analysed in the playa samples. It is a pitty, since information about this metabolite in plant material is lacking, and the sampling design here would have been very useful in clarifying this important point.
The statistical analysis is poor, not well explained in the methods and almost unreported in the tables and figures; only some p values are given in the text.
Validity of the findings: The residue data presented are valid, but the presentation is quite poor.
Comparison of the data with previous studies could be improved, in particular the residues in playa water samples. No risk evaluation is done, and the only benchmark values cited are out-of-date. Authors should consult the latest regulations by the US EPA in regard to neonicotinoids in waters.
Additional comments: line 38: rather than “nitrogen-containing”, indicate these insecticides are “chloro-nicotinic” compounds, because chlorine gives them stability and nicotine is their base.
line 39: the citation Main et al. 2014 is not very appropriate in this context; a better one would be Simon-Delso et al. 2015, Environ. Sci. Pollut. Res. 22, 5-34.
line 41: better say “…include mainly seed coatings.”
line 44-5: this statement requires a citation(s). Suggestion: Bonmatin et al. 2015, Environ. Sci. Pollut. Res. 22, 35-67.  Please add also that natural waters are usually turbid and these half-lives are, therefore, longer - check the IUPAC database on pesticides, http://sitem.herts.ac.uk/aeru/iupac/atoz.htm
line 51: that regulation by the European Community was superseed last year; see Official Journal of the European Union L 132, whereby the same three compounds were banned from application outdoors - they can only be applied in glasshouses.
line 57: in this context, please cite Sanchez-Bayo et al. 2016, Front. Environ. Sci. 4, 71
lines 57-9: no, Hallmann et al. 2014 did not report on migratory waterfowl, but on small insectivorous birds! Waterfowl usually do not feed on insects but on algae, grass and other plant material.
line 61: yes, neonicotinoids are more selective not only for pests but also for parasitoids and natural enemies, unfortunately. Please indicate this drawback, because it is one of the criticisms made of this class of compounds, and the reason why they are not welcomed in IPM programs.
lines 68-70: this comment should be backed up by citing the work by Balfour et al. 2016, Agric. Ecosyst. Environ. 215, 85-88.
line 81: sorry, but authors assume that only chemicals can offer protection against early pests, whereas the reality is different. Ladybirds and other natural enemies are the best protectors of the crop at these early stages, so if we use neonicotinoids as seed treatments, they are eliminated completely. Please indicate here that there are other ways of containing the early outbreak of aphids and other suckers. You can refer to Furlan et al. 2018, doi:10.1007/s11356-017-1052-5
line 105: how far apart were the treated rows?
line 106: are pivot sprinklers the most common irrigation system in Texas? This may not be representative of the common practices for this crop, although it is OK for the purposes of the study. Other countries prefer flood irrigation, which will move the residues in the soil among all plants, treated or untreated.
line 108: insert a subheading “Sampling”
line 118: indicate how the soil was collected, i.e. auger, hand-held core, scoop…I don’t understand what “Eight cm” of soil means in this context; shouldn’t be  “Eight cm deep core” or equivalent? What was the approximate mass of the samples?
line 132: were the water samples collected in amber or dark containers/bottles? If not, the residues analysed would be compromised by photolytic degradation in the containers.
line 234: insert a subheading “Sample analysis”
line 136: this procedure is for determining the dry soil weight, so indicate its purpose here.
line 133: the expected analytes would be the two applied (imidacloprid and thiamethoxam) plus the metabolite clothianidin. I’m surprised to see that authors analysed the metabolite in water samples but not in the others. This is a missed opportunity, since the same analytical effort is necessary for analysing two or three compounds in a given sample. In particular, it would have been interesting and novel to report the levels of clothianidin in the leaves from thiametoxam-treated plants…
line 174: apart from the analytical methods, a summary of extraction recoveries for each matrix (leaves, soil and water) should be presented. Also, limits of detection and quantification for both HPLC and LC/MS methods should be indicated either in the text on in the respective tables.
lines 176-80: this section is poor. What comparisons were made? For instance, how would you compare the levels of the residues among the three playas? Student t-tests are not applicable in this case. Also, did you test the assummptions of normality of the data distributions? Residue levels of chemicals in environmental samples usually follow logarithmic distributions, so transformations of the data are necessary to achieve normality and use statistical tests such as the t-test. Furthermore, the soil data allows for estimation of a rate of disappearance from the field, as the late samplings were done about 150 days after planting of the seeds. This information is important, and is typically expressed as half-lives.
line 187: what about clothianidin?
lines 192-3: to make sense of these concentrations you must refer to the days after planting; e.g. 31-36 days for the 18 ppb values and 21 days for the 10,600 ppb.
lines 194-220: these paragraphs should be summarised and refer to the days after planting in order to understand the differences in residue levels.
lines 224-5: along the same lines as above, indicate in the text the difference between high and low values. Calculation of a dissipation rate (half-live) with time is feasible: you only need to combine all the data points from the various locations, as shown in Figure 1, and plot them against the number of days after planting.
lines 231: alternatively, you can also calculate the rate of residue change between the two sampling dates at the same locations.
line 255: please, cite here Balfour et al, 2015.
line 261: “previously reported” requires a reference.
lines 270-93: as for the residues in leaves, please summarise the findings and refer to the days after planting to understand the dissipation of the soil residues among the various locations.
lines 314-5: this is an important finding, and since 80% of the coating remains in the soil (Goulson 2013), it should be stressed here that the seed-treatment results in a long-term contamination of the field, which for compounds like imidacloprid appear to accumulate year after year (see Jones et al. 2014, Pest Manag. Sci. 70, 1780-1784); thiamethoxam may not accumulate because it is converted to clothianidin, but this metabolite is very persistent in soil - see in this regard Schaafsma et al. 2016, Environ. Toxicol. Chem. 35, 295-302. and Limay-Rios et al. 2016, Environ. Toxicol. Chem. 35, 303-310.
line 317: indeed, that appeared to be the case in the experimental work reported by Sanchez-Bayo et al. 2007, J. Environ. Sci. Health B 42, 279-286.
line 317-9: degration rates may vary among the two conditions you mention, but in the case of very soluble compounds like neonicotinoids, it is not degradation as such (i.e. chemical decay and biological metabolism) that is crucial but the actual dissipation rates due to losses by leaching and runoff. These two factors prevent accumulation of residues in the field to a certain point, because half of the amounts applied as coatings will dissolve in water after a rain or irrigation event and move into the nearby drains or percolate (ie. leaching) through the soil profile and contaminate the ground water - see Gupta et al. 2008, Bull. Environ. Contam. Toxicol. 80, 431-437.
line 322: please cite here Jones et al. 2014
line 323: it is not only a “possibility” but rather a fact; there is plenty of evidence of this, and for the USA please refer to Hladik and Kolpin 2014, Environ. Pollut. 193, 189-196.
line 324: as said above, not just run-off, but mainly dissipation by leaching - see also Wettstein et al. 2016, J. Agric. Food Chem. 64, 6407-6415.
lines 335-41: this paragraph should be moved into the Methods section.
line 344: better indicate the actual water solubility of the two compounds used in this trial, which is well known and reported.
line 249: insert a subheading “Playa samples”
line 351: indicate the actual percentage of positive samples (47%) instead of an approximate number.
line 366: please explain here the reason for adding clothianidin to the list of analytes of the playa samples, whereas it wasn’t included in the soil or leaf samples. After all, the contamination of the waters comes from the soil and perhaps leaves.
lines 371-81: these statistics should be included in Table 3 as well - see comment below.
line 418: the current EPA acute bechmark values for imidacloprid is 0.385 ppb; the chronic benchmark is 0.01 ppb.
line 422: there is an acute benchmark for thiamethoxam in the USA, established as 17.5 ppb by the EPA - please, update your reference sources.
lines 425: obviously, some of the samples exceed the current EPA benchmark values.
lines 435: temporal sampling was obtained in this study for the soil residues.
lines 443-5: please, cite here Hladik et al, 2018, Environ. Pollut. 235, 1022-1029.
line 445: in fact, tilling may increase the leaching potential of these soluble compounds, whereas the more sustainable practice of non-tilling reduces their leaching potential.
line 462: see comment above in regard to aphids: there is hardly any need to apply neonicotinoids for controlling aphids when natural enemies are used under IPM programs; let alone for re-application.
line 467: this is a rather misleading statement; as mentioned above, IPM practices may render neonicotinoid application unnecessary and in fact damaging to the IPM itself.
line 475: add to the sentence “…and move into waterways nearby and groundwater.”
line 480: please revise your conclusions after taking into account the current EPA benchmarks.
line 486: you could cite here the correlaton study by vanDijk et al. 2013, PLoS One 8, e62374.
Table 1: suggest adding a column to indicate the number of days after planting
Table 2: these data would be better shown in a figure, plotting the average residues (plus error bars) against the days after planting. In that way we can visualize the trend with respect to the application day.
Table 3: the raw data in this table are not helpful; a summary of the detections, average and highest levels, and statistical differences among playa types would be more meaningful. You may need to swap the rows and columns to present the data in this way.
Figure 1 presents the same data as in Table 1 except that a couple of data points apperar to be missing for each compound - there are 8 different data point in Table 1, but only 6 here. Error bars are also missing.


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: TRACKING NEONICOTINOIDS FOLLOWING THEIR USE AS COTTON SEED TREATMENTS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The article is well-written. It provides a clear background and justification for the study and  pertinent literature for context. The manuscript presents good data obtained from diverse media, insecticides and scenarios with high relevance in meeting the aim of the work.
Experimental design: The article fits well within the aims and scope of PeerJ.
The aim of the manuscript is clearly defined and relevant. Even more relevant and elaborate is the research design, thereby ensuring the aims are met. The relevance of this article to a clearer understanding of the fate of neonicotinoids is not in doubt. The experimental design appears well-thought through and represent good quality methodology. The use of LC-MS was revelant for detection of very low quanitities of insecticides as reported in the work.
The sampling procedure is clearly explained for the various types of samples: leaves, soil and water.
My comment is on the sampling proceedure for soil:
The authors explanation of sampling 15 cm from the plant makes a lot of sense. However, if  the aim is to track neonicotinoids following their application as seed treatment, then leaving out a potentially large concentration of the applied insecticide possibly present in the seed coating or remains, may not give a good estimate of exposure in the environment. Possibly, a suggestion to the effect that, potentially large amounts of insecticide may be present around location of the seed will be help enrich the study.
Sur & Stock (Bulletin of Insectology 56 (1): 35-40, 2003) has shown that <5% of imidacloprid used in seed treatment in cotton is taken up by plants.
Such an estimation based on knowledge  of concentration applied neonic and concentration found in cotton leaves following germination will be a good idea.
Validity of the findings: There is a great deal of data presented which is good and provides good validation for the study. However, this advantage of a large pool of data makes reading of the results (particularly without ready access to tables) rather difficult and boring. while I belive this will improve when the final article is ready, generalised discussion highlighting the major differences or similarities in results rather than the mention of almost every single value for  the various pesticides, media sampling dates and sampling sites may be ideal.

The authors have provided a good discussion of the results obtained and provided sufficient reasoning or plausible explanation for findings. The data is well analysed statistically and the inclusion of models to further predict fate in the environment in commendable.
In table 3, detected limit is indicated as 0.05 ng/mL. However quantification limit is not inidicated. It would be important to indicated the LoQ as values presented are based on quantification instead of detection. This is expectially because values of 0.1 and 0.2 ng/mL (very close to LoD) have been reported as quantified (for clothianidin).
Additional comments: As indicated by the authors, the scope of work was broadened as work progressed further enriching the manuscript. However, I believe a clearer background in this respect would be ideal here.
For instance, while the study was focused on imidacloprid and thiamethoxam, other neonicotinoids were analysed for in water samples. This background was lacking and hence the first appearance of clothianidin or acetamiprid outside of literature appears out of place.
Kindly edit the following:
line 24 "as a result in" may read "as a result of" or "may result in"
line 55. consider replacing the word charismatic
line 57 & 58 may read "A possible connection between declines in migratory waterfowl, reduced aquatic invertebrate populations along migratory pathways and neonicotinoid use..."
line 64: but the issue may read. although this assertion...
line 77-79: particularly imidacloprid and thiamethoxam may come right after neonicotinoids in line 77
line 166: conducted instead of conducting
line 171: used
Consider moving reference in line 388 tp 385
line 467: consider "for" instead of "of"
line 472: consider underestimation


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: SELECTION OF REFERENCE GENES FOR QUANTITATIVE REAL-TIME PCR ANALYSIS IN CUCUMBER (CUCUMIS SATIVUS L.), PUMPKIN (CUCURBITA MOSCHATA DUCH.) AND CUCUMBER–PUMPKIN GRAFTED PLANTS
Review round: 1
Reviewer: 1

Output:
Basic reporting: Well done.
Minor:
Lines 58/59: Formatting error
Line 112: Please add the authors for all species you mention in the complete text not only for Cucumis sativus.
Formatting of the of the reference genes (in Italics) has to be carefully checked in the complete manuscript. There are more formatting issues that need to be carefully corrected.
Reference in line 486 is not in alphabetical order. There is a disproportionally high number of references published by Asian/Chinese authors. There are many more relevant publications from authors from all over the world. Please carefully address this point.
Experimental design: Abstract
The abstract provides all information in a condensed way.

Introduction
In the introduction many studies mentioning many putative reference genes are listed. What could be added is a more detailed compilation of the problems that might occur when the reference genes chosen are not experimentally verified. This aspect is still not taken into account in many publications which often leads to the uncritical application of Actin as a reference gene for many different cultivation conditions.

Material & Methods
Line 154/155: Please be more specific about the unpublished data. It might be more scientifically meaningful to publish the unpublished data set together with the analysis of the reference genes submitted in this manuscript.

Results
The paragraph starting in line 222 is very long and need to be structured. In additions some sentences could be written in a clearer way. Please carefully improve this paragraph for better readability.

Discussion
Part of the discussion is a repetition of aspects mentioned already in the other parts. Please try to reduce and be more specific with respect to your data.

Conclusions
This important part of paper needs to be more carefully arranged and completely rewritten because of incomplete sentences and repetitions.

Supplementary
The supplemental data files need meaningful legends, best summarized in a legend file. The note in Table S1 is not clear and the sentence and the described fast hast to be described in more detail.
Validity of the findings: The data are well presented and the description and conclusion based on the data are plausible and evident.
Additional comments: The authors carry out a very broad study investigating 12 different reference genes. There are no technical concerns on the execution of this study. However, this paper is a very technical paper as the authors also state in their cover letter. My major concern is that it could be part as a supplement of a publication that deals already with a real biological research question instead of being published by its own.


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: SELECTION OF REFERENCE GENES FOR QUANTITATIVE REAL-TIME PCR ANALYSIS IN CUCUMBER (CUCUMIS SATIVUS L.), PUMPKIN (CUCURBITA MOSCHATA DUCH.) AND CUCUMBER–PUMPKIN GRAFTED PLANTS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Li et al. reports the optimal reference gene to normalize the expression data for qRT-PCR in cucumber, pumpkin and cucumber-pumpkin grafted plants by four statistical tools. Eight candidate genes were tested under various conditions, and most constant expression genes were defined as candidate reference genes. This study is a well-organized and thorough to identify optimal reference genes. However, the current manuscript is missing several important requirements for data presentation and methodology explanation. I provide major and minor points to revise.
Experimental design: No problem.
Validity of the findings: There is no large impact but meaningful.
Additional comments: Li et al. reports the optimal reference gene to normalize the expression data for qRT-PCR in cucumber, pumpkin and cucumber-pumpkin grafted plants by four statistical tools. Eight candidate genes were tested under various conditions, and most constant expression genes were defined as candidate reference genes. This study is a well-organized and thorough to identify optimal reference genes. However, the current manuscript is missing several important requirements for data presentation and methodology explanation. I provide major and minor points to revise.

<Major comments>
1. In my view, I do not find any citation of Figs 3 and 4 in the text. Please remove or cite them in the text.
2. Figure titles and legends are not written in proper manner. Some parts seems to be just copied, then titles include detailed panel information and legends are missing information needed to understand all presented figure panels. Please consider to revise them.
3. As the current study screened available references which have stable expression patterns under several stressful conditions, the authors could consider to inform such strategy in titles and introduction section.

<Point-to-point comments>
L167; don’t→do not
L177; H20→H2O
L186-187; This part should be explained in result section.
L208; It is the content of the method. Please move this sentence to the method section.
L224−233 and L310-312; These seem to be the content of the introduction. Please remove or explain them in introduction section.
L346; Here, some reference is required.
Gene names/transcripts should be written in italics, eg L77-78, L81-82, and L355. Please check throughout the manuscript and revise them.


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: SELECTION OF REFERENCE GENES FOR QUANTITATIVE REAL-TIME PCR ANALYSIS IN CUCUMBER (CUCUMIS SATIVUS L.), PUMPKIN (CUCURBITA MOSCHATA DUCH.) AND CUCUMBER–PUMPKIN GRAFTED PLANTS
Review round: 1
Reviewer: 3

Output:
Basic reporting: Miao et al. report on the evaluation of a reference gene set for the use in cucumber, Pumkin and cucumber-pumpkin grafted plants. The experimental procedure is sound and well described in good English language (judged as non-native speaker). Results, discussion, tables, figures and supplemental material are well written and documented. The raw data are shared. Literature is mostly documented (for missing references see below). The whole paper is well structured.
Authors refer to their own unpublished transcriptomic data (L155). This should be publishes before or along with the manuscript.
Experimental design: The experiments are sound and well described with some minor comment detailed below.
Validity of the findings: The findings are valid.
Additional comments: I have some comments on different passages of the text:

Title: delete "optimal". There is no proof that these are the best. Only for the current conditions, they may be the most suited reference genes.

Title (L3): include ...gene expression "data derived from" instead of gene expression in cucumber

L45: delete "optimal"

Introduction: Sentence and reference missing on the MIQE guidelines: Bustin SA et al. (2009) The MIQE Guidelines: Minimum Information for Publication of Quantitative Real-Time PCR Experiments Clin Chem 55:611-622 doi:10.1373/clinchem.2008.112797

L52: replace "always" by "usually"

L81-86: Unclear. The mentioned reference genes were used all together or one by one? Explain the "specific environments"

84: italics "Cucurbita pepo"

L92-97: name and function of the mentioned genes

L103: replace "gernerated" by "generated"

L104-107: provide reference after "...which are thought to be related to graft union healing in grafted cucumber..."

L117: give size or volume of the pot instead of cell number

L122: ...previously described (Fig S1). Please provide reference.

L139: replace "seedlings"  by "grafted plants"

L152: specify "other plants"

Why did authors not evaluate the "classic" reference genes in their transcriptomic data? This is missing.

L161: BLAST against what data base?

L163: rephrase sentence to "This resulted in ten and seven genes of cucumber and pumkin, respectively, which may be suitable as reference genes"

L168: provide reference for Primer Premier 5.0 software

L174: replace "the" by "an"

L176: give manufacturer of "Premix DimerEraser"

L193: Please provide reference instead of web page

L205: "eight genes used traditionally...and four potential (instead of "new") reference genes..."

L232: From here onward many abbreviations are used. These should be limited and better explained.

L241: Explanation of V2/3 value missing. Please add.

L222: The whole section should be shortened and summarized with a table if possible.

L299 & 300: "abnormally" is not a scientific expression. Please replace by proper term.

L338: replace "," with "."

L364: "Grafted plant is..." has nothing to do with the context of the manuscript. Delete.

L362: Conclusion: Authors did not comment on the importance of validation of reference genes for each experimental setting, organ, or  treatment. Please add.


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: SELECTION OF REFERENCE GENES FOR QUANTITATIVE REAL-TIME PCR ANALYSIS IN CUCUMBER (CUCUMIS SATIVUS L.), PUMPKIN (CUCURBITA MOSCHATA DUCH.) AND CUCUMBER–PUMPKIN GRAFTED PLANTS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors tried hard to improve according to the suggestions of the reviewers. In some aspects it might be too verbose now. Please try to focus on the most important aspects and shorten te results section.
The English language has to be corrected by a native speaker.
In my version are many blanks missing, mainly in the part added in red. It might be a version problem but has to be solved.
Experimental design: There are no technical concerns on the execution of this study.
Validity of the findings: There are no technical concerns on the execution and evaluation of this study.
Additional comments: My major concern is still that it could be part as a supplement of a publication that deals already with a real biological research question instead of being published by its own. The arguments of the authors are not convincinb to me.


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: SELECTION OF REFERENCE GENES FOR QUANTITATIVE REAL-TIME PCR ANALYSIS IN CUCUMBER (CUCUMIS SATIVUS L.), PUMPKIN (CUCURBITA MOSCHATA DUCH.) AND CUCUMBER–PUMPKIN GRAFTED PLANTS
Review round: 2
Reviewer: 2

Output:
Basic reporting: Thank you for the resubmission. I feel written texts are well proofreading, and very close to accept for publication. However, there are still some points that require revision, so please correct them.
Experimental design: No problem.
Validity of the findings: There is no large impact but meaningful.
Additional comments: Over the entire paper, there were several points that did not have the required space, such as before and after the parentheses or after the comma. Please insert correct spaces.

Figure titles of Fig. 1, 2, and 3 contain the contents of figure legend. Please remove the contents of the figure legend.

L202; Fig2 is the content of the result, that it is not suitable to be in Materials & Methods.


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: SELECTION OF REFERENCE GENES FOR QUANTITATIVE REAL-TIME PCR ANALYSIS IN CUCUMBER (CUCUMIS SATIVUS L.), PUMPKIN (CUCURBITA MOSCHATA DUCH.) AND CUCUMBER–PUMPKIN GRAFTED PLANTS
Review round: 2
Reviewer: 3

Output:
Basic reporting: This is the review of the revised version of the manuscript. Most comments are presented in the attached documents. Here, only some general comments:
1. many spaces between words missing.
2. Manuscript needs careful English editing.

The manuscript is not ready for publication in its current state. I suggest a minor revision.
Experimental design: na
Validity of the findings: na
Additional comments: na


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: VALIDATION OF PLASMODIUM FALCIPARUM DEOXYHYPUSINE SYNTHASE AS AN ANTIMALARIAL TARGET
Review round: 1
Reviewer: 1

Output:
Basic reporting: In this manuscript, the investigators evaluate whether hypusination, a post-translational protein modification, is essential in P. falciparum malaria parasites. Using a glmS riboswitch, the investigators reduce expression of PfDHS, an enzyme required for hypusination. Immunoblot analysis indicates a significant reduction in PfDHS-GFP levels, although protein is still present. Hypusination levels are modestly but reproducibly decreased to 30% of untreated levels (Fig. 3), even with maximum reduction of PfDHS-GFP protein levels. With maximum reduction of PfDHS-GFP protein level, parasite morphology remains grossly normal. Using a competitive growth assay and comparing relative parasite levels by qPCR, the investigators conclude that reduced DHS protein levels cause a modest, albeit significant, reduction in asexual parasite replication. Overall, this is a clearly written manuscript that provides initial evidence on the biological function of a possibly essential gene in malaria parasites. In general, replicates are well described and adequate, and analyses are transparent and statistically rigorous. There are a number of minor concerns noted. Specifically, several conclusions are more strongly stated than is warranted by the data presented.  In addition, because the growth defect is so modest and the data presented has larger-than-expected biological variability, additional data should be provided in support, as noted below. Specific comments are noted below:
Experimental design: 1) Fig 4a. I understand why the investigators chose to use growth competition given the modest effect on parasite growth by reduced DHS. However, the data presented in Fig 4A is not quite convincing. The biological variability of the 5 mM GlcN samples (see t=6 in particular) is wide, and substantially larger variability is seen for this strain than, for example, DHFR (Fig 4C). I would prefer to see the data in terms of % parasitemia. The investigators suggest that this method is preferred over correcting for dilution factors, but it would be preferable to present those data side-by-side for direct comparison.

2) In addition, I suggest softening the language, as the data presented is promising but not sufficiently definitive to conclude that “PfDHS gene is essential” (line 548). Certainly, PfDHS is not a highly promising drug target, if >5-fold reduction in activity leads to only a modest growth defect after multiple cycles of asexual growth.

3) The investigators should also soften the language linking the phenotypic effects of reduced DHS levels to reduced hypusination. Many metabolic enzymes have “moonlighting” functions that do not depend on their catalytic activity, and therefore the cellular function of DHS may be broader than just hypusination. A better control would be integration of a “catalytically dead” version of this protein, so that enzymatic activity and hypusination could be distinguished from any other cellular roles.

4) The investigators should soften the language with respect to GC7. Specifically, the data presented does not definitively confirm the in vivo target of GC7 (line 522-523). Although this compound appears to inhibit DHS in vitro, it is not clear that its antiparasitic effects are mediated exclusively through DHS. Since “off target” effects are possible (even likely at high concentrations), sensitivity to this compound is suggestive but far from definitive.
Validity of the findings: As noted above, conclusions are somewhat overstated and alternative explanations for findings have not been discussed.
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: VALIDATION OF PLASMODIUM FALCIPARUM DEOXYHYPUSINE SYNTHASE AS AN ANTIMALARIAL TARGET
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper is clearly written for a general audience, provides adequate context and motivation for the work done, and includes legible and informative figures/tables to support the manuscript text.
Experimental design: The central research questions related to whether dehydrohypusine in Plasmodium plays an essential role and its potential as an antimalarial drug target are clearly stated. Appropriate experiments explained in sufficient detail to allow repeating are carried out with adequate rigor. Prior work on this gene in Plasmodium has been published, but direct information on its likely essentiality had not been reported until this manuscript.
Validity of the findings: Experimental data is accompanied by appropriate controls--e.g. use the functional glmS ribozyme for controlling gene expression is paired with a control using an inactive version of this ribozyme, and these are used together throughout the manuscript.
Additional comments: Overall, the manuscript is clearly written and provides useful additional findings to the existing literature.

Two minor points to address are:

1) In the Results and again the Discussion sections (e.g lines 446-452 ), the authors attempt to justify why the PfDHS enzyme is more likely essential based on the frequency of proteins with poly-Pro motifs in various proteins (including non-essential genes. This could be true. At the same time, though, if only one essential poly-Pro-containing protein were dependent on DHS function this enzyme would also be essential. Thus, a more balanced (though not necessarily exhaustive) discussion exploring why PfDHS function could be essential should be considered.

2) Lines 527-528. The statement “Low EC50 rations is consistent with off-targeting” is not always true and should be revised for improved accuracy. An alternative explanation, for example, could be that target protein expression levels after knockdown relative to what is needed for parasite survival is modest, and similar compound concentrations are required to abrogate function of the target protein


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: VALIDATION OF PLASMODIUM FALCIPARUM DEOXYHYPUSINE SYNTHASE AS AN ANTIMALARIAL TARGET
Review round: 1
Reviewer: 3

Output:
Basic reporting: Line 381: It is not clear what is the puromycilation signal. I suggest to add one sentence for explanation.

Line 532-535: The sentence "this number is markedly fewer than in yeast (Li et al., 2014) and other lower eukaryotes (Mandal, Mandal & Park, 2014)." is ambiguous. Provide the number of essential proteins containing polyproline motifs per total protein numbers or its percentage in yeast and other lower eukaryotes clearly so that readers are able to compare. Also are they significantly different between Plasmodium and others?

To discuss if the parasite molecule is a potential target of drug development, structural difference between parasite and human molecules would provide important insights. This pathway is well-conserved among eukaryotes, so discuss the feasibility of DHS as a drug target based on the structural dissimilarity or similarity in the discussion section.

I strongly recommend authors to supply legends for supplementary figures. Currently nothing is provided. Some are impossible to understand without the legend.
Experimental design: Line 381 and Fig S1C: Fig. S1C is not really sufficient to show the expected integration of the plasmid into the target gene locus. Southern blot analysis is required to show the integration to the DHS gene locus (glmS and M9) as was done for PfFC gene locus in supplementary Fig. S2. I guess the pattern of the lane 3 on the Southern blot in Fig S2 indicates disrupted gene locus and existence of the remaining episomal plasmid. Remaining plasmid could produce false positive by PCR.

Line 408. What is the effect of GlcN against the FC expression in PfFC_glmS parasite line? Why Western blot was not performed? Is it possible that the gene locus was disrupted and FC was not expressed anymore? If that is the case, 3D7 strain would serve as a control and I cannot see the rationality to use PfFC_glmS as a control. Comments?

In the conclusions, authors clearly state "Loss of PfDHS function leads to reduction of eIF5A hypusination,..". However, the claim that < 20-kDa band stained with anti-hypusine antibody was eIF5A was solely speculated based on the band size. Immunoprecipitation with anti-hypusine antibody and staining with anti-eIF5A antibody or mass-spec analysis with proper controls is suggested. Otherwise lower the tone.
Validity of the findings: Having a look at Fig. S6, I have a concern that authors might not clearly define the parasite stages; ring, trophozoite, and schizont. For example, "trophozoite"s indicated in A and C are actually schizonts as they have multiple nuclei. Also "ring" indicated in B is a trophozoite as this clearly contains hemozoin. This misclassification likely reflect analysis based on the stages, I suggest authors re-examine all images, re-classify the parasites for re-analysis.
Additional comments: Line 538-544 I feel there is a gap in the following argument: "P. falciparum also possesses a number of non-essential polyproline-motif proteins, including notably the erythrocyte membrane protein 1 family, which plays important roles in virulence (Deitsch & Hviid, 2004). Interestingly, polyproline motifs are also abundant in the variable surface glycoprotein (VSG) protein family of the African sleeping sickness parasite Trypanosoma brucei. Translation of VSG proteins is sensitive to eIF5A levels (Nguyen et al., 2015), possibly pointing to a similar mechanism for controlling expression of virulence factors among these highly diverged human parasites.". Polyproline residues may have structural function such as forming polyproline helices, which may be important for the protein-protein interaction, as a linker between domains in newly generated species-specific proteins, and so on. Any evidences suggest T. brucei use hypusinated eIF5 to control VSG expression? Do authors suggest involvement of eIF5 of T. brucei and P. falciparum in the antigenic variation? Unless authors provide more robust data or more comprehensive bioinformatics analysis including other eukaryotic pathogens, I would suggest to remove these sentences.


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: VALIDATION OF PLASMODIUM FALCIPARUM DEOXYHYPUSINE SYNTHASE AS AN ANTIMALARIAL TARGET
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: The authors have addressed my previous concerns with this manuscript and I have no new concerns.


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: VALIDATION OF PLASMODIUM FALCIPARUM DEOXYHYPUSINE SYNTHASE AS AN ANTIMALARIAL TARGET
Review round: 2
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: The manuscript is significantly improved. However, I have still one concern regarding Fig. S2. I agree with the authors about the identity of the 6-kb band in Fig. S2C lane 3. If so, it is not recommended to show in Fig. S2B the expected modified gene locus by design, but not by the obtained data. Author should draw a schematic diagram including concatenated plasmid part for this transgenic parasite (an example is attached). The identity of this 6-kb band should be explained in the figure legend, too.
Validity of the findings: no comment
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: UNDERSTANDING THE NACL-DEPENDENT BEHAVIOR OF HYDROGEN PRODUCTION OF A MARINE BACTERIUM, VIBRIO TRITONIUS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The paper is interesting and acceptable for publication but requires minor revisions
Experimental design: Well done
Validity of the findings: Very good
Additional comments: Minor Revisions
1-	In line 137 Materials and Methods, The authors should mention the method they used to install anaerobic condtions in the batch fermentation for hydrogen production by  V. tritonius strain AM2 and also for E. coli strain JCM 1649. they should outline the method they used whether by sparging with an inert gas such as nitrogen or argon. If they did not do sparging then they should illustrate this in the paper as both Vibrio  and  E. coli are facultative anaerobes and can do self instaltion of anaerobiosis in closed system of fermentation. The authors should illustrate which one of these protocols was used.
2-	It would be good if the authors mentioned in the abstract and the text the maximum mole of hydrogen produced per mole of mannitol and also compare their results to previous studies results for same and some other carbon sources using same bacterium and some other phylogenetically close bacteria
3-	In legend of Figure 5  (line 5) the authors refer to triangles as mannitol consumption while in the Figure per se it is glucose consumption. They should fix this mistake in the legend.
4-	In legend of Figure 3 line 1 : put a space between the two words mannitolconsumption>>>>>> mannitol consumption
5-	In legend of Figure 5 line 1 : put a space between the two words glucoseconsumption >>>>>> glucose consumption
6-	Lines 432 and 440 the expression (terrestrial bacteria) is better to be (other bacteria)
7-	  Line 317 the expression (terrestrial microbial biocatalysts) should be (microbial biocatalysts other than marine originated Vibrio tritonius).


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: UNDERSTANDING THE NACL-DEPENDENT BEHAVIOR OF HYDROGEN PRODUCTION OF A MARINE BACTERIUM, VIBRIO TRITONIUS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The use of English should be rechecked. The section of Introduction and Discussion could be revised to make them more concise and easier to comprehend. The comments below might be useful in revising the manuscript.

1) Please check spelling, e.g. favourable (Line 33), controliling (Line 393).

2) Language should be checked throughout the manuscript to improve readability. Also, the use of punctuation marks, e.g. commas, need to be checked.

3) Please revise “Thus, potentially … terrestrial bacteria” (Line 81-84) to improve readability.

4) Line 85-89, and Line 98-102 seem to be irrelevant to the research question. Please consider revising.

5) In Table 1 and 2, if a, b, c, and d were used to indicate significant differences, please place them where appropriate.

6) Please check Line 274-276 and Fig. 3.
Experimental design: The research question was well defined. However, more information and revision are required in order for the manuscript to be suitable for publication. The following comments might be useful in revising the manuscript.

1) Please clarify why E. coli was used as a reference in the present study.

2) Conditions for organic acids and mannitol determination, e.g. mobile phase and flow rate, should be provided (Line 175-178).

3) Eq. (4) was not used in the present study. Please consider revising.

4) Please give details about how microbial growth kinetics, i.e. maximum number of organism, maximum specific growth rate, and lag time, were determined. It would be better if the authors show these results in the manuscript.

5) To my understanding, Eq. 6 is not the modified Monod model reported in the study of Han and Levenspiel (1988). It, instead, shows how the reaction rate constant changes as a function of inhibitor concentration. Please consider revising.

6) Please explain how relative activity (%) in Fig. 2 was calculated.

7) Please explain how substrate conversion efficiency (SCE) was calculated.
Validity of the findings: More explanation and discussion are required for sections of Results and Discussion. However, these sections should be kept concise. The following comments might be addressed to improve the manuscript.

1) Please explain why molar yields of acetate, lactate, succinate, and ethanol were important, so that these should be determined.

2) Although the concentration of formate was determined during the course of fermentation, this might not be adequate to draw a conclusion that hydrogen production by V. tritonius was by FHL-complex. Please explain more on this point.

3) Since E. coli is not a halophile and the conditions for E. coli fermentation were different from those used for V. tritonius, it might be inappropriate to compare the hydrogen production between the two microbial strains (Line 336-338).

4) Please explain more on "Concurrent investigation ... from glucose" (Line 338-340).

5) Please explain more on "Moreover, Casey et al. (2013) ... Saccharomyces cerevisiae" (Line 363-365).

6) Please add a reference for "A genome analysis ... hydrogen formation" (Line 379-381).

7) Conclusions should be rewritten based on the results obtained in the study. Please also consider revising "On the other hand, .... hydrogen production" (Line 435-438) as this was not supported by the results.
Additional comments: The idea of using a marine bacterium to produce hydrogen from marine biomass is interesting as this could alleviate the effect of salt on the bacterium performance. However, the manuscript needs to be revised in order for it to be suitable for publication. More specific comments were given and these might be addressed for the improvement of the manuscript.


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

Input:
Title: UNDERSTANDING THE NACL-DEPENDENT BEHAVIOR OF HYDROGEN PRODUCTION OF A MARINE BACTERIUM, VIBRIO TRITONIUS
Review round: 2
Reviewer: 1

Output:
Basic reporting: Well done
Experimental design: Well done
Validity of the findings: very good
Additional comments: Well done revision


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

Input:
Title: UNDERSTANDING THE NACL-DEPENDENT BEHAVIOR OF HYDROGEN PRODUCTION OF A MARINE BACTERIUM, VIBRIO TRITONIUS
Review round: 2
Reviewer: 2

Output:
Basic reporting: Please recheck carefully the writing to correct typing and grammatical errors.
Experimental design: No comment.
Validity of the findings: Although the authors have made revisions according to the previous comments, I would like the authors to address the following comments for further revisions of the manuscript.

1. Line 227, should Eq. 3 be Eq. 2?

2. Line 243, it would be better if the authors report the growth data of AM2 in the manuscript. This is to show how AM2 responded to the increased NaCl concentration.

3. Line 266, please show the non-competitive inhibition model used to fit the data shown in Fig. 2. Also, please explain why n=2 was used.

4. Line 281-282, the authors stated that substrate conversion efficiency (SCE) was used to determine the effects of various salts level on substrate consumption. However, no SCE (%) is presented in the manuscript. Please consider revising.

5. As far as I am concerned, Fig. 2 is misleading. Since the relative activity was calculated by dividing ln(r) of each NaCl concentration by ln(r) of 0.5% NaCl, the relative activity of 0.5% NaCl should be 100%. I would like to suggest the authors adjust properly the scale of the secondary Y-axis. Please also explain what the gray line in Fig. 2 represents.

6. Please check the results shown in Fig. 4. The authors stated that 2.25% NaCl had achieved 42.3 mM formate (Line 374); however, the data point for 2.25% NaCl at 24 h is at around 37.5 mM.
Additional comments: The manuscript would be suitable for publication after minor revision.


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

Input:
Title: PATIENT-REPORTED FATIGUE IN PATIENTS WITH RHEUMATOID ARTHRITIS WHO COMMENCE BIOLOGIC THERAPY: A LONGITUDINAL STUDY
Review round: 1
Reviewer: 1

Output:
Basic reporting: Generally the reporting is clear, though there are some grammatical errors, some examples attached in the abstract, but would suggest a full review prior to resubmission
Experimental design: The aouthers defined the question well, though it was in a very specific population.
Overall the experimental design is fine are seems to have been carried out well with some minor reporting issues. The authors should have considered extending the recruitment period as 48 patients is an extremely small number to make any real assumptions about. Also the authors should have adjusted the analysis using baseline ffs.
Validity of the findings: It is difficult to make relationship assumptions based on such a small sample size. There is a great risk of type II errors and this may lead to an overemphasis on gender fatigue - also not assessed based on baseline FFS. I think the authors need to be clear in the abstract that this is an issue as well as doing adjustment analysis.

Also the authors haven't considered the role of individual biologics in this setting - these biologics have varied mechanisms of actions and this could lead to issues around fatigue. Given that there are five biologics it would be difficult to show statistical differences in the magnitude of effect in these numbers (compared to two genders).
Additional comments: Suggest needs to consider the reporting of the methods - critical appraisal checklist added to attached document