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: THE ADDITION OF VERY LIGHT LOADS INTO THE ROUTINE TESTING OF THE BENCH PRESS INCREASES THE RELIABILITY OF THE FORCE–VELOCITY RELATIONSHIP
Review round: 1
Reviewer: 2

Output:
Basic reporting: No comment - see general comments below
Experimental design: No comment - see general comments below
Validity of the findings: No comment - see general comments below
Additional comments: The aims of the study entitled « The addition of very light loads into routine testing of the bench press increases the reliability of the force-velocity relationship » were:
I) Test whether the evaluation of the force-velocity (F-v) relationship in bench press throw (BPT) using a machine-guided bar, which is the usual testing machine, could be replaced by a traditional bench press (BP) evaluation without guided bar.
II) Test whether the addition of very light loads to the F-v during traditional BP testing could improve the reliability of extrapolated parameters, notably V0.
III) Test whether the F-v relationship is still linear on the velocity side, which has not been experimentally explored in bench press of movement.
These goals were motivated because of technical issues specifically due to heavy machinery that lead the F-v relationship to be explored in a shorten range, notably closer to the force side. In consequence, the quality of the testing, that is, the reliability of associated parameters to define neuromuscular capacities, could be negatively influenced.
In general, I commend the good work done by the author and the excellent initiative toward improving strength & conditioning methods. Nevertheless, I believe that there is still a room for improving the manuscript. Therefore, the remaining text represents the list of my general and specific comments and suggestions, although, I will understand, with logical and justified answers, if author decide not to address all of them in the revised version.

GENERAL COMMENT:
For each section of the manuscript, the content is sufficient to well understand the manuscript and its goals. I also appreciate the effort of authors for the overall clear-written sentences. However, some additional information is still needed to facilitate the reading while other sentences should be deleted because there are not enough informative and make the reading difficult. Also, although I am convinced by the pertinence of the study, I would strongly suggest the authors to reorganize the order of presentation of the goals as suggested in the paragraphs above. I am convinced that would improve significantly the understanding and help readers to identify more easily the three main goals.
Please, feel all my comments as objective suggestions with no negative judgements and with the only idea to improve the understanding for all of your excellent manuscript.

SPECIFIC COMMENTS:

INTRODUCTION
Lines 59 – 61: Since the force-velocity relationship is related to the neuromuscular system force capabilities, I am concern about the role of osteoarticular system.
Could you explain and justify with appropriated references how the latter independently influences a force-velocity relationship?
Moreover, the power-velocity relationship is also well used to explore the function of the neuromuscular. This relationship should be presented at these lines and added consequently in the following sentences of the manuscript.
Lines 61 – 64: The main ability of muscle is to transform chemical energy into a mechanical force output. The movement velocity is a consequence and the power is a mathematical construction rather than “muscular productions”. Also, Pmax is not theoretical, it is surely attaint in numbers of movements such as squat jump or cycling.
I suggest authors to clarify this sentence and to consider the following suggestion: “The modelling of the F-V-P relationships in single- and multi-joint tasks, allows to determine mechanical limits of the neuromuscular system being theoretical maximal force capacity at null velocity (F0), the theoretical maximal velocity capacity until which the system is still able to produce force (V0) and the maximal power capacity (Pmax).
At line 64, To avoid any confusion, I would replace the word “property” by the word “characteristic” since the word “property” is also use to qualify muscles.
Lines 64 – 71: From my point of view, both sentences express the same idea. I would recommend to synthetize them into one sentence to shorten the reading as this idea is not the main point of the study.
Also at lines 67 and 68, I would suppress the brackets to define F0 and V0, which as already been defined in the above sentences.
Lines 80: If possible, I would add a small paragraph about how F-v relationship testing is usual done: number of loads, measurements (in laboratory and on the field), apparatus (e.g. force plate, phone). I am convinced that would help readers to understand the limitations of these procedures.
Lines 82 – 83: As this is the main issue, I recommend to introduce here the fact that, both, a wider range and the number of point as a direct impact on the reliability of the F-v relationship.
Lines 84 – 88: I would replace the word “unfortunately” by the word “However” since the latter does not include personal feelings.
Also at line 85, I recommend to clarify the fact that the range of loads is limited in some exercise because, on the field, technical supports to extend the range are not often easily available in contradictory to testing conducted in laboratory.
At line 88, could you justify how the smith machine is considered as a standard procedure?
The justifications should be added  in a short following sentence or associated to the previous sentence. I propose to replace the word for “the most common and often used method”.
Lines 92 – 96: The sentence should be clarified and authors could, if agreed, followed this suggestion “Since the minimum load imposed by the unloaded Smith machine system is approximately 17-20 kg, the resulting experimental points to determine the F-V relationship during the BPT exercise are generally closer to the force-intercept than to the velocity-intercept (i.e. force-biased).”
Lines 96 – 102: I would suppress these sentences because they address unclearly the main goals without being very specific. I recommend to replace this paragraph for quantitative information about how far the experimental points obtain with the smith machine is from V0. I would also add quantitative information about previous studies (if any) that have used very light load during BPT and measured force and velocity data or computed a force-velocity relationship. This would inform readers about the gap to fill until V0 is reached.
Lines 104 – 117: As previously suggested, I would recommend the authors to reorganize the order of the goals and to write specific sentences for each goal as readers can identify them easily.
At lines 104 to 106, I am concerned about the justification of the F-v relationship linearity testing. The authors should provide appropriate references to convinced readers that the linearity is still challenged.
At lines 115 to 117, the use of the words “to approximate” is not clear can you clarify this sentence?
Lines 119-138, I strongly advice authors to shorten this paragraph by suppressing lines 119 to 125 and directly introducing the main goal of the study. Since the paper is very short, there is no need to add a sum up, even less so the sum up is quite as long as the introduction. I am convinced that would help the understanding of the study. I also recommend to dissociate, in two separated paragraph, the aims of the study from the hypotheses with, both, short and precise sentences.

METHOD
Lines 142 – 144: I would shift the results about one repetition maximum (1RM) in BP toward the result section.
Lines 153 – 155: I would suppress this sentence, because, from my point of view, it does not help the understanding of the study design.
Lines 157 – 159: This sentence is not in line with a following sentence in the same section, which is: “The testing protocol of both testing sessions consisted of the traditional BP performed against six loading conditions and the ballistic BPT performed against four loading conditions.”
Actually, if I well understood, subjects performed two testing sessions: a F-v relationship testing in BP under 6 loaded conditions and a F-v relationship testing in Smith machine under 4 loaded conditions. Using 4 or 6 loads to compute different F-v relationships in BP is rather an analysis strategy. I would recommend here to suppress the bracket and just to introduce the F-v relationships determination for two movements in BP and BPT rather than with three methods.
Lines 160 – 169: This paragraph should be suppressed. From my point of view, it is confusing to address these specific points at the beginning of the method section when readers have few information about the whole protocol. Also, all of these information is almost all addressed in a next paragraph.
Lines 173 – 175: Could you be more specific about the joint warmed-up during the joint mobility exercises and the details of the jogging (duration and running velocity)?
Lines 175 – 178: Could you be more specific about the steps of increasing the load during the 1RM determination? Notably, how did the steps of increase 10, 5, 2, or 1 kg was chosen and what was the objective criteria to adapt the step.
Lines 178 – 180: I don’t understand why two repetitions were performed since this test is completed as the subject is able to perform just one repetition? Could you clarify why this was done?
Lines 186 – 188: I also don’t understand why subjects were to ask perform the repetition as quickly as possible. The aim here was to assess if the subject is able to lift the load rather than to throw as high as possible. Could you clarify why this was done?
Lines 188: The brackets are not clear; I would suggest authors to suppress it as it has been explained before.
Lines 188 – 192: These sentences should shift towards the next sub-section.
Lines 197 – 199: Could you explain why they performed BPT with the unloaded smith machine?
Lines 207: The 29kg of the unloaded smith machine is not similar as the data presented in the introduction: “The experimental points used […] the minimum load applied is approximately 17-20 kg (mass of the unloaded Smith machine) […].”. Could you clarify this point?
Lines 213 – 215: I would suggest the authors to precise that force and velocity data are computed from a linear transducer rather recorded. Also, the method to compute the force and velocity data from the linear transducer should be presented as well as the signal treatment (filtering or average moving window).
Also, while I respect the authors decision to focus on the propulsive phase, I would like to highlight that depending of the loading condition, the propulsive phase during BP do not consider the same push-off distance. The averaged force and velocity data come from more or less complete part of the movement (the lower the load, the shorter the push-off distance). In consequence, the data does not represent the subject capability to produce force in the same condition. Since the force-velocity relationship should represent so, could you justify how the use of the propulsive phase could be interpreted?
Lines 223 – 226: These sentences could be suppressed.
Lines 235: Could you rather express the standard error of measurement relatively to the mean of both sample? The SEM in absolute value does not fully inform about the error and can be bias depending on the magnitude of the dependent variable, as suggested By Hopkins in 2001.

RESULTS
Lines 253 – 255: I suggest the authors to change this sentence and only talk about individual results, since a mean F-v relationship across a sample is difficult to interpret; There is actually no interest to determine a mean F-v relationship across subjects except when team work is performed such as in rowing.
This suggestion is also applicable to the figure 1. I would prefer a figure with a typical subject rather than a figure that inform about the mean variability between subject which is not informative regarding the aims of the study.
Lines 273 – 278: The validity of BP with 6 loads against smith machine with 4 loads included different number of load and different range. I’m afraid that the effect of range and number of point may influence the potential link between BP and smith machine. This limitation is over come for the comparison of BP with 6 loads to smith machine with 4 loads. Can the authors justified why they decided to compare a 6 load methods to a 4 loads method to test the validity?
Overall, I strongly suggest the authors to add an additional table with mean +/- SD force, velocity and power across subjects for each loading condition in both methods. Firstly, it would help the understanding of the protocol and secondly the data could be used for potential meta-analysis or use as a scientific data base being a solid and quantitative knowledge.
DISCUSSION
Lines 347 – 352: I personally find this discussion very interesting and I think that adding the intra-subject coefficient of variation between the trials of the two light loads could strengthen the discussion and give very interesting information about future studies on the reliability of very high velocity movement.
Lines 283 – 285: I would recommend the authors to suppress this sentence.
Lines 286 – 294: I would reorganize the aims’ order as suggested above.
Lines 291 – 294: This sentence should be shift towards the conclusion section.
Lines 296 – 323: This paragraph is not clear. It is not possible to dissociate if some sentence are statements based on results of this study or other studies or either hypotheses. I suggest the author here to reorganize the paragraph and use results to support their statement which could help to clarify the outcomes of the study.

CONCLUSION
I would suggest the authors to also highlight that despite the fact that extreme point could increase the F-v quality by reducing the extrapolation of parameters of interest, on the over hand, due to the low reliability of these unusual movement, the positive effect could be turn into a negative effect. This point may catch attention about the importance of familiarization before using these extreme conditions into testing routine in order to avoid methodological bias.

REFERENCES
Authors’ references in the text is not conventional, when there are more than 2 authors in publication, only the first author’s name and the formulation “et al., + year of publication” should be cited, otherwise the both authors name should be cited. This comment should be applied to entire the manuscript.
Also, the citation of articles in the reference section are not suitable. I recommend the authors to check the review's guidelines.


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: THE ADDITION OF VERY LIGHT LOADS INTO THE ROUTINE TESTING OF THE BENCH PRESS INCREASES THE RELIABILITY OF THE FORCE–VELOCITY RELATIONSHIP
Review round: 2
Reviewer: 1

Output:
Basic reporting: I believe that the authors have done an excellent job and should be commended on their reporting. The English was excellent, they have provided a great background, and the tables and figures are of a high quality. Well done.
Experimental design: The research question is clear and the investigation was rigorous. All methods were well described.
Validity of the findings: This is a well designed study that has good impact and is novel.
Additional comments: Well done on this manuscript. It is great to see more research in the velocity based training, force/power area. I look forward to seeing this in print in the near future.


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: THE ADDITION OF VERY LIGHT LOADS INTO THE ROUTINE TESTING OF THE BENCH PRESS INCREASES THE RELIABILITY OF THE FORCE–VELOCITY RELATIONSHIP
Review round: 2
Reviewer: 2

Output:
Basic reporting: I would like to thank the authors to have some much consideration for both reviewers’ comments and suggestions. The detailed revision of the manuscript is highly appreciated, as well as the honest and justified answer that the authors provided.
I feel that the manuscript is almost ready to be published since few important details need to be still discussed or adjusted.

ABSTRACT
Lines 29 – 30: I would replace a part of this sentence:
“The aim of this study was to examine whether the addition of very light loads for modelling the force-velocity (F-V) relationship during the bench press exercise can increase its linearity […]”

by

“The aim of this study was to examine whether the addition of very light loads for modelling the force-velocity (F-V) relationship during the bench press exercise can confirm its experimental linearity […]”

METHODS
Line 199 – 201: I thank the authors for being more specific about the computation but the way to compute the force need to be more detailed. I’m concerned about the fact that the force computation, if I well understood, is F = Total mass . (gravitational acceleration + barbell acceleration).

My first interrogation: is the total mass comprise the mass of the barbell, the additional mass and the mass of the upper limbs?

Secondly, have you quantified the frictional force of the smith machine? because it should be added to the computation.

My thinking is based on the study of Rahmani et al in 2001 where they detailed the usual computation to estimate the force production during a bench press movement:

(Abderrehmane, R., Fabrice, V., Georges, D., & Lacour, J.-R. (2001). Force / velocity and power / velocity relationships in squat exercise. European Journal Of Applied Physiology And Occupational Physiology, 84, 227–232. https://doi.org/10.1007/PL00007956)

The computations being F = (mul + mb) . ab + (mul + mb) . g + Ff

With mul, the masse of the upper limbs, mb the mass of the barbell, ab, the acceleration of the barbell, g the gravitational acceleration and Ff, the frictional force.

The authors should confirmed their computation or, unfortunately, re-analyzed the data to compute the force production :

1) To get the true value because such data could be used later in other study analysis

2) because, although excluding the mass of the upper limb during the heavy loading condition could be negligible, during the very-light load conditions, the mass of the upper limb would be substantially higher than the mass of the barbell, and in turn, influencing greatly the force production.
Experimental design: See commentary above
Validity of the findings: See commentary above
Additional comments: See commentary above


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

Input:
Title: THE ADDITION OF VERY LIGHT LOADS INTO THE ROUTINE TESTING OF THE BENCH PRESS INCREASES THE RELIABILITY OF THE FORCE–VELOCITY RELATIONSHIP
Review round: 3
Reviewer: 1

Output:
Basic reporting: See commentary below
Experimental design: See commentary below
Validity of the findings: See commentary below
Additional comments: I would like to thank again the authors to have some much consideration in writing their manuscript and getting perfectly involved in collaboration with reviewers !
I encourage them to continue their works in this field !

Enjoy the published paper !


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

Input:
Title: MIGRATION AND TRANSFORMATION OF DISSOLVED CARBON DURING ACCUMULATED CYANOBACTERIA DECOMPOSITION IN SHALLOW EUTROPHIC LAKES: A SIMULATED MICROCOSM STUDY
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comments
Experimental design: well designed. but still need some improvement
Validity of the findings: Some conclusions are not well supported by the data in the study
Additional comments: The manuscript written by Li et al. detailed changes in dissolved organic and inorganic carbon in both overlying water and pore water was monitored and diffusive fluxes of DOC at the sediment-water interface was calculated. It is significant in understanding carbon cycling in water- sediment interface after settlement of cyanobacterial biomass. However, some revisions should be done to improve the manuscript.
1. Some conclusions are obvious, for example, more cyanobacteria more DOC. Suggest to analyze contributions of per amount of cyanobacterial biomass to DOC and DIC and make a conclusion.
2. Suggest monitoring POC concentration which would be vital for description of carbon cycling.
3. The title should be corrected. Actually, the research was conducted in microcosm system in laboratory, and just using the sediment and cyanobacteria collected from Lake Taihu. The system is much simper than the situation in situ. So “in shallow eutrophic lakes” in the title should be changed to “in simulated microcosm system”, or something like that.
4. Environmental conditions in microcosm were different from lake environments. Discuss how the results from the microcosm were applied to interpret the effects of cyanobacterial biomass decomposition on carbon cycling in lakes.

Some minor comments
Line 22, Provide the biomass for the increased TDC of 1900.0mg/L?
Line 28, what did the low biomass referred to, was it general?
Line 29-30, What is the reason for this transportation
Line 33-34, “with the maximum value of 411.01 mg/(m2·d).” what is the cyanobacterial biomass corresponding to this value?
Line 35, “presented a faster degradation of DOC” should be “presented a faster degradation to DOC”?
Line 37, “biological structures of lacustrine sediments” is not investigated in the paper, should limited to addition of cyanobacteria.
Line 41, both gaseous carbon and cyanobacteria-derived POC were not detected, so the conclusion was not well supported by the data provide in the study.
Line 130-131, the weight is wet or dry? It is better to indicated by biomass.
Line 134-135, the biomass of cyanobacteria was 5 cm-10 cm in accordance with that in field, was the length of plexi-glass tube coincides with the height of water column?
Line 186, decomposition process of cyanobacteria began after 10 days? From the data of figure 5, DOC began to increase much earlier than 10 days. So the conclusion was arbitrary.
Line 202 “with added cyanobacteria biomass” refers to all tubes with addition of various amounts of cyanobacteria or in each tube
Line 216, what are the later stages of incubation? Please give the incubation days
Line 262, it is reasonable that more cyanobacteria lead to more carbon involved in the cycling, but cycling model is similar, the study did not clearly illustrate what is the difference of migration and transformation processes of DCs among additions of different cyanobacterial biomass.
Line 351-354 the conclusion of methanogenesis, transformation cyanobacteria-POC into volatile organic carbon was not directly supported by the data in this study.
In figure 9, the diagram of carbon transformations is well known. Suggest to quantity the amount of transformation between carbon based on the result of this study. In addition, some DOC may be also assimilated by bacteria thus transformed to POC.


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: MIGRATION AND TRANSFORMATION OF DISSOLVED CARBON DURING ACCUMULATED CYANOBACTERIA DECOMPOSITION IN SHALLOW EUTROPHIC LAKES: A SIMULATED MICROCOSM STUDY
Review round: 1
Reviewer: 2

Output:
Basic reporting: This study is to test the migration and transformation of dissolved carbon during accumulated cyanobacteria decomposition in shallow eutrophic lakes. The author find that the decopmosition of the accumulated cyanobacteria can change the carbon cycling in eutrophic lakes and will possible induce the cyanobacteria related water pollution. The paper is well designed and discussed detailly. However, there are still some questions problems that should be clearly stated before acceptence.
Experimental design: Line 111-113. The setence should be writed with caution.
Line 116-117. This might not the main reason which responsible for the formation of black water bloom.
line 130-134. The biomass of cyanobacteria is wet or dry? This is very important parameter in the experiment.
Validity of the findings: The abstract should be re-wrote and it seem very complex in its present state.Please make concise of the manuscript.
Additional comments: This paper descrice the dynamic carbon in wate and sediment during the decopmsition of cyanobacteria and the results were useful to the understanding of C cycling in eutrophic lakes. However, further study should relate these process with microbia activity.


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: MIGRATION AND TRANSFORMATION OF DISSOLVED CARBON DURING ACCUMULATED CYANOBACTERIA DECOMPOSITION IN SHALLOW EUTROPHIC LAKES: A SIMULATED MICROCOSM STUDY
Review round: 1
Reviewer: 3

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Comments to #28549, “Migration and transformation of dissolved carbon during accumulated cyanobacteria decomposition in shallow eutrophic lakes”.

Cyanobacerial bloom has been a big problem in shallow eutrophic lakes for decades, which plays a significant role in carbon cycles in these lakes. However, the chemical and biological mechanisms involved in cyanobacteria affecting carbon cycling in shallow lakes remains largely unknown. Therefore, this manuscript “Migration and transformation of dissolved carbon during accumulated cyanobacteria decomposition in shallow eutrophic lakes” provide more information concerning this issue. This manuscript can be published after some revisions.

Major comments:
1)	Abstract
Firstly, the abstract are too long and not well written. Some information are not clearly stated in the abstract.
Is it an in-site microcosm or incubation experiment in the lab (I found the answer in the end of the Instruction)? How long did the experiment go on? It was mentioned “In the early incubation” and “latter incubation”, what are the exact days? For example, L14-15 and L19-20 are repeated to the results and should be deleted.
I recommend the author re-write the abstract and make it clear and brief.

2)	Materials and Methods
The 1st section of Results and Discussion is about “Visual changes and physicochemical environment associated with DC release”. However, in M&M, nothing was mentioned about how these visual changes (Fig. 3) was measured.
Do you have the chemical and biological characteristics (e.g., pH, Temp., phosphorus, and nitrogen levels, and Fe, etc.) of the lake water when collected? These data are important to estimate the chemical and biological activities during incubation.
Even if these parameters are not analyzed in this study, I am sure there are plenty data available in previous publications, which can also give a background information of the water conditions.

3)	Results and Discussion
Somehow, I feel the big weakness of this study is lack of biological explanations of the transformations among of DC, DOC, and DIC. The authors gave too much emphasis to physical “immigration”. This may due to there are only carbon data in this study.
The decomposition of cyanobacteria can release carbon substrates and nutrients (P, N, and trace metals) which support microorganism growth in the water column. The growth of microbes utilize DOC to generate CO2 (DIC), which called mineralization. Microbial mineralization of DOC to DIC plays a crucial role in C cycling in freshwaters.
Another way for providing the nutrients to support microbial growth is sediment-release. This can explain the phenomenon in this study where “sediment increased the transformation intensity from DOC to DIC (L280-280)”. Therefore, it is important to know the P and N levels during these processes. The variation of phosphorus concentration may not be easy to detected, but it is possible to measure other parameters e.g., Fe concentration. Fe is usually bound by P and organic carbon in the sediment. The changes of Fe is a good indicator for the P release from sediment.
Abiotic (photochemcial) mineralization also plays a role in this process. However, there is no light-effect information in this study. In M&M, the authors only mentioned that “the upper parts of the plexi-glass tubes were opened and their entire sides protected from light” (L137-138).
I recommend the authors can add some discussions concerning the microbial and photochemical mineralization mechanisms to explain the phenomenon observed in this study.
Other comments:
(1)	L48-51, please correct this sentence.
Two ambiguities:
 a) what is the definition of ”sediment overlying water”? Does it mean the whole water column or only a few centimeters above sediment?
b) only dissolved organic carbon absorbs light.
(2)	L107, please give information how the data of Figure 3 was measured.
(3)	L128, is this 40cm×π×4.42cm2 correct? how much water added?
(4)	L142, please give full name for DO and Eh when first being used.
(5)	L142-143, what is the model of water quality monitor?
(6)	L148-150, please give more information how TDC and DIC are measured by using multi N/C® 3100.
(7)	L169-170, please indicate the significant level and also how D-value was calculated in this study.
(8)	L183-184, there is no evidence for the EPS formation.
(9)	L187, what do you mean with “in overlying water became thicker with low density”? thick and low density?
(10)	L190-191, this is too farfetched. In this study neither Fe nor S concentration was measured, so one can not be sure this is related to the settle down of FeS. The settle down of FeS can be make sure by measuring the concentration of FE and/or S in the water.
(11)	L206-207, correct the sentence, “The incubations were alkaline at the beginning of the experiment”.
(12)	L279-281, add discussions concerning microbial and photochemical roles in this process, see main comments 3).
(13)	L284, consider to change the order of Fig. 6 and 7. It seems Fig. 7 appears in front of Fig. 6 in the text.
(14)	L349, delete “ecological indicator”.
(15)	The legend of Figure 2 is misleading. Consider to change “in lakeshore of Taihu Lake” to “in the laboratory”.


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: MIGRATION AND TRANSFORMATION OF DISSOLVED CARBON DURING ACCUMULATED CYANOBACTERIA DECOMPOSITION IN SHALLOW EUTROPHIC LAKES: A SIMULATED MICROCOSM STUDY
Review round: 2
Reviewer: 1

Output:
Basic reporting: The quality of this paper has been improved a lot after revision.
Experimental design: The experimental design was reasonable and scientific feasible.
Validity of the findings: The finds is important to understand the carbon cycling in freshwater lakes.
Additional comments: All of the consieration has been answered and this paper can be accepted in its present situation.


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: MIGRATION AND TRANSFORMATION OF DISSOLVED CARBON DURING ACCUMULATED CYANOBACTERIA DECOMPOSITION IN SHALLOW EUTROPHIC LAKES: A SIMULATED MICROCOSM STUDY
Review round: 2
Reviewer: 2

Output:
Basic reporting: no comments
Experimental design: no comments
Validity of the findings: no comments
Additional comments: Reviewer #3: I appreciate the authors’ revisions considering my comments on the original submission. The manuscript is now much better presented than the original version.
Some minor comments,
(1)	In abstract, L32, maybe it is better to change 1823.7 mg/L to 1.82 g/L;
(2)	L53-56, this long sentence is not correct or accurate. “DC can be found in the whole water column, not mainly found in …..”. I know the author want to emphasize the importance of overlying water and pore water, but this sentence needs to be modified.
(3)	L125-126, what is measured? Please modify or delete this sentence.
(4)	L153-155, this long sentence need to be simplified. It is not clearly stated. The same problem can be found in L221-225, a very long sentence, it is hard to catch the main point. I suggest the authors rewrite these sentences and replace with short and clear 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: EARLY IDENTIFICATION OF RECURRENCE IN OVARIAN CANCER: A COMPARISON BETWEEN THE OVARIAN CANCER METASTASIS INDEX AND CA-125 LEVELS
Review round: 1
Reviewer: 1

Output:
Basic reporting: In general I believe that it is a quality paper with interesting and relevant results, taking into account the small sample size as mentioned by the authors.
The English would require some small improvements (please refere to the comments I the attached file).
Literature references are adequate.
Experimental design: This paper deals with an important and original topic, supported by robust methods and statistics. Moreover it meets the aims and scope of this journal.
The authors adequately included the informed consent.
Validity of the findings: As above mentioned this paper addresses an important and novel subject showing interesting and relevant results. The presented statistics are meticulous. However, the results need to be further validated with larger samples.
In my opinion, the conclusion could be rewritten in a more concisely and straightforward manner.
Additional comments: No further 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: EARLY IDENTIFICATION OF RECURRENCE IN OVARIAN CANCER: A COMPARISON BETWEEN THE OVARIAN CANCER METASTASIS INDEX AND CA-125 LEVELS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The English language should be carefully revised to improve the clarity of the scientific message. For example, lines 60 (“Thus far, …”), line 75 (”By such an  …) and line 191-193 (“The high degree…”) should be rephrased.
Experimental design: In the introduction, the authors did not refer to NCC which is used to compare results with CA-125 assay in the result section (Table 1, Table 2 and Figure 2). OCMI should be better defined in the introduction as a hybrid model of NNC and multiple linear regression as defined in the Material and Methods section.

Results Section: Metastasis and multi-organ metastasis should be better defined. Metastasis refer to peritoneal metastasis? And Multi-organ metastasis refer distant metastasis (e.g. lung) or refer to organs within the peritoneal cavity (e.g.liver)

Figure 1: Graphic A should be reformulated to show that within the “Active responders” which ones respond negative.
Validity of the findings: Discussion: The final message should be positive and demonstrative of the strong points of the presented work. The limitations should be discussed in the beginning of the discussion.
Additional comments: Wang F. et al presented a work with ovarian cancer patients to evaluate the precision rate of the ovarian cancer metastasis index (OCMI) to predict disease recurrence. The results where compared with classical follow up biomarker (CA-125) and Neural network cascade (NCC). Authors showed that OCMI ROC was 0.856, NNC ROC 0.804 and CA-125 alone was 0.752. Moreover, OCMI level predicted recurrence earlier than CA-125 values (1 chemotherapy cycle earlier).  The improvement of OC recurrence prediction is of paramount importance and the idea of refining the already available follow up methods would accelerate the implementation of this improved method in to the clinical. The aim of this work is therefore very significant but the present manuscript require some alteration in order to clarify the results.


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: EARLY IDENTIFICATION OF RECURRENCE IN OVARIAN CANCER: A COMPARISON BETWEEN THE OVARIAN CANCER METASTASIS INDEX AND CA-125 LEVELS
Review round: 2
Reviewer: 1

Output:
Basic reporting: In general I believe that it is a quality paper with interesting and relevant results, taking into account the small sample size as mentioned by the authors.
The English would still require some small improvements (please refere to the comments I the attached file).
Literature references are adequate.
Experimental design: This paper deals with an important and original topic, supported by robust methods and statistics. Moreover it meets the aims and scope of this journal.
The authors adequately included the informed consent.
Validity of the findings: As above mentioned this paper addresses an important and novel subject showing interesting and relevant results. The presented statistics are meticulous. However, the results need to be further validated with larger samples.
Additional comments: No further 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: EARLY IDENTIFICATION OF RECURRENCE IN OVARIAN CANCER: A COMPARISON BETWEEN THE OVARIAN CANCER METASTASIS INDEX AND CA-125 LEVELS
Review round: 2
Reviewer: 2

Output:
Basic reporting: As suggested the English language was improved.
Experimental design: The authors addressed all questions and/or suggestions required to refine the scientific message of the manuscript.
Validity of the findings: As suggested the Discussion section was improved.
Additional comments: The authors addressed all questions and/or suggestions required to publication.


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

Input:
Title: MICROBIOME DIFFERENCES BETWEEN RIVER-DWELLING AND CAVE-ADAPTED POPULATIONS OF THE FISH ASTYANAX MEXICANUS (DE FILIPPI, 1853)
Review round: 1
Reviewer: 1

Output:
Basic reporting: This manuscript is written in a clear professional English with a good logical-flow. Literature reference and background information are sufficient and adequate. The manuscript structure, figs and tables meet requirement of proficiency, and Raw sequence data was shared. Authors provided clear hypothesis "cavefish and surface fish have distinct gut microbiota" and their result did not support. I suggested slightly adjusted hypothesis that their result supports.
Experimental design: The experimental design meets the aim and scope of PeerJ: The good quality of original research in Biological Sciences. Research question is clear and well defined. I found a potential major issue that authors did not enphasize how they chose stomach as the tissue they studied. The midgut and hind-gut are more popular to investigate the gut microbiota composition. Authors need to provide clear explanation for it. Nonetheless, the result filled the gap of the knowledge of the gut microbiota compositions in the wild surface fish and cavefish. The study meets high technical and ethical standard, and the described method is sufficient to replicate by others.
Validity of the findings: Authors' finding is surprising to me because there is no difference in between gut biota compositions of surface and cave populations. Instead, there was a difference between populations living in different oxygen concentrations. Authors suggested further investigations in other cave populations to enrich the full-view of the symbiotic evolution between the gut microbiota and cavefish. I personally would like to see larger sample size per population (N ~ 8) rather than N= 2~3 in this study. However, I understand that there is a high hurdle to sample wild-cavefish because these populations are endangered.
The most of data and analysis seems robust. I left comments where I wondered such as Fig. 5: In this figure, Prevotellaceae is extremely high in RM1 individual. I would like to know there is no technical error (such as a bug in their script) in the analysis. The conclusion follows what they found, and is linked with original questions. Authors did not make any unreasonable speculations.
Additional comments: The followings are line-by-line comments

L25: “Stomach biopsies…”
I assume that authors meant stomach microbiota. Biopsy is confusing because authors euthanized fish and dissected out the entire digestive tract. Biopsy is, in general, taking a sample tissue from a living organism. I first thought that authors recovered the stomach microbiota by using a thick syringe needle in the field.

L33: “beta-diversity”
It is difficult for non-ecologists to recognize what beta-diversity is. You may state “stomach microbiota composition” or else instead of beta-diversity. However this is my personal opinion.

Introduction:
Authors wrote a quite good summary to inform about the gut microbiota. Can authors use the term “commensal” in the Discussion section starting from L328- “Symbionts and pathogens in A.mex microbiome”? Authors made a good job to discuss about opportunistic/pathogenic bacteria in the later of this discussion section. The first half of this section seems for commensal bacteria. It will be clearer for readers if you declare that you start talking about commensal bacteria.

L71 reference “(Jeffery 2009; Gross 2012;…)
As a suggestion, you may add “(Keene et al., 2015)”  Keene AC, Yoshizawa M, McGaugh SE: Biology and Evolution of the Mexican Cavefish. Amsterdam: Elsevier Inc.; 2015.

L79-L82: this sentence is too long so that confusing. You may split it into two sentences.

L88: references for olfactory capabilities, you may add:
(1) Blin M, Tine E, Meister L, Elipot Y, Bibliowicz J, Espinasa L, Rétaux S (2018) Developmental evolution and developmental plasticity of the olfactory epithelium and olfactory skills in Mexican cavefish. Dev Biol in press. Available at: https://doi.org/10.1016/j.ydbio.2018.04.019.
(2) Protas M, Tabansky I, Conrad M, Gross JB, Vidal O, Tabin CJ, Borowsky R (2008) Multi-trait evolution in a cave fish, Astyanax mexicanus. Evol Dev 10:196–209.

L95-L97: “Differences between surface and cave-dwelling populations…”
This sentence describes authors' initial aim. However, the result does not support it. Although PeerJ can accept negative result, to impress readers positively, I suggest authors to restate. For example, “Determining the degree of the contribution of biotic and abiotic factors that are associated with the stomach biota composition, in the present study, we compare the [stomach] microbiome of cave and surface A. mexicanus, in order to…”

Method:
Sample size is substantially low (N=2~3 per pop) by taking account of the high variability of gut microbiota, which can change between different ages, different diets, and sick vs. healthy states in human (Luzupone et al 2012***). However, I understand that it is difficult to gather large sample sizes for endangered populations. I believe that authors’ data is still informative for cave animal societies.
I have very limited knowledge for Ion Torrent system, thus, cannot evaluate the validity of how author processed. Besides of it, checking V2-V9 regions of rRNA genes is solid and valid, ANISOM analysis seems valid too.
L173: typo in “OTUS”, it should be “OTUs”.
L177: Please provide the submission number for SRA

*** Lozupone CA, Stombaugh JI, Gordon JI, Jansson JK, Knight R (2012) Diversity, stability and resilience of the human gut microbiota. Nature 489:220–230.

Results:
There is no major issue in Result. It was well written and easy to follow the logical-flow.

L187 and L189: Please provide brief explanations for “Chao index” and “Simpson index” for non-ecologists.

L248: Just double check if “226 S/cm” and “580 S/cm” are still right digits. I think these are extremely high. For example, Rohner et al. 2013 reported that Nacimento Del Rio Choy was 1324 µS, which is 0.001324 S/cm.

Discussion:
L291-L293: It may be good to emphasize A. mexicanus. For example, “using different amplicon regions is beneficial to the studies of the A. mexicanus microbiome too.”

In the section of "Environmental factors influencing microbiota diversity of A. mexicanus."
Please discuss a possibility that cave and surface populations eat different diets that influences their gut microbiota. It is critical to refer this. You may refer [Espinasa L, Bonaroti N, Wong J, Pottin K, Queinnec E, Rétaux S (2017) Contrasting feeding habits of post-larval and adult Astyanax cavefish. Subterr Biol 21:1–17.]

Fig 1.
Lost a red line from Pachon fish. Provide explanations what blue and yellow shades represent (lakes and cities?), and what hatched and solid blue lines stand for.

Fig. 2.
Color codes are difficult to follow. You may make them solid colors instead of gradient colors, and draw arrows between the index color boxes and bar graphs. You may draw arrows only the major taxonomic goups including Firmicutes, Beta-proteobacteria, gamma-proteobacteria, and Actinobacteria.

Fig. 3.
Please show the relative abundance of bacterial genera for 52 that shared between M and P, also show 44 that is unique for R. these graphs inform the candidates that are sensitive for oxygen concentration.

Fig 5
Please double check if Prevotellaceae is truly accumulated in RM1 rather than calculation-mistake. This odd score or Prevotellaceae might skew the conclusion although authors wisely chose rank-test for most of the stats.


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: MICROBIOME DIFFERENCES BETWEEN RIVER-DWELLING AND CAVE-ADAPTED POPULATIONS OF THE FISH ASTYANAX MEXICANUS (DE FILIPPI, 1853)
Review round: 1
Reviewer: 2

Output:
Basic reporting: No comment.
Experimental design: The Introduction could use some improvement on framing the study in light of current knowledge of fish microbiomes and vertebrate gut microbiomes in general. There are some more recent reviews on both that can be found in Shapira (2016); Colston & Jackson (2016) and I recommend Vatsos 2016 for experimental design considerations specific to fish microbiome studies.

Additionally the authors need to address how differences in diet and environment between these populations (particularly cave vs surface) could influence their findings. Omnivorous fish tend to have gut microbiomes similar to free-living communities in the water column whereas that isn't necessarily the case for strict carnivores. In some cases gut microbiome isn't lined to ecotype or diet (Sullam et al. 2015). It is unfortunate that the authors did not sequence environmental samples as a control and comparison, as this extremely limits the ability to draw conclusions from their results.

The methodology regarding sample collection needs to be expanded. As written it is unclear whether fish were collected and stored in native water or water that was sterilized prior to sample collection or the conditions under which dissections were made to ensure sterility. The authors do not specify the amount or type of gut material used in extractions. After dissections were samples stored at room temperature or flash frozen? All of these minutia must be detailed in microbiome studies both for purposes of evaluating methodology and for replication.
Validity of the findings: I can only comment that the rigor of the analyses are sound but without clarification on collection methods and controls in sampling design there is not enough information to verify the validity of the author's claims.
Additional comments: This is a very interesting and important study. I do think that results could be biased by comparing 2x the number of surface samples and populations to a single cave population. I appreciate that the authors have used multiple primer sets to evaluate the efficacy of a single set to yield comprehensive data. However, there is a wealth of information on fish microbiomes (reviewed in Colston & Jackson 2016) to which the authors could add their data for a meta-analyses type study on this topic, too.

Finally, when making concluding statements such as "...resembles that observed in other fish groups..." etc the authors need to specify the taxonomic level to which they refer. In the broadest sense 16S surveys of vertebrate guts suggest all vertebrate gut microbiomes "resemble" one another so this statement carries little weight.


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: PROMOTERPREDICT: SEQUENCE-BASED MODELLING OF ESCHERICHIA COLI Σ70 PROMOTER STRENGTH YIELDS LOGARITHMIC DEPENDENCE BETWEEN PROMOTER STRENGTH AND SEQUENCE
Review round: 1
Reviewer: 1

Output:
Basic reporting: Bharanikumar with coauthors developed a regression model to predict the strength of E. coli promoters. Paper is clearly structured and written. Raw data and results of modeling are available
Experimental design: Authors use 13 (actually twelve as promoters BBa_J23103 and BBa_J23112 are the same) to create the linear regression model describing dependency of a logarithm of activity from sequences in -10 and -35 boxes of the promoter. It is known that in average from 12 base pairs in two boxes (-10 and -35 hexanucleotides) only eight is conserved. Together with variation in spacer length, it makes not unusual that one promoter can equally good match several combinations of the boxes and spacer. Authors do not discuss how they choose positions in promoter sequence to calculate position weight matrices (PWMs).
Authors use the approach similar to one provided in Rhodius and Mutalik PNAS,2010. 107, 2854-2859. Rhodius and Mutalik use over 60 promoters in both in vivo and in vitro setup to investigate the correlation of sigmaE promoter strength with PWMs and penalty for non-optimal spacer length. The major concern about the design of computational experiment in the study under review is that the use the same small set of 12 promoters to get PWMs and learn regression coefficients. Together with three regression coefficients, authors learn 48 weights in two PWMs. The number of coefficients to find is higher than the number of samples, which opens the question about the validity of results. It would be interesting to compare your regression results with regression using more general promoter PWMs, obtained in the other studies, for example in Huerta AM, Collado-Vides J (2003) Sigma70 promoters in Escherichia coli: Specific transcription in dense regions of overlapping promoter-like signals. J Mol Biol 333: 261–278.
Validity of the findings: Authors do not test the predictive power of their model, restrict their self with analysis of 12 promoters in training set. However, over about 50 years of investigation of bacterial transcriptions, there are many studies comparing the strength of various promoters in different conditions (to name a few J. Mol. Biol. 1978 125, 467, Plasmin 1996, 35, 108,  J. Biol. Chem. 1984, 259, 1616). And despite that direct comparison of those result with each other is rarely possible this data could be used as independent validator set for the regression model provided in the paper. If regression results will be ordered in the same way as the strength value in experiment paper, it proves the validity of the model.
Another aspect missing in the paper is the validation of the model on negative results. It would be interesting to see what would be an average level of strength predicted by the model on non-promoter sequence set.
Additional comments: There are minor remarks on analysis of the regression. The fact that after training the model with combination term demonstrates lost of significance for all components of the model could also be an indicator of overfitting.


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: PROMOTERPREDICT: SEQUENCE-BASED MODELLING OF ESCHERICHIA COLI Σ70 PROMOTER STRENGTH YIELDS LOGARITHMIC DEPENDENCE BETWEEN PROMOTER STRENGTH AND SEQUENCE
Review round: 1
Reviewer: 2

Output:
Basic reporting: Correlation between the promoter sequences and their strength is a matter discussed from the very beginning of the promoter era. The further the more it becomes clear that the use of simple correlations usually leads to erroneous conclusions and any statement needs to be carefully checked. Now, there are many possibilities for this, including a huge amount of expression data that allow sequence-functions comparison for large sets of bacterial promoters. Why not to use them instead of an unrepresentative set of variants of the sequence of only one plasmid promoter.
Experimental design: Very bad: training set is basically unsuitable for predictive modeling.
Validity of the findings: Minor. There are several unexpected observations, but they are suspicious and convincingly not proven.
Additional comments: The authors proposed an approach realized as a freely available resource for predictive modeling of the strength of sigma-70 promoters. This is useful if not misleading. I'm afraid that the authors did not submit any data to prove the adequacy of their approach.

Major concerns:

1.	The training set gave consensuses substantially different from those that were created for the entire set of bacterial promoters. Therefore, its suitability for predictive modeling is very doubtful.
2.	The training set with 19 samples is too small for decent modeling. It contains identical sequences in both -35 and -10 regions. Thus, the actual number of variables for PWM generation in no way can be considered sufficient, and the authors did not discuss whether and how they took into account this similarity.
3.	The predictive ability of the software should be verified on some other data set(s). Several comparative sequence/strength studies were published 25-35 years ago, including exhausting mutagenesis in the same promoter. So, authors are recommended to find these data, starting, for instance, with an article of Knaus and Bujard (1990) ‘Principles Governing the Activity of E. coli Promoters”. In: Eckstein F., Lilley D.M.J. (eds) Nucleic Acids and Molecular Biology, but there are others.
4.	At least one of the three main findings of the study is very doubtful:  “The –10 and –35 sites were equally important in determining promoter strength”. It directly contradicts the existence of many promoters without the -35 element and must be carefully checked. It is unlikely that it will be confirmed on a representative set of natural promoters. In the second conclusion, that logarithmic scales give a better correlation between scores and strength, on the contrary, there is no novelty. There also an interesting statement that “the PWM—10 and PWM—35 scores were uncorrelated”, which should be validated by the whole set of E.coli s-70 promoters available in RegulonDB.
5.	At the end of the paper there is a statement that “The user is provided with an option to add any number of promoter instances with –10 and –35 sequences and the corresponding strengths to augment the training data of the supervised model.” It is unclear how the strength of the new promoters will be integrated into the existing set. At least strategically, the normalization method should be indicated.

Minor concerns:

1.	It should be clearly indicated that the training set was composed of plasmid tet promoter variants.
2.	All symbols used in the formula:  Adj. R2 = 1 – {(1-R2)*[(n-1)/(n-m-1)]} should be deciphered.
3.	It is not clear, why Biopython resource was required to convert frequency matrices into log-odds matrices? Too simple procedure to discuss it.
4.	Citing: “The two hexamers are located ~10 bp and ~35 bp upstream of the transcription start site, and are called the –10 and –35 sequences respectively (Paget and Helmann, 2003; 41 Kadonaga, 2012). Both -35 and -10 elements were introduced much earlier and must be cited properly.
5.	The statement: “Promoters with –10 and –35 sequences matching the consensus motif of the hexamers are typically stronger, meaning they initiate more transcripts per unit time than promoters with less canonical –10 and –35 regions” requires citation as well as mentioning of contradictive data as far as authors want to contribute to this area.


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

Input:
Title: PROMOTERPREDICT: SEQUENCE-BASED MODELLING OF ESCHERICHIA COLI Σ70 PROMOTER STRENGTH YIELDS LOGARITHMIC DEPENDENCE BETWEEN PROMOTER STRENGTH AND SEQUENCE
Review round: 1
Reviewer: 3

Output:
Basic reporting: The article proposes a method for predicting the strength of E. coli promoters on the basis of the regression model. The paper is written in professional English. It is structured in accordance with the requirements of the journal and contains raw data.
The article does not have enough literary references and a brief description of the results of other works in which attempts were made to develop computer methods for predicting the strength of prokaryotic promoters (for example, Michael DekhtyarEmail author, Amelie Morin and Vehary Sakanyan Triad pattern algorithm for predicting strong promoter candidates in bacterial genomes BMC Bioinformatics20089:233;  Marjan De Mey, Jo Maertens, Gaspard J Lequeux, Wim K Soetaert, and Erick J Vandamme Construction and model-based analysis of a promoter library for E. coli: an indispensable tool for metabolic engineering BMC Biotechnol. 2007; 7: 34.; Joseph H. Davis, Adam J. Rubin, and Robert T. Sauer Design, construction and characterization of a set of insulated bacterial promoters Nucleic Acids Res. 2011 Feb; 39(3): 1131–1141.).
Experimental design: Although now there are non-commercial programs for predicting the strength of prokaryotic promoters, they are not available online (Michael Dekhtyar, Amelie Morin and Vehary Sakanyan Triad pattern algorithm for predicting strong promoter candidates in bacterial genomes BMC Bioinformatics20089:233). The authors offered the first Internet-accessible program to solve this problem.
Based on the regression model, the authors analyzed 19 E. coli promoters and evaluated the contribution of weights of -10 and -35 promoter regions in the final strength of promoter. Unfortunately, the analyzed sample contains a significant number of identical promoter sequences having a similar or identical strength value. This can lead to a significant shift in the estimation of correlation and significance. The use of duplicates is especially dangerous for LOOCV methods, since the ejection of sequences one by one does not release the training set from the control sample.
In addition, Table 3 contains an arithmetical error in the calculation of 1, 5, and 11 rows (-4.6 - - 3.77! = -0.73), which also requires a recalculation of the results.
Validity of the findings: Unfortunately, the authors evaluated the effectiveness of the proposed approach only on sequences from a small training sample containing duplicates. It would be useful to test its effectiveness on other available experimental data (for example, Joseph H. Davis, Adam J. Rubin, and Robert T. Sauer Design, construction and characterization of a set of insulated bacterial promoters Nucleic Acids Res., 2011 Feb; 39 ( 3): 1131-1141.). In spite of the difference in the experimental approaches used, it is possible to obtain a general idea of the reliability of the proposed method on independent data. In addition, on random or non-promoter sequences, it is necessary to look at the distribution of the predicted sequence strength to estimate the error of the method's over-prediction.
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: PROMOTERPREDICT: SEQUENCE-BASED MODELLING OF ESCHERICHIA COLI Σ70 PROMOTER STRENGTH YIELDS LOGARITHMIC DEPENDENCE BETWEEN PROMOTER STRENGTH AND SEQUENCE
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors took into account the recommendations of reviewers and expanded the list of references.
Experimental design: The authors recalculated the data taking into account the detected errors, but Table 1 contains the old values of Predicted ln(Promoter Activity) and must be brought into line with the new results. For example, for hexamers TTGACG and TACAGT, the value -1.46 is indicated in the table, and the program returns -1.63.
Validity of the findings: The authors took into account the wishes of the reviewers and significantly expanded the set of test samples to assess the effectiveness of the proposed approach.
Additional comments: I have no doubt about the usefulness of article submission, but I would recommend to double-check all of the values in the article. In addition, I recommend that you change the settings for the ppp photo on the website, because when you scale the page, it significantly distorts.


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: PROMOTERPREDICT: SEQUENCE-BASED MODELLING OF ESCHERICHIA COLI Σ70 PROMOTER STRENGTH YIELDS LOGARITHMIC DEPENDENCE BETWEEN PROMOTER STRENGTH AND SEQUENCE
Review round: 3
Reviewer: 1

Output:
Basic reporting: Authors have improved manuscript and take into account all concerns of reviewers.
Experimental design: Authors incorporate both negative set analysis and additional promoter strength data.
Validity of the findings: Results are now statistically sound.
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: PROMOTERPREDICT: SEQUENCE-BASED MODELLING OF ESCHERICHIA COLI Σ70 PROMOTER STRENGTH YIELDS LOGARITHMIC DEPENDENCE BETWEEN PROMOTER STRENGTH AND SEQUENCE
Review round: 3
Reviewer: 2

Output:
Basic reporting: The authors took into account all the comments of reviewers and the article is ready for publication.
Experimental design: The authors took into account all the comments of reviewers and the article is ready for publication.
Validity of the findings: The authors took into account all the comments of reviewers and the article is ready for publication.
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: APPLICATION OF A MALDI-TOF ANALYSIS PLATFORM (CLINPROTOOLS) FOR RAPID AND PRELIMINARY REPORT OF MRSA SEQUENCE TYPES IN TAIWAN
Review round: 1
Reviewer: 1

Output:
Basic reporting: Line 47: Tone down the statement that the incidence of MRSA is rapidly increasing. At least fort he European countries, the incidence of MRSA infections are stagnating (see Germany, for instance: https://www.eurosurveillance.org/content/10.2807/1560-7917.ES.2015.20.46.30067).

Line 49: Please clarify what you mean by saying „relationship between the results of genotyping from multilocus sequence typing (MLST) and characteristics of MRSA strains“. Do you mean an association between genotypes and certain virulence factors?

Line 50: Use either „strain“ or „lineages“.

Line 53: It is true what is written here but this was the status almost 10 years ago. Nowadays, whole genome sequencing can be done within 1-2 days for less than 100 €. Sequence based typing methods are by far more discriminatory than anything else. So what is the clinical relevance of this study? MALDI-Tof based typing might have some value if transmission can be ruled out. But to confirm transmission, you definitely need more discriminatory power. Why is spa-tying not mentioned here?

The language is not clear and sometimes of poor quality in some sections. For instance Line 61: In what sense were the results varying? Line 62: If you start with „first“, one expects „second“, „third“ and so on. Line 67: What do you mean by „complicated data“? Line 81: write „to“ instead of „for“. Line 87: Do not start a sentence with digits. I strongly recommend that a native English speaker check the text again.

Line 62: Correct to „it may be due to several reasons“

Line 63: Add...“and the discriminatory power of MALDI-TOF might therefore differ when compared between different MRSA lineages.

Lines 137-138: Mention the ST and add (n= ) in brackets right after the ST. The numbers are very unclear, as it is written right now.

Lines 150-155: Add the OR, 95% CI and p-values in brackets for the association of peaks with the respective STs.

Line 158: Why are these data “preliminary”?

Line 161: Distribution of what?

Figures are ok, raw data are supplied.
Experimental design: What are thin inclusion and exclusion criteria fort he MRSA isolates? Indicate the year of collection.

Line 84: How did you rule out that Staphylococcus argenteus was not misidentified as S. aureus. S. argenteus is now considered to be widespread in Asia so this point need to be addressed.

Line 92: Bruker is based in Bremen, not Leipzig.

Lines 103-107: I gain the impression that the authors did not go carefully through the manuscript before submission. In this paragraph, there are so many mistakes that could be easily avoided: aroE not areE, glpF not glp, arcC not araC. Please adhere to the nomenclature for MLST as suggested by Enright et al.

Line 114 (reference): GmbH is probably not the author!

Statistical analysis: please include a section in Materials and methods as well in the results to calculate the performance of MALDI compared to MLST (sensitivity, specificity, PPV, NPV etc.) In the end, the reader wants to know: how likely is the Maldi-typing result true.
At the end of the discussion: add a section on the limitations of the study
Validity of the findings: Line 182-183: I do not agree with the conclusion that MALDI can differentiate the different MLST ST with high accuracy. Even if the p-values suggest a statistical significance, a quick look to figures 3 to 5 clearly show that there is a huge overlap of the spectra (as I would have expected). The only value of MALDI-typing would be to quickly rule out transmission, which cannot be done considering the significant overlap of spectra.
Additional comments: The authors test the performance of MALDI to type major MRSA lineages from Taiwan and compared results from MALDI with ST. Although the study objectives are fine, the authors fail to highlight the clinical impact of this method. In particularly, I do not agree with the conclusions.


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: APPLICATION OF A MALDI-TOF ANALYSIS PLATFORM (CLINPROTOOLS) FOR RAPID AND PRELIMINARY REPORT OF MRSA SEQUENCE TYPES IN TAIWAN
Review round: 1
Reviewer: 2

Output:
Basic reporting: Some improvements are needed.

1.  The Figure labels for the scatter plots do not seem to match the text in the results section.  In the text Figures 2A, 2B, and 2C are mentioned, but the figures are labeled Figure 1, 2, 3, 4, and 5.
2. Can a P value be reported for scatter plots shown in Figures 2 – 5?
3. There are some minor grammatical errors throughout the manuscript- eg line 81 should say “for confirmation” instead of “for confirm”.
Experimental design: Some suggestions are listed below.

1. It appears that the 10 peaks included in Table 1 are present in all strains, and peak intensity, rather than presence/absence was used to differentiate the different major STs.  Were there any peaks that were present in only some STs? Peak presence/absence may be a more robust way to differentiate between STs than peak intensity.

2. In Table 2, the authors present the performance of three binary classification models for ST5, ST59, and ST239.  Would it be possible to develop a single model that could classify an isolate into one of four categories (ST5, ST59, ST239, or other)? This would be more useful than multiple binary models.

3. It would be helpful to provide a little more context for the statistical tests included- what exactly are you using them to measure? For example, Wilcoxon/Kruskall-Wallis is assessing peak intensity among ST5, ST59, ST239, or other ST. Why was PTTA (Table 1) conducted? You can also state that Anderson Darling test was used to assess data distribution.
Validity of the findings: One minor suggestion to add to the discussion- What would be the ability of this approach to detect the emergence of a new MRSA clone in Taiwan?
Additional comments: No other 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: APPLICATION OF A MALDI-TOF ANALYSIS PLATFORM (CLINPROTOOLS) FOR RAPID AND PRELIMINARY REPORT OF MRSA SEQUENCE TYPES IN TAIWAN
Review round: 2
Reviewer: 1

Output:
Basic reporting: I am happy to re-evaluate the changes and corrections made by the authors. Almost all concerns were addressed. In particular, the authors were able to convincingly highlight the significance of MALDI typing compared to WGS in settings with constrain resources. However, although I am not a native English speaker, I still have the impression that some statements could be improved.

Line 74: “Finally, the data obtained from MALDI-TOF mass spectra are relatively complicated and may be analyzed using various methods”. It is still unclear what it means. Does it mean: “Finally, the data obtained from MALDI-TOF mass spectra are complex and need to be analyzed by bioinformatics tools”?
Experimental design: The inclusion criteria are still not clearly stated. If this is a convenience sampling, it should be stated. At least some basic criteria should be mentioned.  Inclusion criteria: community or hospital acquired or both? Colonization or infection or both?  Exclusion criteria: duplicate isolates or anything else that applies. The authors might mention the criteria as published by Wang et al. 2012 (if applicable).

Line 94-96: 16sRNA gene sequencing is inappropriate to differentiate S. aureus and S. argenteus and the sequences are identical (doi:  10.1099/ijs.0.062752-0). I suggest NRPS or nuc gene PCR (Zhang et al. etc.).

Table 2 seem to contain 3 sub-tables. They can be combined to make it easier to readby just adding one collum and changing the title as follows: test performance of various lineage typing ML models:

ST	Model	Selected peaks	Acc	Sen	Spe
ST5	QC	8
	SNN	24
	GA_KNN1
	GA_KNN3
	GA_KNN5
	GA_KNN7
ST95	QC
	SNN
	GA_KNN1
	GA_KNN3
	GA_KNN5
	GA_KNN7
STXY
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: APPLICATION OF A MALDI-TOF ANALYSIS PLATFORM (CLINPROTOOLS) FOR RAPID AND PRELIMINARY REPORT OF MRSA SEQUENCE TYPES IN TAIWAN
Review round: 2
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The majority of the comments and questions raised by reviewers have been responded to in a satisfactory manner. Two minor comments/suggestions are provided below:
1.  As suggested by reviewer #1, it may be helpful to include some mention of spa typing in the introduction or discussion, as this is often used for characterization of S. aureus.
2. The section on the AD test (Lines 155 - 165) could be shortened. It is enough to say that it is used by ClinProTools to assess for normal distribution of peaks.


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: HEMIPARASITIC PLANTS INCREASE ALPINE PLANT RICHNESS AND EVENNESS BUT REDUCE ARBUSCULAR MYCORRHIZAL FUNGAL COLONIZATION IN DOMINANT PLANT SPECIES
Review round: 1
Reviewer: 1

Output:
Basic reporting: •	good English (only the first sentence in the conlusions need rephrasing to be easier to follow)
•	intro and literature good, but could be improved
•	normal structure
•	figures relevant, but Fig. 2 with different elevation for the highest site and missing description of boxplot charasteristics (median, first and third quartile) and whiskers (2% and 98% percentile ???)
•	raw data provided
Experimental design: •	primary research reported
•	questions well defined
•	knowledge gap is not properly identified
•	rigorous investigation performed
Validity of the findings: •	impact of findings not well assessed, rather descriptive and vague
•	data is robust but interpretation is not well balanced, need to take into account the limitations of experimental design
•	last paragraph commenting effects of global changes is not relevant to the study
•	conclusions are well supported
Additional comments: This study addresses an important issue whether hemiparasitic plants (from genus Castilleja) consistently increase diversity of plant communities across an elevational gradient and if their impact can be connected to disrupted root mycorrhizal colonisations of the plant community dominants. Especially the second part could represent substantial contribution to the respective field.
Research questions are properly defined, data collected in the field survey correctly analysed and presented using suitable diagrams and tables. However, the interpretation of the results lacks the view of plant ecologist and discussion of the findings is sometimes rather vague (see specific points below).
Biology of hemiparasitic Castilleja plants was not well introduced and also acknowledged when planning field sampling design for this study. Comparison of adjacent plots with and without hemiparasites (from visual estimates of Castilleja presence in the year of survey) does not enable to make strong inference about effect of this functional group on plant community functioning. This would need experimental manipulation (either introduction or removal of Castilleja) and more years of plot monitoring.

Major study caveats:

1) Samples of roots selected for evaluation of mycorrhizal status (lines 123 – 140) were not checked for the connection of haustoria from Castilleja plants. Thus, this study does not bring a direct test whether hemiparasites decrease colonisation of host roots by mycorrhiza.

2) According to methodology (lines 118 – 119) the dominant plant species for evaluation of the mycorrhizal status should be the species with ‘the highest relative abundance across 20 plots recorded at each site’. However, having the raw plant community data in hand this rule was respected by the authors only at one site – i.e. with the lowest elevation (2480m, Balsamorhiza sagittata) but not in other 4 sites. Correctly should be used following species: 2740m (Phlox hoodii with 37% relative abundance instead of Chrysothamnus viscidiflorus with 22%); 3200m (Helianthella quinquenervis with 11% instead of Viola adunca with 9%); 3392 m (Potentilla gracilis with 16% instead of Ligusticum porter with 15%) and 3460m (Poa alpina with 17% instead of Arctostaphylos uva-ursi with 7%).

3) Missing raw mycorrhizal data in the Excel sheet (showing only 98, missing 2 from 3200m site).

Minor points to be solved:

Lines 44 – 47: Hemiparasitic plants can reduce the abundance of dominant plant species, but this feature is rather limited to ‘root hemiparasites’ (not stem).

Lines 52 – 54: It needs to be emphasized that hemiparasites from definition (hemi) are dependent on host in the case of water and dissolved mineral nutrients (N, P, K, Ca, Mg  etc.) but carbon received from parasitism is of minor importance for them. Hemiparasites are green plants and do photosynthesis and carbon assimilation on their own (in contrast to holoparasites).

Lines 54 – 55: Indeed ‘hemiparasites may compete with host plant plants for soil resources through absorptive roots’ but this is not ‘additionally’ to above mentioned ‘haustoria’ (line 53). This is connected to the same root structure.

Lines 62 – 63: ‘Hemiparasite colonization reduces carbon allocation to fungal symbionts’ may be rewritten to the following: Attack by hemiparasites reduces host’s carbon allocation to fungal symbionts.

Lines 80 – 84: Please provide some details on biology of Castilleja species under investigation: whether they are biennial / perennial, clonal; which hosts do they prefer.

Line 83: Castilleja rhexiifolia was present according to Table 1 only at two sites (3200 and 3392 m).

Lines 116 – 117: ‘Percent coverage was estimated to the nearest 1% for species >20% and the nearest 5% for 117 species <20% coverage.’ Please first use <20% and then >20%.

Line 174: ‘The presence of Castilleja increased plant richness by 11% (F1,90=33.64, p > 0.0001), increased Shannon’s diversity by 9% (F1,90 = 13.82, p > 0.0003)’. Please replace it with p < 0.0001 and p < 0.0003, respectively.

Line 264: Please correct occurrence of C. rhexiifolia according to Table 1 (i.e. 3200 and 3392 m).

Lines 267 – 275: Out of focus of the study, remove it.

Lines 278 – 281: Please rephrase it with a couple of simple sentences.

Line 306: Correct to Ecology Letters (with a capital letter for the second name).

Lines 309, 318, 336, 354: Please put ‘and’ in front of the last author names.

Line 328, 394, 397 : Please give journal titles in italics.

Line 412: Please correct the legend of Fig. 1 according to diagram. There is no Simpson’s index.

Line 432: Please correct TAROFF = Tarax(i)acum officinale.

Line 444: Calculation of ‘Simpson’s diversity’ was neither shown in the Methods nor reported in the Results.

Figure 1 and 3: Please indicate the values which are shown by boxplot (median, first and third quartile) and especially whiskers (???).

Figure 2: in the legend please correct BALSAG = Balsamorhiza sagittata (e); TAROFF = Tarax(i)acum officinale; in the diagram use uniformly the same elevation for the highest site as anywhere else in the text (i.e. 3460 m).

Figure 3: Please say in the legend what the different colours (blue and orange) show (Castilleja presence and absence).

Table 2: Please change the ‘>’ signs to ‘<’ for all P values (last column).


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: HEMIPARASITIC PLANTS INCREASE ALPINE PLANT RICHNESS AND EVENNESS BUT REDUCE ARBUSCULAR MYCORRHIZAL FUNGAL COLONIZATION IN DOMINANT PLANT SPECIES
Review round: 1
Reviewer: 2

Output:
Basic reporting: There are quite a few minor errors in spelling, grammar, and punctuation throughout.  The literature cited does not always back up or refer to the points made in the article, and this was particularly common in the introduction. The sections on fungi and climate definitely need to be improved as they do not make the best use of the literature.  The article is structured well but the figure and table legends need to be clearer so that the reader can interpret them without referring to the main text.

I applaud the authors for making their raw data available along with their R-code.  This really useful.

I have made specific line by line comments in the general comments section below, which will hopefully assist the authors.
Experimental design: The design appears to be mostly sound, although a figure of the actual layout would be really helpful (randomised but adjacent sampling could be more clearly expressed in a  figure).  The root sampling is not convincing from the point of view of only collecting the target species.  I think the authors need to acknowledge that they cannot be certain that the roots examined come from the target plant alone.

Research questions were well defined, relvant, and meaningful.

Technical and ethical standards are high, but choice of statistical analyses is incorrect in places.

Replication of the methods will be possible once the randomised adjactent sampling is better explained.
Validity of the findings: The main issue with the article is the use of simple linear models to assess data that includes binary variables and species counts.  GLM or mixed model approaches are needed, and it would be useful to note whether the distribution and variance of the data was examined.  The use of ordination techniques could also be improved and further explored by exploring the correct number of dimensions for NMDS and applying MRPP or PerMANOVA approaches.  Once the authors have revised their analyses to use the correct techniques then it will be easier to assess the validity of the findings.
Additional comments: In general I think there is a really good paper in here that just needs some more thought and careful re-examination of the data with the correct statistical techniques.  The study system is really interesting and the results of the study will be of interest to readers in a few different fields of ecology.

Specific comments
Introduction, ln 48: abundance, not abundant
Ln 53: haustoria, not haustroria
Ln 56: remove comma
Lns 54-58: This sentence is a bit unclear and needs to be more specific. Is the suggestion here that the hemiparasites may form mycorrhizas with AMF that compete with the AMF of the host plant for resources? Or do you mean that the hemiparasites associate with the same AMF as the host plant (e.g. via a common mycorrhizal network) and reduce the quantity of nutrients being transferred to the primary host? How would DSEs help a hemiparasite to compete for soil resources? It would be appropriate to provide a reference for this, although I’m not aware of any evidence for DSEs providing competitive benefits to hemiparasites (Li and Guan record colonisation in their 2007 paper but I don’t they studied impacts on competition).
Lns 59-60: The Joshi et al 2000 paper does not measure belowground biomass or even discuss fungi. Here you are speculating that AMF and DSE may have an additional effect beyond what has been investigated in the literature, but this sentence reads as though it has been previously explored and is an accepted idea.
Lns 60-62: That is a strong statement to make about DSEs. The Mandyam & Jumpponen paper you cite makes the point that responses to DSEs are hugely variable.  I don’t recall there being any evidence of nutrient uptake by DSEs, so you might want to clarify whether you mean growth benefits or something else.
Ln 62-63: Should be (Stewart and Press, 1990).  This reference does not make that claim. Your statement is one possible hypothesis that can be drawn from the paper, but they certainly don’t test it or even mention it.  It could also be that hemiparasite colonisation has no effect on the carbon allocated to fungal symbionts, or perhaps the plant allocates more carbon to the symbionts in an effort to increase its access to nutrients.
Ln 63-66: This is better.  It would be useful to note that this has been shown in controlled pot experiments.
Ln 67: The Stewart and Press reference does not mention this concept.
Ln 69-70: Choice of references is a bit odd again, but maybe it is just the sentence structure.  If you start out by noting that climate contexts shape fungal and plant community structure and function (there are lots of more recent papers on the impacts of climate on plant and fungal communities), you can then say that hemiparasites are likely to interact with these effects.
Ln 70-71: So do beneficial mutualistic interactions. I think you could strengthen this section (lns 69-79) through better choice of references and more careful wording. Section starting Lns 73-79 is good, but 69-73 is weak (including a sentence that cites the same two papers twice).

Ln 91: Point 2) does not flow properly in the context of a list beginning with “We hypothesised that:” You could change it to 2) the presence of Castilleja would alter community composition.
Methods, ln 104: You have a superscript 1 after cm.
Ln 113-114: Can you put in a figure to illustrate this? I’m curious about how this was done in practice as 20 plots per elevation is easy to understand, but randomly selected adjacent plots with and without Castilleja is not so clear.  There is the potential for spatial autocorrelation in your sampling so it would be useful to give the reader more information.
Lns 123-140: So this is just a bulk root sample, you didn’t try to identify whether the roots came from one or multiple host plants / host plant species?
Ln 144: plant species richness
Ln 145-149: This is problematic. You do not indicate having examined the distribution or variance of the data, and one of your variables is binary (present/absence). Really you should be using a glm (Generalised linear model) or LME (linear mixed effect model) function not a simple linear model.  This will allow you to account for a binomial error structure by including a logit link function or a poisson error structure using a log link function (plant species richness is count data).  You should also include some species accumulation curves (could be supplemental) for your plant community data to show whether you reached saturation or not.
Ln 158-164: Using NMDS you could include all of the elevations together to see if they differ from each other.  You would also want to use an MRPP or PerMANOVA analysis to examine whether + and – Castilleja groups are considered significantly different or not.  The problem with using R to do NMDS is that you are telling it to look at two axes without knowing how many axes best explain the data.  I’m not sure if there is a workaround because I do not use R for doing ordinations.  It may be that a 3D fit is best, which could change things substantially.
Ln 165-170: Same problem as lns 145-149 above, you cannot use a linear model to examine a binary predictor in this way. You also need to adjust the language to note that the roots are not necessarily just from the dominant host.
Results will all need to be re-assessed following analysis with correct models. Subheadings should reflect the hypotheses being tested, rather than the interpretation of the results.
Discussion will also need to be reassessed following corrected analyses.
ln 216: low abundance, not low abundant. Should be a full stop after diversity, a comma after however, and insert “the presence of these plants” or something similar.
Ln 234-236: From the way the methods are written you cannot be sure that those roots all came from the dominant host, so be careful with the statements about what you can show here.
References ln 398: the link is broken
Figure 1. Define what you mean by plant community.  Legend details are a bit sparse. The reader should have all of the information they need in the figure legend.
Figure 2. How many ordination axes did you examine?  If you have three significant axes then those communities could be separated in ordination space.


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: HEMIPARASITIC PLANTS INCREASE ALPINE PLANT RICHNESS AND EVENNESS BUT REDUCE ARBUSCULAR MYCORRHIZAL FUNGAL COLONIZATION IN DOMINANT PLANT SPECIES
Review round: 1
Reviewer: 3

Output:
Basic reporting: Meets the standards of PeerJ
Experimental design: Generally appropriate experimental design and data analysis, but see my suggestions for improvement below.
Validity of the findings: The data and analyses are robust, but the interpretation is not fully supported by the results, especially since the causality is unclear in observational study. See detailed comments below.
Additional comments: Review on manuscript 28743
Hemiparasitic plants increase alpine plant diversity but reduce arbuscular mycorrhizal fungal colonization in dominant plant species
Submitted to PeerJ

Recommendation: Major revision

The study reported in this manuscript aimed to explore the effect of a hemiparasitic plant genus on plant species diversity, composition and root fungal colonization in an altitudinal gradient. The research questions are well supported by the introduction, the sampling was well designed and data processed by appropriate methods. The authors are native speakers, unlike me, and the manuscript was easily intelligible to me. The study is generally good to be published in PeerJ, but it needs a revision of certain points. Especially, I am very doubtful about the interpretation of the observed patterns as causal relationships, and I find the selection of diversity measures misleading. In addition, I have many minor comments, which need the authors’ attention.

Comments to the authors:
Throughout the whole manuscript, you state that “presence of Castilleja impacted / increased / reduced... something”. However, this is an observational study and you have no evidence that the observed statistical relationships are caused by the parasitic behaviour of Castilleja. For instance, a related hemiparasitic plant Rhinanthus minor is also known to reduce community biomass and sporadically increase plant richness, but at the same time it fails to establish in more productive and less diverse communities, and it is impossible to disentangle these two processes without a manipulative experiment. Your study provides valuable data, but the observed patterns must be interpreted appropriately, e.g. “presence of Castilleja was associated with higher species richness...”.
Hejcman, M., Schellberg, J., Pavlů, V., 2011. Competitive ability of Rhinanthus minor L. in relation to productivity in the Rengen Grassland Experiment. Plant Soil Environ. 57, 45–51.
van Hulst, R., Shipley, B., Thériault, A., 1987. Why is Rhinanthus minor (Scrophulariaceae) such a good invader? Can. J. Bot. 65, 2373–2379.
Westbury, D.B., Davies, A., Woodcock, B.A., Dunnett, N.P., 2006. Seeds of change: the value of using Rhinanthus minor in grassland restoration. J. Veg. Sci. 17, 435–446.

Lines 144 – 145, Table 2: I do not like using all of these measures: richness, evenness, Shannon’s diversity and Simpson’s diversity. Richness and evenness are independent of each other, but both diversity measures are just composed of richness and evenness in various proportion. Therefore the p-values for the diversity measures are in between the ones of richness and evenness, and Simpson is less significant than Shannon. Statements like “Castilleja increased plant species richness and diversity” (e.g. lines 31 – 32, 209 – 210) seem to present two effects, but it is actually just one. Moreover, you present Simpson only in the table, not in the text.

L. 21 – 22, 44 – 51: Some hemiparasitic plants do not always provide the desirable effect.
Westbury, D.B., Dunnett, N.P., 2007. The impact of Rhinanthus minor in newly established meadows on a productive site. Appl. Veg. Sci. 10, 121–129.
L. 84, 218: Is there any information available about the level of host specificity of Castilleja species?
L. 104 – 105: I guess that you used mm/yr (not cm/yr). What are actually these values? Why do they not correspond to “MAP (mm)” in Table 1? The same for temperature.
L. 113 – 114: Could you honestly describe, how did you select the experimental plots? Real random selection would hardly result in such a nice pair design. How did you select plots with the parasite and how did you select the adjacent control plots?
L. 119 – 121: Statement “Next, we collected a single root core...” fits better to the next section.
L. 124 – 126: The calculation of number of samples in brackets repeats previous paragraph, and moreover is not completely true. I wondered why there are only 88 residual df in Table 1 for AMF and DSE colonization when you state in methods you have 100 soil cores. I found only in supplementary material that there were 9 – 11 data points in each site*treatment. You should state in methods something like “about 10 plots” and “98 total soil cores” and mention the cause of missing data.
L. 145: Typo in the formula, should be “H= - Σpiln(pi)” (lowercase subscript i, not “H= - ΣpIln(pi)”)
L. 147 – 148: Statement “... by constructing linear models with elevation (m),...” clearly implies that numeric variable Elevation was used in general linear model, which is not true. Categorical variable Site was in fact used in analysis of variance (or general linear model, as you wish) and the statement should be rephrased appropriately.
L. 151 – 155: These lines can be omitted. The first sentence describes well-known principles of ANOVA which is redundant here, the last sentence fits more to discussion.
L. 158 – 162: nMDS does not perform a statistical “test”, you should better use a synonym which is not a statistical term (e.g. “compare”?). Moreover, I think that statements “Castilleja influenced plant community composition” and “certain plant species were impacted more or less by Castilleja” mean the same and the latter sentence can be omitted.
L. 173: The headings within Results and Discussion sections sound very weird to me. You should not say the result in the heading, especially in the Results section (I could accept it in Discussion).
L. 180 – 183, 191 – 193: Do not interpret the results in the Results section, you can omit these lines.
L. 189 – 190. You cannot interpret p = 0.045 if you have 5 related tests (think about multiple testing and false discovery). Also the 3 out of 5 trends in the same direction mean nothing, it cannot be closer to the null hypothesis 2.5 out of 5.
L. 201 – 204: Remove brackets from DF.
L. 211 – 221: Do not refer to “our first/second... hypothesis”, the reader does not remember what they were. Consider rephrasing (maybe “contrary to our expectations” instead of “leading us to reject our second/fourth hypothesis”?)
L. 261 – 262: Statement “Additionally, the effects... did not vary by species...” sounds to me as if you were introducing an additional result, but it is just an alternative interpretation of the previous result with unknown cause. Consider rephrasing. For instance, for several reasons mentioned above, you can rephrase l. 218 – 221 “Surprisingly, we found that positive hemiparasite association with plant richness was independent of site differences (possibly related to climate, community composition or Castilleja species present).”
L. 280: “reduced”
L. 281: “are highlighting” or “highlighted”
L. 435: Really also AMF in 3460m?
L. 441: Abbreviation of fungi are missing (AMF, DSE and especially ERM, which is mentioned here first time)
Figure 2: Disproportionate labels. If the figure is printed in one column, the species labels are too small. If it is printed in two columns, the altitude and treatment labels are too large.
Table 1: A row with summary of Castilleja abundance would be interesting. In addition, the row “Castilleja sp. present” does not fit to the raw plant community data. I see in the raw data: 2480 and 2740 CASANG (what is this species?), 3200 CASSUL, 3392 CASSUL and CASMIN, 3460 CASSUL.
All “>” and “<” signs are in the wrong direction. I guess that e.g. P<0.0001 or that you estimated coverage to the nearest 5% for species >20% coverage.
The figure and table captions on lines 410 – 447 differ from the captions on the following pages. Some captions do not fit the content of the figures and some captions are obviously incomplete.

Petr Blažek

České Budějovice, 30 June 2018


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: HEMIPARASITIC PLANTS INCREASE ALPINE PLANT RICHNESS AND EVENNESS BUT REDUCE ARBUSCULAR MYCORRHIZAL FUNGAL COLONIZATION IN DOMINANT PLANT SPECIES
Review round: 2
Reviewer: 1

Output:
Basic reporting: OK
Experimental design: OK
Validity of the findings: OK
Additional comments: I am satisfied with responses, all corrections and changes were made by the authors with respect and the manuscript now reads well. Only correct species name to 'Rhinanthus' on line no. 335 and ensure that species abbreviations in Fig.2 do not overlap.