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: CELL PROLIFERATION CONTROLS BODY SIZE GROWTH, TENTACLE MORPHOGENESIS, AND REGENERATION IN HYDROZOAN JELLYFISH CLADONEMA PACIFICUM
Review round: 1
Reviewer: 1

Output:
Basic reporting: In this manuscript, Fujita et al. analyze the pattern of cell proliferation in the hydrozoan medusa Cladonema pacificum. Using hydroxyurea, they show that cell proliferation is required for medusa growth, tentacle morphogenesis and tentacle regeneration. They also analyze the distribution of proliferating cells in two other hydrozoan medusae. These data add to our understanding of cell proliferation in hydrozoans. The text is clearly written and the figures are relevant and well described.

Correct spelling mistakes: Line 23 ‘cellar’; Line 251 ‘Cnidrians’.
Experimental design: The design of the reported experiments is in general satisfying. However, some details should be added in the Material and Methods and Results parts:

1) In the M&M section, it is written that two types of EdU incubation have been performed, 20uM for 24hr and 150uM for 1hr. It is unclear why the Authors used two different EdU concentrations for the two different incubation times. Also, it is unclear in the Results section which type of EdU labeling has been performed for each experiment. Please add details in the M&M and the Results sections.

2) It is unclear how the medusae were fed. Since the Authors show that feeding has a major impact on medusa growth, it would be important to know the frequency and quantity of feeding in the different experiments. This should be added to the M&M section. Please also explain the meaning of ‘normal feeding condition’ (lines 193, 219).
Validity of the findings: 1) In the first section of the Results part, the Authors describe the pattern of cell proliferation in Cladonema pacificum. This description is very succinct and should be much expended. This section should at least answer in details the following questions:
-	In which cell layer are the proliferating cells located in the tentacle, manubrium and medusa bell? ectoderm/endoderm? exumbrella/subumbrella?
-	Are the proliferating cells uniformly distributed in the tentacles? It seems in Fig 2D that the smallest tentacles contain many more EdU positive cells than the longer ones.
-	How are distributed the proliferating cells in the tentacle bulb? Looking at Fig 1B’, it seems that they are mainly located in two “clusters” on either side of the tentacle bulb.
-	Are proliferating cells present in the manubrium? And if so where? It is not possible to assess this on the images provided.

2) The Authors use DAPI staining to detect poly-γ-glutamate in Cladonema nematocytes. Line 233-235, the Authors state: “Using poly-γ-glutamate staining, we discovered nematocyte size variations ranging from 2μm2-110μm2 (Fig. 3D). Because nematocytes increase in size during maturation, small nematocysts tend to be immature nematocysts” Implying that the small DAPI labeled nematocytes are the immature forms of the larger ones. This is unlikely since poly-γ-glutamate in both Clytia and Hydra start accumulating only after the nematocyte capsules are fully formed. The authors here are more likely observing different nematocyte types and not different stages of maturation. This could be checked by analyzing the nematocyte composition of the tentacles.

3) The Authors show that Cladonema medusae keep growing for a day after being starved. This has already been described in “Costello J. 1998. Physiological response of the hydromedusa Cladonema californicum Hyman (Anthomedusa: Cladonemidae) to starvation and renewed feeding. J. Exp. Mar. Biol. Eco. 225, 13-28.” Please cite and discuss this article.
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: CELL PROLIFERATION CONTROLS BODY SIZE GROWTH, TENTACLE MORPHOGENESIS, AND REGENERATION IN HYDROZOAN JELLYFISH CLADONEMA PACIFICUM
Review round: 1
Reviewer: 2

Output:
Basic reporting: See general comments.
Experimental design: See general comments.
Validity of the findings: See general comments.
Additional comments: This paper investigates the role of cell proliferation in growth and regeneration of jellyfish in the hydrozoan cnidarian Cladonema pacifica. The authors used cell proliferation markers EdU and an anti-PhosphoHistone H3 antibody to study the spatial distribution of proliferative cells. In addition, they used hydroxyurea (HU) to pharmacologically inhibit cell proliferation. They find that proliferative cells occur throughout the medusa body, and report a concentration of proliferative cells at the base of tentacles referred to as the tentacle bulb. Moreover, they show that pharmacological perturbation of cell proliferation leads to defects in growth, nematogenesis, and tentacle regeneration in C. pacifica medusae. The authors conclude that C. pacifica medusae possess non-randomly distributed proliferative cells that have necessary roles in development and regeneration.

The role of cell proliferation in jellyfish development and regeneration is understudied, and therefore descriptive and functional analyses of proliferative cells in hydrozoan jellyfish reported in this paper are important. I think this paper should be of interest to broad audiences including invertebrate zoologists, evolutionary developmental biologists and regenerative biologists, and thus would be suitable for publication in PeerJ. Overall, I think that the basic reporting requirements are satisfied for the most part; in particular, figures appear to be of high quality. My main concerns relate to 1) the lack of statistics to support authors’ claim that proliferative cells are uniformly distributed in the umbrella and are enriched in tentacle bulbs, 2) the lack of data to rule out the possibility that phenotypes observed in HU-treated animals have resulted from the toxicity of HU treatment, and 3) the lack of data showing the identity of proliferative cells, as discussed below.

1.	On the basis of the spatial distribution of EdU- and/or PH3-positive cells, the authors suggest that proliferative cells are uniformly distributed except in the tentacle bulbs where a cluster of proliferative cells, or “a proliferative zone”, is observed. However, no statistics (e.g. spatial autocorrelation) was performed to reject the null hypothesis that EdU- and/or PH3-positive cells are distributed randomly throughout the medusa body. Evidence is qualitative. The authors should perform appropriate statistical tests to determine whether the spatial distribution of proliferative cells in medusae is uniform, clustered, or random.

2.	Based on the phenotype observed in HU-treated animals, the authors conclude that cell proliferation is necessary for normal growth, nematogenesis, tentacle morphogenesis and regeneration in C. pacifica medusae. However, the possibility that the observed phenotype in HU-treated animals resulted from the toxicity of HU treatment has not been ruled out. Are HU-treated animals capable of feeding? Are the effects of HU treatment reversible? Addressing these questions is critical for authors’ main conclusion.

3.	As the authors indicate in the manuscript, postembryonic cell types in hydrozoans can be generated by differentiation of interstitial stem cells (i-cells), or by transdifferentiation of differentiated cells (e.g. striated muscle cells in Podocoryne). It would therefore be important to determine the identity of proliferative cells during growth and regeneration in C. pacifica medusae. Do all, or a subset, of the proliferative cells show morphological hallmarks of i-cells (i.e. high nucleo-cytoplasmic ratio, the presence of nucleolus, basophilic, etc)? Where exactly are the proliferative cells located? In the ectoderm and/or endoderm? In the tentacle bulb, are proliferative cells enriched on the oral side, the aboral side, or both?

Minor points:

-Line 240: It is not clear what is meant by “the rate of small nematocysts.” Do authors mean the number or proportion, instead of the rate? Please clarify.
Also, which statistical test was performed to assess the significance of difference between HU-treated animals and the control animals? This information is lacking in Line 264 as well.

-Line 268: Start a new paragraph from “In order to…”

-Line 284: Start a new paragraph from “To gain insight into…”

-Line 310: Start a new paragraph from “Another interesting feature…”

-Figure 2D: How old are the animals?

-Figure 3 caption: E and F are mislabeled. Information on scale bars is missing.


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

Input:
Title: CELL PROLIFERATION CONTROLS BODY SIZE GROWTH, TENTACLE MORPHOGENESIS, AND REGENERATION IN HYDROZOAN JELLYFISH CLADONEMA PACIFICUM
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The Authors did a good job answering the comments from both reviewers. In particular, Figure 1 and the related 'Results' section have been much improved  The manuscript can be accepted in its current form, in my opinion.


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 COMPLETE MITOCHONDRIAL GENOME OF PYXICEPHALUS ADSPERSUS: HIGH GENE REARRANGEMENT AND PHYLOGENETICS OF ONE OF THE WORLD’S LARGEST FROGS
Review round: 1
Reviewer: 1

Output:
Basic reporting: Literature references, sufficient field background/context provided.
It needs more detail in the introduction to explain the value of studying Pyxicephalus adspersus, especially its complete mitogenome.
Experimental design: The complete mt genome results showed that there are 15 PCGs for Pyxicephalus adspersus. Why 10 PCGs were chosen as an concatenated dataset to implement phylogenetic analyses, and what protein coding genes were chosen? Why not choose 13 PCGs or 15 PCGs? In addition, the authors named the concatenated dataset as 10P123 in line 167, while it was changed as 13P123 in line 168. The best substitution models obtained from PartitionFinder  in line 174 were not the same as the authors used in BI and ML analyses, please explain why.
Validity of the findings: 1. Some academic terminology abbreviations are not homologous. For example, the expression “the trnT gene” was used in line 80, while “tRNAs Ile, Cys, Lys, and Arg” was found in line 118.
2. There are some inappropriate sentences in the manuscript, e.g., in line 226 “…located between ND6 and Ile genes” should be “… ND6 and tRNAIle genes”. The same expressions were found in line 228, 229, 230, etc.
3. Only one species, Pyxicephalus adspersus, representing the family Pyxicephalinae cannot explain its monophyly.
Additional comments: The English language should be improved to ensure that your international audience can clearly understand your text. I suggest a pre-review of your manuscript from your native English speaking colleague before your submission. Some examples where the language could be improved, e.g. lines 51, 96, 170, 171 etc - the current phrasing makes comprehension difficult. In the whole manuscript, it is very interesting about the rearrangement of mitochondrial genome, while the authors did not address this in phylogenetic analyses, and the monophyly of family Pyxicephalinae was not well supported in this study. I suggest the major revision before resubmission.


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 COMPLETE MITOCHONDRIAL GENOME OF PYXICEPHALUS ADSPERSUS: HIGH GENE REARRANGEMENT AND PHYLOGENETICS OF ONE OF THE WORLD’S LARGEST FROGS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Some sentence are unclear, and some abbreviation are not  normalized.
1.	Line 47  It's an incomplete sentence. “and” what?
2.	Line 63  It’s better to add a topic sentence in this paragraph, as the author described many kinds of gene rearrangement in anurans.
3.	Line 164  The genes name should be normalized and unified in one paper.
4.	Line 168  what is “13P123”? Is there any difference between “10P123”?
For 10 mt PCGs, it’s no need to describe the name “10P123”.
5.	Line 187  This sentence is ambiguous.
6.	Line 193  What is “NCR12”? The definition should be shown for the first time of the paper.
Experimental design: no comment
Validity of the findings: The manuscript by Cai et al. is an important contribution regarding mitochondrial genome of Pyxicephalus adspersus and the anurans mt evolution. The results of NCR need check.
Line 208-209 There should be another NCR between Arg and ND5.
Additional comments: The author sequenced the whole mt genome of this species, and found specific gene rearrangement. Now, the genome of P. adspersus has been sequenced, but the mt genome of this species is lacking. The results of this study could be used to identify the mt sequences and helpful understanding the phylogeny and mt evolution of anurans.


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 COMPLETE MITOCHONDRIAL GENOME OF PYXICEPHALUS ADSPERSUS: HIGH GENE REARRANGEMENT AND PHYLOGENETICS OF ONE OF THE WORLD’S LARGEST FROGS
Review round: 2
Reviewer: 1

Output:
Basic reporting: 1. The sentence in Line 91 should be deleted

2. Line 103, “Pyxicephalinae as one subfamily of Ranidea” or Ranoidea?

3. Line 97, it’s better to add a topic sentence in this paragraph, as the author described the taxonomic status of Pyxicephalidea.

4. Line 120, the sentence is not precise or persuasive. “a species with a giant size with an animal group may be associated with a larger mt genome” may be reasonable in frogs but not in all other species. Although the following example was given to support this sentence, please give more references.
Experimental design: 1. Line 196, can be modified as:
Although extra COX3 and Cyt b genes were found in Pyxicephalus adspersus (see the result in the following context), the extra copies of COX3 and Cyt b genes were identical to the other COX3 and Cyt b genes (100% similarity). Therefore, in phylogenetic analyses, only one set genes of COX3 and Cytb was used. In addition, due to some mitochondrial protein-coding genes missing in some species (ND5), lacking good information (ATP8) and the heterogeneous base composition and poor phylogenetic performance (ND6) (Zhang et al., 2018a), ten PCGs genes were used in this study and separately aligned in Mega 7.0 (Stecher et al., 2016).

2. The best substitution models for BI and ML can be both obtained from PartitionFinder. The models of each partition can be set separately. It is not reasonable to replace GTRGAMMAI model in RaxML and GTR+I+G in BI. Please explain why and do the new analyses.
Validity of the findings: 1. Line 246, Ile should be tRNAIle gene?

2. The discussion about the monophyly of Pyxicephalidae should be in the discussion or conclusion part. In addition, the monophyly of Pyxicephalidae should be confirmed by more adequate sampling in future studies.
Additional comments: The authors have amended the manuscript very quickly and carefully and given positive feedback in most of the reviewing points. But there are still some sentences should be modified. In addition, it is better to do a new phylogenetic analyze to confirm 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: GRADUAL, TEMPERATURE-INDUCED CHANGE OF SECONDARY SEXUAL CHARACTERISTICS IN TRICHOGRAMMA PRETIOSUM INFECTED WITH PARTHENOGENESIS-INDUCING WOLBACHIA
Review round: 1
Reviewer: 1

Output:
Basic reporting: The current paper compared the temperature effect on the production of intersex individuals of Trichogramma pretiosum when they are infected with Wolbachia. In this study the authors install reproductive females in different environment (temperature) and measured external parameters to evaluate intersex characteristics.
The results are very concise and clear, and the paper is really focused.
Here are some general comments.
The introduction explains that in the presence of Wolbachia individuals impact the production of females.
L59 and 60: what are the two types of intersex?
L74: the reference Almeida and Stouthamer, 2018 is not appropriated to described Wolbachia impact on insects. Several review or book chapter are more appropriate.

What is the link between the parthenogenesis induced y Wolbachia and the observed intersex? The connection in the introduction is difficult.
L79: the word feminization here is not appropriated. Diploid individuals are necessary females, right?
L81-82: the feminization here refers to individuals that are genetically males with the physiology of female, such process is very different that the one observed in the current study model.
Could the authors clarify the definition of intersex in their species? Morphology? Physiology impact? Can they reproduce? Life history traits?
In the introduction, the authors didn’t introduce the concept of masculinization, but this part is really developed in the result section and in the discussion.
Experimental design: Materials and methods.
L113: 20 generations: how long is one generation? Why did the authors wait for so long? Was the raising condition managed in a specific way? Was the reproduction controlled?
When the individuals were killed, how old were they? How were they scarified?
Could the authors explain why the preparation L134-137 was necessary as they observed external aspect of the individuals?
L139: remove “for”.
Validity of the findings: Results:
Table 1: the authors could also add the “letter” for each line (A to K) it will be easier to compare the different categories.
I suggest to add pictures of antennae and genitalia of regular female and regular male as a comparison. What is the main difference between male and female antennae?
Moreover, the pictures in the table are too small, it’s almost impossible to see the sample.
L154: here for the first time the use of the word: masculinization is surprising as since the beginning we read about feminization. Same comment l165.
The authors should also include the results with asymbiotic individuals and it’s a control. Including in the figure and or legends. It’s mentioned only L181 of the discussion.
L204: what is CSD?
Why the authors switch in the discussion to masculinization, I don’t understand, the underline process.
Figure 1. The figure showed probability. Is it a prediction or based on your real data?
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: GRADUAL, TEMPERATURE-INDUCED CHANGE OF SECONDARY SEXUAL CHARACTERISTICS IN TRICHOGRAMMA PRETIOSUM INFECTED WITH PARTHENOGENESIS-INDUCING WOLBACHIA
Review round: 1
Reviewer: 2

Output:
Basic reporting: I would suggest corrections on the English language. For example, I don't like the word "proven" that is often used throughout the text, because it is often a too strong statement (replace by "this study showed", or "this study suggests"...).
Else, the article structure is fine to me.
In the discussion, I have one major concern. Authors claimed that "Wolbachia is
a direct factor that causes the occurrence of intersexes, while high temperature is an indirect factor that determines the external morphology of intersexes". However, it is hard to be so affirmative. Indeed, the effect of temperature is supposed to be through an effect on Wolbachia (partial destruction or inhibition of their effects). To be affirmative, one should expose the W+ lines to a temperature that have no effect on Wolbachia, e.g. 25°C. This would have allowed to present the "basal" proportion of intersexes (i.e. proportion of intersexes with Wolbachia in absence of any effect of high temperatures). Here this control series is lacking.
I would like, also, that authors note if intersexes are sterile or not. This is important, because if they are sterile, the impact of the interaction Wolbachia*Temperature, by increasing the proportion of intersexes, would induce a cost for the Trichogramma.
Experimental design: no comment
Validity of the findings: Figure 1 is showing that the proportion of intersexes reach a maximum of 1.5%. However, in the text (L. 162-163), the authors noted that the "The probability of intersex in F1 is 0.66±0.13 %... and in F2 0.24±0.019 %". There is therefore a huge difference between the text and the figure. Please correct this.
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: GRADUAL, TEMPERATURE-INDUCED CHANGE OF SECONDARY SEXUAL CHARACTERISTICS IN TRICHOGRAMMA PRETIOSUM INFECTED WITH PARTHENOGENESIS-INDUCING WOLBACHIA
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors addressed most of the comments and improved it but there is still some point that could be clarified.

What are the consequences of Wolbachia in the host species? Of course beside parthenogenesis? Do you have any information regarding other impacts?
Do you have information regarding Wolbachia prevalence in natural population?
Do the authors know if all intersex can reproduce?
In the answer you explain the complexity of the sex determinism of the species which is very important and could help the reader to better understand your study model and the impact of Wolbachia. This information could also contribute to better understand the discussion L 223-225.
L82: “known” should be corrected.

Discussion.
L198 -199: could we considered that without Wolbachia the sex ration is 50/50 for males and females in the study species? Or is it almost females?
L215 “… is relatively stronger,..”. Could the author precise stronger than what?
L217: the verb of the sentence is missing
L219: the authors should precise what they mean by dominance.
Experimental design: Materials and methods.
Did the authors check for Wolbachia infection in some individuals? Are they sure that 100% of the females were Wolbachia infected?

L115: “genenrations” should be generations and “collectiong” should also be changed.
L153: authors did some dissection but never said which dissection? Dissection to check what, which tissue? And do they have any picture?
L155 the sentence should be rephrased
Validity of the findings: Results:
The authors found 235 Intersex. Could the authors precise out of how many “normal” individuals?
The probability are very low and the value (%) are difficult to understand  if the authors do not provide more information.
These informations are provided in the supplementary materials, I suggest that the authors refer to the supplementary data in the text.
Moreover, in the supplementary file, the intersex are describe with number but in the manuscript it’s letters. Could the authors add the letter in the supplementary file as well.
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: GRADUAL, TEMPERATURE-INDUCED CHANGE OF SECONDARY SEXUAL CHARACTERISTICS IN TRICHOGRAMMA PRETIOSUM INFECTED WITH PARTHENOGENESIS-INDUCING WOLBACHIA
Review round: 2
Reviewer: 2

Output:
Basic reporting: The authors responded satisfactorily to my comments.
Experimental design: N.A.
Validity of the findings: The authors responded satisfactorily to my comments.
Additional comments: I noted few language oddities:
- L. 77-78: I do not really understand what you want to say. is it : "According to our knowledge of Trichogramma, intersexuals are only present in parthenogenetic species."
- L. 113: change "genenrations " for "generations", and "collectiong " for "collection"
- L. 117 should  "contains " be "containing" ?
- L. 143-144. There is something wrong with the sentence "In order to obtain the pictures of all masculinization levels of intersex and make the size of the sample remains unchanged for a long time." As far as I understood, it should be an introductory part of the following sentence (?). So the dot should be replaced by a comma.
L. 246-247 : the sentence "The genetic conflict between host genes and Wolbachia-induced parthenogenesis is the cause of intersex can induce intersex to occur" is weird. It should be something like : "The genetic conflict between host genes and Wolbachia may also be the cause of intersex development".


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: VISUAL SEARCH CHARACTERISTICS OF PRECISE MAP READING BY ORIENTEERS
Review round: 1
Reviewer: 1

Output:
Basic reporting: Major points
While the paper might offer some interesting insights into the perceptual-cognitive components of skilled performance in orienteering, and as such into skilled performance more generally, the presentation of the paper falls well short of the standards expected of a scientific paper. While some of these issues are superficial, many are not, which means that the paper in its current form is difficult to follow, and has methodological and conceptual issues. Much more attention must be given to the format, writing, and citation and referencing, which are poor. One example of these shortcomings is that several citations provided in support of an assertion appear to be entirely unrelated to the assertion (I provide a few specific instances below). More attention to detail is needed in the methods section; see my comment below about how there is a proposal in the measures section that a retrospective report was elicited from the participants but this method is not mentioned again and no associated data are presented. There also appear to be key conceptual issues; I detail one such problem below concerning the distinction made between general and precise map reading. My recommendation is to bring on board to the research team a more experienced researcher to critique all aspects of the current paper in detail and aid with a re-presentation of the paper and also a native English to enhance the writing, which will aid reader comprehension.

Minor points
Line 33: A critical missing piece of information here is that the orienteer must visit these points on foot
Line 35: I am quite sure strength is not important to orienteering and that measures of intelligence are at best weak predictors of orienteering performance.; see the literature on prediction of sport performance using domain-general abilities (e.g., intelligence) (generally poor) versus domain-specific perceptual-cognitive skills (generally good)
Lines 43 and 47: I cannot see how the Robertson et al. and Happe and Frith citations can possibly support the claims made prior to them. The Happe paper concerns autism, not orienteering. I found other instances of inappropriate support in this regard.
Lines 63-68: I’m not sure I understand the distinction made between general map reading, requiring athletes to plan a running route between points, and precise map reading, requiring athletes to combine information checklists and clarify the running route to find target points. Sometimes a distinction is made in the sport of orienteering between fine navigation, which involves very frequent comparisons between the map and surrounding environment to be sure that one knows where one is located in the world given the information on the map, and less fine navigation, where less frequent map-world comparisons are made. Fine navigation is usually required because the cost, in terms of time, of making a navigational error is higher than normal, and two instances where this is true are in complex terrain, which involves few distinguishable features, and when nearing a control (referred to as a target here) within a given leg; often, this is in the last 50-100 metres of a leg. I am not sure I see that the authors’ description of precise map reading is the same as my understanding of fine navigation. While the description of precise map reading mentions finding the target, what I see in the associated images is some less complex (Fig 1) and more complex (Fig 2) terrain. In other words, I see a conflating of approaching the control with complex terrain; yes, they both require fine navigation but for different reasons. And I don’t agree that less fine (general, in the authors’ terms) map reading does not require combining information checklists. If you orienteer in relatively easy terrain and don’t need to engage in much fine/precise map reading and navigation, you are still likely to consult the control checklist on the map when approaching a control to know where the control is located.
Line 54: Manzanares etc. This is not how to provide a citation.
Line 81: The citation is Arsal, 2015 but the reference, which is correct, is Eccles and Arsal.
Line 82: “Liu yang, 2018” Citations ask for the last name only; no first names
Line 87:  “Van” citation; I don’t think this can be correct
Line 158: The reader is told that the participants completed a retrospective report after the experiment. I assume this means a retrospective verbal report of thoughts recalled from during the task, but no details or supporting literature (e.g., Ericsson & Simon) are provided. Furthermore, the method is not mentioned again and no results are provided.
Line 164: “Total planning time”. The variable is total gaze time, surely. I think you might be inferring that total gaze time reflects total planning time. This is an important distinction.
Experimental design: See above
Validity of the findings: See above
Additional comments: See 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: VISUAL SEARCH CHARACTERISTICS OF PRECISE MAP READING BY ORIENTEERS
Review round: 1
Reviewer: 2

Output:
Basic reporting: This article reports information on an interesting study design. The authors are interested in interactions of expertise level (novice, intermediate, and expert) and map complexity (simple, complex) on accuracy and response times for reading and interpreting topographical maps, as well as for route planning using topographical maps. Eye tracking was used to record participants' eye movement data and the eye tracking data was analyzed to assess for the hypothesized interactions. The authors begin with an introduction to the sport of orienteering and do a good job of explaining the variables of interest within orienteering. A sufficient review of the literature is also present in the introduction. The authors state their hypothesis at the end of the introduction.

The language used by the authors is at times very difficult to follow. This appears to be the result of 1) poor sentence construction 2) nebulous use of terminology. For an example of poor sentence construction, please refer to the sentence in line 54 through line 57: "In addition, Manzanares etc (2017) empirical research, It further shows that athletes with different skill levels will have different visual behaviors, and the top ranked players can adopt a more active visual search strategy, and more experienced athletes can better obtain favorable information from important positions." Sentences such as these pose the reader undue challenges in deconstructing what the authors are attempting to communicate.

For an example of nebulous terminology, please refer to the hypothesis (lines 104 to 107). The hypothesis states that different levels of expertise will be "affected differently by the difficulty of the task during precise map reading and will have different visual search characteristics and processing strategies." It is unclear, however, exactly what is meant by "visual search characteristics and processing strategies." Furthermore, in their results section the authors use terminology specific to eye tracking which is not well defined. What is meant by "response times" (line 190), "gaze times" (line 204), and "average gaze frequency" (line 216)? This lack of specific explanations for what each of these variables mean with respect to the authors' hypothesis and results make it extremely difficult if not impossible to reconstruct the effects being explained in the results and discussion sections.

In looking at the raw data, the same problem exists. The raw data includes columns for "total gaze times", "gaze times", and "average gaze times" however it is unclear what any of these column headings mean with respect to their values. I was unsuccessful in reconstructing what any of the column headings refer to with respect to the data below the column headings or how the column headings related to each other.

The authors discuss an analysis of route-planning accuracy (lines 248-265), however no raw data is provided. The authors refer to the use of three orienteering expert trainers who scored "the correctness of each participant's gaze point track on a 5-point scale and then give a final score based on the average of the experts' scores, please include the raw data for this analysis.
Experimental design: As stated above, there are serious problems with syntax and lack of specific explanations which seriously impede the reader's ability to understand and interpret the hypothesis and results section.
Some of the methods described by the authors are presented in a much more understandable and clear fashion. For example, the experimental process (lines 139 to 158) was written in a very clear manner which allows sufficient detail to replicate this process.
Validity of the findings: As stated in section 1 ("Basic Reporting"), the results section (lines 170 - 244) is very difficult to follow. This difficulty primarily arises from a lack of clear and explicit descriptions of terms such as "response times", "gaze times", and "average gaze frequency." It is strongly recommended that the authors revisit the use of these terms in this article to provide clearer and more explicit descriptions. This will aid greatly in readers' ability to more clearly understand the hypothesis and stated findings of significance.
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: VISUAL SEARCH CHARACTERISTICS OF PRECISE MAP READING BY ORIENTEERS
Review round: 2
Reviewer: 1

Output:
Basic reporting: See below
Experimental design: See below
Validity of the findings: See below
Additional comments: The paper is much improved such that I can now understand it much more easily when I read it, and it is an interesting study that is quite well-designed and will contribute to our general understanding in the area of expertise research in psychology. Specifically, there is some nice use of cognitive process tracing and performance measures to uncover classic expertise by problem complexity interactions: that is, experts show their superiority over novices more clearly when the problems are complex enough to require that they draw on their more elaborate and refined problem representations. However, there are still some outstanding issues that need to be addressed, but these are now mainly superficial. That said, they must be addressed if the reader is going to be able to follow the work; readers won’t read all the work and thus won’t use and in turn cite the work to inform their own research if they can’t understand the work.
The authors refer to route planning “correctness” and “accuracy” but I think it is unlikely that there can ever be a single optimal route between two controls. My feeling is that the three expert judges can certainly judge the quality of a route, seeing whether one route is a better choice than another, and so I suggest using the word planning quality rather than planning correctness or planning accuracy. Check for every instance throughout the paper and make this change.
When follow up tests are run (e.g., line 190), make sure to state which level of the factor these are run on. On 190, the post-tests are presumably run on the complex level of the factor only because the main analysis had showed a main effect of skill level at the complex level but not the simple level; currently, this is not stated explicitly. Check all instances throughout the paper and correct this.
Make clear that all of the eye tracking data analysed are based only on data from the route planning stage of the study. This is important because the eye was tracked in the trail stage to identify the route planned, so the reader might be unsure (this reader was unsure initially) about whether the data from the trial stage were also analysed in these analyses.
Line 211: Some statistics are missing here.
Line 218: “…and the number of the total gaze is 90%”. Total gaze directed to the checkpoint? Is terminal point the same as checkpoint? If so, use one term only. This paragraph is unclear generally and needs to be very carefully revised if the reader is going to be able to understand what’s being presented.
Figures 7 and 8 is uninterpretable. Remove these.
Check all tables and figures. Units of measurement should be clearly provided for all. For accuracy scores, provide a note against tables and figures specifying the scale range and anchor points so the reader can interpret what the values mean; without these, the values are meaningless.
The efficiency in gaze behaviors observed by the experts in this study is consistent with the notion of experts’ circumvention of processing limitations generally (I suggest citing: Ericsson, K. A., & Lehmann, A. C. (1996) Expert and exceptional performance: Evidence of maximal adaptation to task constraints. Annual Review of Psychology, 47, 273-305) and expert orienteers’ circumvention of visual attentional limitations specifically (i.e., the experts derive key information from environmental displays using minimal visual attentional resources). As such, I suggest citing: Eccles, D. W. (2008). Experts' circumvention of processing limitations: An example from the sport of orienteering. Military Psychology, 20, S103-S121.
The citations and references are extremely poorly presented and MUST be revised so that there are no errors at all. Carefully follow APA format so each reference adheres fully to this format.


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

Input:
Title: VISUAL SEARCH CHARACTERISTICS OF PRECISE MAP READING BY ORIENTEERS
Review round: 2
Reviewer: 2

Output:
Basic reporting: * Line 21 forward: The authors use the terms "orienteer" and "athlete" interchangeably. These terms are not synonymous. Orienteering is a specialized type of athleticism and it is confusing to have the terms “orienteer” and “athlete” used interchangeably. It is especially confusing because levels of expertise for orienteer as a variable of interest whereas levels of expertise for general athleticism may have nothing to do with map reading.
	* Unclear use of terminology in the following instances: lines 80-81 “positive thinking characteristics”; line 87 “the accuracy of maps”; beginning with line 155 forward, please define specifically how authors are operationalizing the term “gaze”, this extends to line 196 “gaze time”
	* Lines 218-219 “and the number of the total gaze is 90%” is unclear
	* Lines 219-220 “and the number of the table and the terminal point is 75% of the total gaze” What does this mean, exactly?
	* Line 244 “The visual search of tasks generally needs to be done through top-down target attention and feature analysis” What is meant by “visual search of tasks”?
	* Line 261-262 “The gaze frequency refers to the number of gaze per unit time, which can be regarded as the processing speed of the map search…” This explanation is unclear. Does gaze frequency mean the amount of time a participant looks at a certain area of the map?
	* Line 301 Use of the term “checkpoint form” is unclear. Do the authors mean to refer to the use of the map legend, which contains explanations for symbols used in the map?
Experimental design: No comment
Validity of the findings: This is an interesting line of research with worthwhile results. I maintain that the authors would help to promote this study and future research by using a narrative that is more concrete and specific in the use of terminology and phrasing. Please see section of “Basic Reporting” for specific details.
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: REVISION OF THE TANZANIAN DICYNODONT DICYNODON HUENEI (THERAPSIDA: ANOMODONTIA) FROM THE PERMIAN USILI FORMATION
Review round: 1
Reviewer: 1

Output:
Basic reporting: Kammerer examines the phylogenetically problematic dicynodontoid species from the upper Permian of Tanzania, 'Dicynodon huenei'.

After an authoritative review, he walks us through the referral of Tanzanian specimens of 'Dicynodon huenei' to Daptocephalus huenei (new combination) and erects Dicynodon angielczyki (new species), based on consistent morphological differences that are well figured. Kammerer also clearly explains consistent differences between Tanzanian Daptocephalus and Dicynodon and their congeners in South Africa. The phylogenetic analysis supports the morphological interpretations, and the assignments fit into a developing picture of species level endemism among dicynodonts across upper Permian Pangea.

A few suggestions/edits:
-Specimen numbers for comparative taxa on lines 363-364 in the description (Peramodon, Vivaxosaurus, Dinanomodon) would be beneficial (with corresponding institutional abbreviations added). In-text comparison with Karoo Daptocephalus and Dicynodon do not need numbers necessarily as that information is included in figure legends.
-Figure 8: "pf, pineal foramen" is in the legend, but not labelled on the figure; "mpp" is labelled on the figure, but not listed among the anatomical abbreviations.
-Figure 11: The legend refers to "Figure Y" when it should say "Figure 12".
Experimental design: The OTUs were included in extremely modern phylogenetic analyses.
Validity of the findings: No comment
Additional comments: No additional comments


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

Input:
Title: REVISION OF THE TANZANIAN DICYNODONT DICYNODON HUENEI (THERAPSIDA: ANOMODONTIA) FROM THE PERMIAN USILI FORMATION
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper is written clearly and logically. There is a wealth of relevant references that will be extremely helpful for readers. The figures also look great and are organized in a way that facilitates comparisons between specimens. I have a few changes to suggest that may help with clarity:
Line 65: As tedious as it is, since each formation is a proper name you should include "Formation" captialized after each one. "Usili Formation and Madumabisa Mudstone Formation". Don't worry, we all hate it, too.
Line 128: Is there any reason to not call out a figure here for UMZC T1089 to show the thickened zygomatic arch in this specimen?
Line 129: The thickened zygomatic arch doesn't look obvious to me in Figure 3A. I'm guessing that's because the matrix is covering the arch a bit in this view, so maybe choose another view to illustrate this or at least mention that the thickened arch is partially obscured by matrix in this figure.
Line 130: Change to “…present in SAM-PK-10630, and Angielczyk…”
Line 138: Add a period after “(Kammerer, pers. obs.)”
Lines 151-161: I’m not sure the numbering here is very helpful. 1-4 would work just fine as individual sentences, and the rest could just be separated by semicolons. The numbering makes it a little messy, and it’s even a bit confusing when items that aren’t complete sentences have the first letter capitalized.
Lines 270-271: “All referred material is from the Ruhuhu Basin of southwestern Tanzania.” Maybe move this line to the start of the paragraph so readers don't encounter the name Kingori and wonder where/what that is.
Lines 376-377: Description of the frontal shape is kinda messy/unclear. Change to "The frontal is depressed in the interorbital region."
Lines 396-399: This description is confusing. I'm not sure what you mean by height here, and how that is deceptive.
Lines 416-418: I am unclear on where this fossa is exactly. In which direction is it bounded by the postorbital? Which face of the intertemporal bar is this? Are you referring to the fossa on the underside of the intertemporal bar?
Line 446: Change to "...but this is tentative". Otherwise the wording could be confusing to non-native English speakers
Line 485: Change to: "fused at the base"
Lines 503-587: This sections jumps out of nowhere, at least the way it's introduced. I would suggest either putting this paragraph at the beginning of the description (near where you state which specimens are being mostly used for the cranial description) or putting in subheadings for the cranium and the mandible so the reader knows you're going to do another specimen introduction here. Otherwise we're suddenly reading about gorgonopsians for half a paragraph before being told why.
Figure 6 caption: “Major facial bones colored to show arrange in various specimens…” Change “arrange” to “arrangement”
Figure 11A: Unless you were to label what all these other bones are in the block, it seems to me that the only function of Figure 11A is to give context for the otherwise odd-looking 11B. To make it more useful for this purpose, I would suggest outlining where in Figure 11A the stuff in Figure 11B comes from (so, the dicynodont skull and the gorgon bones that have been grayed out.
Figure 13: Are these all the resampling values you got? If so, fine, but if not, I'm unclear on why you're displaying only the values here. It seems to me like you'd at least want to display the value for D. lacerticeps+D. angielczyki. I'd prefer to see all of the values in this figure because so many bidentalian groups have been volatile in the various iterations of this analysis (especially Cryptodontia, which you even discuss in this paper), that it could be helpful for readers to be able to easily compare node support between analyses.
Experimental design: The author does a great job of providing the historical context for this revision. He provides a thorough description and sensible taxonomic changes.
My main concern is with the lack of information on the phylogenetic analysis. I understand that this is the next installation in a series of analyses with one database, but I’d still like to see the list of characters used here as a supplemental file. If the characters haven’t changed from a previous version, then maybe just cite the paper with the version you used so readers can get this information somewhere. You do cite a paper of yours that’s in press, but even if that is published before this one, there is a level of uncertainty with citing an in-press paper as the source for your characters. It may not be clear to the audience which paper this is referring to, so I think it's best to just upload the character data here, too. I don't see any harm in doing so. Similarly, I think you could include more information about how you conducted the analysis itself. Are there any other search parameters that you personalized? Which search algorithms did you use, etc.? Were any characters treated as ordered? If these things are also identical to a previous paper, please state which one. If it's from the in-press paper, I would again urge you to go ahead and list them here, too, to make it easier to replicate your work precisely. For example, I was unable to replicate the tree length you got in your results when I ran the data you provided. I even tried running it with parameters you mentioned in your emydopoid paper, and it still didn’t give me the tree length you got here (the topology was basically the same, though).
Validity of the findings: Overall, this is a welcome contribution to dicynodont taxonomy. I also think the discussion about the nuances of cosmopolitanism versus endemism across the P-Tr boundary is important. I only have a few comments:
Line 253: I don’t think the “tip of varying length” belongs here in the diagnosis. You can’t identify a species based on this. I would just include the part about it lacking the hooked shape of Dinanomodon.
Lines 276-278: Based on the figure, I don't see how the lacrimal is enlarged. It seems to have a more rounded shape, but it doesn't seem to be all that different in area from that of D. leoniceps. If what you're describing is more of a shape difference, please describe it as such to make the diagnosis more precise. If there really is a size difference, maybe include another specimen or a different view that shows this more clearly in Figure 6. Additionally, based on the data given, I don't have a good sense for how important of a difference this is. I think this could be helped by including more information about how consistent this difference is. How many specimens of each species show this difference? Is there maybe an additional specimen of D. huenei that you could add into Figure 6 to further illustrate that this is a consistent difference? This would make it more convincing that these should be considered two different species based on the lacrimal proportions.
Additional comments: Overall, I think this is a great paper with thorough background information and interesting implications. I think both the taxonomic revision and the points brought up in the discussion are timely.


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: REVISION OF THE TANZANIAN DICYNODONT DICYNODON HUENEI (THERAPSIDA: ANOMODONTIA) FROM THE PERMIAN USILI FORMATION
Review round: 1
Reviewer: 3

Output:
Basic reporting: Please check all for: GPIT/RE/9316 (=K6), GPIT/RE/9136(=K2), GPIT/RE/9641 (=K2),
9136 should be 9316?

L272: you should specific lacrimal taller (but shorter) (not larger) in D. huenei
Experimental design: Why not use TNT 1.5?

I tried your matrix, the shortest tree is 1153.408, there are 2 MPTs, but the consensus tree is same.
Validity of the findings: no comments
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: CHARACTERISATION OF BACTERIA ISOLATED FROM THE STINGLESS BEE, HETEROTRIGONA ITAMA, HONEY, BEE BREAD AND PROPOLIS
Review round: 1
Reviewer: 1

Output:
Basic reporting: •	The authors do a great job providing background knowledge about the bees, their hive components, the physical properties of the components, and the microbes associated with bees, but never really state a strong hypothesis for conducting the study, besides being interested in characterizing the strains of Bacillus. Do the authors have a hypothesis bout the bacteria providing some type of service to the hive (protection, metabolic breakdown)? Currently it is unclear what the expectations are for the study. Please add text that explicitly states a hypothesis.

•	Is there evidence these bacteria are active while present in hive components? Could the bacteria just be dormant (spores) while in the hive components due to a harsh environment, but easily recovered when plated on rich media? Is there any literature on the activity of these bacteria in vivo (this topic seems pertinent to the study, but is never addressed)?

•	What is the difference between “pure culture” (line 113) and “pure bacterial isolate” (line 118)? Is there a difference (there seems to be difference based on context)? Please clarify.

•	Why is table 1 a main figure in the manuscript? It should be in the supplemental. If anything some of the data from ST3 should be made into a main figure to represent the metabolic data, which seems to be a big part of the paper.

•	It would be helpful if the authors order the results and isolates based on their phylogenetic relatedness for all relevant tables (tables 2, 3, ST3, Files 1 and 2)

•	Are file 1 and 2 supplemental tables? Or are they just files that will be deposited with the manuscript?

•	For TS3, it would be nice to know what range (raw values) in which the authors are determining to be “+, -, and +/-“. I think somehow showing the degree of utilization for isolates give the reader a complete view of the data. Providing some type of range for delineating between +,-, and +/- would be sufficient for addressing the issue.

•	The authors state, “Bacillus amyloliquefaciens and B. subtilis have been recognized as the most dominant bacteria in bees foraging for food from rape flowers” and cite Wang et al., 2015. (see lines 318 – 319). The results the authors are referring to were actually presented in a previous publication by Wang et al. that characterized the diversity of bacteria in the honey stomach of bees during the rape blooming season, where Bacillus species were observed to dominate the dataset1. The publication the authors have cited is follow-up paper that mentions said results, but does not provided any such data. Please make certain to cite primary sources accordingly.
1.	Wang, M., Xu, H., Yin, G., Zhao, W., & He, S. (2014). Diversity of bacteria in the honey stomach of Apis cerana and Apis mellifera during the rape blooming period. Chin. J. Appl. Entomol, 51, 1567-1575.

•	For citations pertaining to lines 313 – 317, please clarify if the said strains of Bacillus were isolated from the honeybee gut and honey or the honeybee and/or honey. Currently the way the sentences is structured it is saying all of the strains referenced are found in both. If this is true then disregard the comment.

•	This section of the manuscript needs a bit of work. Similar to the introduction, all the structural elements are there but there is an absence of cohesiveness. The main reason for this is likely due to the absences of a defined goal/hypothesis for the study. If the authors add a brief paragraph in the beginning of the discussion recapping what was known, what was unknown, and the new information acquired by this study, it would setup the necessary framework for the paragraphs that follow.
Experimental design: •	Could you clarify the purpose of the TPC analysis for each of the hive components? Currently, I am under the impression that the goal of the TPC analysis was to demonstrate the bacterial load (total bacterial community) for each hive components. Is this true? If so, this analysis is likely not the best way to address this question. Is it possible that the TPC analysis would have been more inclusive of other microbes if additional media types and growth conditions were included? I ask because based on the results presented, it seems like the conditions provided were highly selective for bacteria in the genus Bacillus as nearly all of the isolates cultured were classified as such (37/41). Would you observe the same results with a different media type? Furthermore, when you say the hive components had “low TPC levels” what exactly do you mean? And what are you comparing these values to? Please clarify.

•	For each isolate, how many biological replicates were conducted for Biolog GenIIIPlate assay?

•	For the antimicrobial activity assay – is it possible some of strains show no or little antimicrobial activity because physical interaction with another microbe is required before antimicrobial production is activated? If the authors could address this in the manuscript it would be greatly appreciated. Furthermore, is there a reason endogenous microbes of the H. itama microbiome weren’t examined?
Validity of the findings: •	Where are the statistical analyses of datasets? For example, claims made regarding TS1 (lines 219 – 226) should have stats to backup interpretations of the reported results.

•	I would urge the authors to be cautious with their interpretations of the data collected in this study. The authors claim that in vitro metabolic profiling of Bacillus isolates suggest the presence of microbes in bee products indicating the availability of nutrients to support microbial viability (Lines 300 – 304). First, all of the data collected in this study were under in vitro conditions, which provide a glimpse into the metabolic potential of microbes, but can not be directly generalized to the function of the microbe during in vivo conditions. Furthermore, the data collected doesn’t speak to the nutrient availability in hive components or the microbial viability within said environments. Currently these ideas are not addressed in the discussion. The authors should add text to provide adequate context to their study.
Additional comments: The manuscript by Ngalimat et al characterizes Bacillus species isolated from hive components (honey, bee bread, and propolis) from the hive of the stingless bee, Heterotrigona itama. Currently, much is known about the microbiome of Apis species, especially Apis mellifera (the honey bee), with particular focus on microbiome composition, function, and the various factors that influence these processes. Overall, studies on the microbiome of other Apis species are somewhat limited compared to A. mellifera. The study by Ngalimat et al focuses on the isolation and characterization of bacterial species within the genus Bacillus that are often found associated with H. itama. The authors’ objective for this study was to elucidate the potential functional role of Bacillus species in hive components. Through utilizing culturing efforts the authors isolated bacteria, many of which were Bacillus species, from honey, bee bread, and propolis. The authors go on to characterize, in vitro, the metabolic and antimicrobial activity of a subset of isolates (N = 11). Initially I am intrigued by this study and the efforts attempted by Ngalimat et al. Overall, there are many positive attributes to the manuscript. The overall composition of manuscript is in great shape. The text is concise and easy to follow and read. The research design is sound and straightforward, and the results presented are convincing. Concerns regarding the manuscript primarily arise due to: 1) Inadequate development of the rational driving the research objective(s) (see comments on the introduction and discussion sections), 2) Absence of statistical analyses, 3) Issues with the arrangement of figures, 4) Issues with citations.


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: CHARACTERISATION OF BACTERIA ISOLATED FROM THE STINGLESS BEE, HETEROTRIGONA ITAMA, HONEY, BEE BREAD AND PROPOLIS
Review round: 1
Reviewer: 2

Output:
Basic reporting: In general the paper has been written relatively well, with the basic idea behind of the work that was carried adequately highlighted. Though, the authors need to be mindful the grammatical errors in the paper, which I believe can be further improved after a few additional rounds of checkings. Certain sentences require attention, for instance:

1.	 “:However, their  biological functions are poorly understood and mostly indicated it as a microbial contaminant  originated from pollen, flower, bees’ digestive tract, dirt, dust and …”
2.	“In addition, Bacillus species that 82 isolated from honeybee honey produced antimicrobial compounds (Zhao…”
Experimental design: In general, the work has been well-described.

Please check the sentences:

Amend the sentence “Dilution of pure cultures were prepared by performing a ten fold serial dilution in a range of 10-1 on each sample followed by incubation at 37°C with shaking at 150 rpm for 24 h.”

The sentence in the section for the “Determination of antimicrobial activity” should be amended to “The 6 mm diameter wells were cut on the agar plate using ??? specify what used to cut out the wells… and filled with 100 μl of supernatant of each isolates obtained by centrifugation at 6000 × g for 15 min at 4°C.”

This sections requires doublecking for grammatical errors
Validity of the findings: The findings appears to agree with many of reported literature, with a few novel findings that would be useful to improve the body of knowledge with regards to antimicrobial potential of the H. itama stingless bees, as well as the bee products.

I believe the findings in this study is very interesting.

However, please doublecheck the following sentences for improvement of grammar etc:

“The TPC ofpropolis ranges from 6.3 × 103 cfu/g (Ladang 10 UPM) to 1.8 × 104 cfu/g (Yayasan Al223 Jenderami) while those recorded for honey samples ranges from 0.0 cfu/g (Ladang nangka PASFA) to 8.0 × 103 cfu/g 224 (Yayasan Al-Jenderami).”.

Break this sentence, into two separate sentences for clarity. The sentence should be improved as the following: “According to the results, 41 isolates were recovered from H. itama nest products. A total of 37 screened isolates were identified as bacteria from the genus Bacillus, as analysed by Gram and endospore staining as well as catalase production (Table S2).”

Amend the grammar. It should be “The results indicated that each isolate has a different profile of substrates utilisation and chemical sensitivity as determined by Biolog…”
Additional comments: The findings in this paper, in my opinion, merits publication in PeerJ. However, it believe the paper is publication ready following minor corrections.


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: CHARACTERISATION OF BACTERIA ISOLATED FROM THE STINGLESS BEE, HETEROTRIGONA ITAMA, HONEY, BEE BREAD AND PROPOLIS
Review round: 1
Reviewer: 3

Output:
Basic reporting: I suggest the authors get editing help from someone with full professional proficiency in English. Currently, some of the sentences are difficult to understand, for example: ; 81-82; 353-355;
Experimental design: The Bacillus cereus comprises a highly metabolically diverse group of bacteria (Cepeus et al., 2013). If the objective of this study was the prospecting for strains that have desired properties, all the 37 strains should have been evaluated.
Validity of the findings: no comment
Additional comments: The manuscript "Isolation and characterisation of Bacillus spp. from stingless bee, Heterotrigona itama honey, bee bread and propolis" describes the phenotype of 37 Bacillus strains isolated from stingless bees' products.
The methods used in this study are appropriate and the data and statistical analysis are sound.
My major concerns are:

1. The current English grammar and style is not appropriate.

2. There is no clarity as to the main objective of this study.

3. In the introduction the authors wrote: "Regardless of plenty antimicrobial activities, some microbes such as Bacillus species still can survive in bee products (Lee et al., 2015) due to the robustness of bacterial endospore which is resistant to heat, radiation and chemicals (Nicholson, 2002; Setlow, 2014)." Based on this, I have some questions:
- Are Bacillus cells active in the bee products or only found in a dormant state?
- Why looking for Bacillus spp. in bee products? Why not other habitats, such as pollen, in which that they could be found in higher abundance and diversity?

Minor comments:

- Were the enzyme activity assays performed in replicates? If yes, please add this information to the Methods section.


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

Input:
Title: CHARACTERISATION OF BACTERIA ISOLATED FROM THE STINGLESS BEE, HETEROTRIGONA ITAMA, HONEY, BEE BREAD AND PROPOLIS
Review round: 2
Reviewer: 1

Output:
Basic reporting: Introduction:

In general, the major issue with the introduction is the lack of a clear hypothesis. It seems as though the authors are attempting to develop a manuscript around the following ideas: 1) bee products have beneficial properties, 2) some of the bacteria found in bee products are beneficial against pathogens, 3) Other bacteria besides LABs, might contribute beneficial properties and need to be investigated. I would urge the authors to edit the introduction so that it is simple, concise, and develops the points I have described above.

Lines 51 – 54: This sentence is extremely confusing. Rephrase for clarity.

Line 67 – 68: What do you mean by primary and secondary contamination?

Lines 65 – 66: What “products” are you referencing to? The Lee et al. 2015 paper is a study on the honey bee gut microbiome. There are other studies in the field that have cultured microbes from honey, pollen, and beebread.

Line 80 – 83: There are many studies that have begun to address this hypothesis, especially for the processing of pollen to beebread. I would suggest the authors seek out those studies and cite them as they are pertinent to this paper.

Figures & Tables:

Figure 1: please add text in the figure legend that indicates that bolded text indicates bacteria isolated in this study.

Table 2: Please put the data for B. oleronius PD3 and B. Wealsonii PD4 in the table. I understand that negative results were reported for these strains, but negative results are still results and should be reported regardless.

Table 3: Report data for isolates with negative results (see comment about Table 2).

Table S1: What are the extremely small numbers next to the values? Exponents? Either way, the text is far too small to read. The figure legend indicates statistics were performed on the data. What kind if statistics were performed? T-test? ANOVA? Was the data normally distributed? This information is not provided in the figure legend or the methods section.

File S1 and S2: In these files there are “A” and “B” columns for each isolate. What does that mean? Are these biological replicates? There is no indication of the purpose of this nomenclature. Please clarify.
Experimental design: No Comment
Validity of the findings: Results:

Lines 240 – 242: I’m a bit confused by this sentence, “Among the three nest products, propolis showed the highest TPC value……while the lowest was honey (0.0 cfu/g).” (Lines 240 – 242). Why is honey the lowest? Beebread also had a TPC value of 0.0 cfu/g for one location. Why isn’t beebread mentioned?

Discussion:

The organization of the discussion needs a bit a work. In its current state, each paragraph seems like a separate entity without any connectivity. This makes the discussion challenging to read. I would encourage the authors to revise this section into a more cohesive text. Finally, it is totally acceptable for the authors to hypothesize the context of their finds, but the authors should also note some of the limitations to the study and their ability to speculate in vivo functionality.

Lines 324 – 328: These introductory sentences are not very helpful for this paragraph that focuses on the TPC data.

Lines 324 – 326: The authors state that “interactions of bee and bacteria are still unclear”, that is not exactly true. There is a large body of literature that addresses just that topic in the honey bee. Perhaps the authors are meaning to reference the stingless bee?

Lines 326 – 328: “…, we partially discovered these enormous characteristics.” – I’m not sure if “enormous” is the right wording. I would revise this sentence.

Lines 345 – 354: In this paragraph the authors discuss some of the similar species of Bacilli observed in stingless bees and the honey bees. Additional references regarding the honey bee microbiome need to be cited. For example, a recent study by Tarpy, Mattilla, and Newton, 2015 characterize the gut microbiome of the honey bee queen. This study should be cited when the authors discuss the queen microbiome (Lines 348 – 352). There is a plethora of other studies that have characterize the microbial communities associated with the honey bee. I would strongly recommend the authors thoroughly examine the literature.

	Tarpy, David R., Heather R. Mattila, and Irene LG Newton. "Development of the honey bee gut microbiome throughout the queen-rearing process." Appl. Environ. Microbiol. 81.9 (2015): 3182-3191.

Lines 369 – 370: The authors speculate that based on the phenotypic substrate utilization assay, the patterns of utilization suggest that the bacteria analyzed might be involved in the formation of bee products. Based purely on in vitro data, I would urge the authors to be cautious with this statement. Currently, it is unclear if the bacteria isolated are active when present in bee products. As suggested by the authors (Lines 69 – 71) these bacteria might be dormant in vivo. If so, the microbes functional potential might be extremely reduced. I would encourage the authors to discuss some of the limitation to their approach. Additionally, it could also be hypothesized that the bacteria could be involved in the degradation of bee products instead of the “formation” of bee products.

Lines 328 – 329: The authors state “In this study, low level of TPC and limited types of bacteria were found.”. It should be noted that the limited profile of bacteria isolated could be due to cultivation on a single medium type and growth conditions.
Additional comments: Overall the authors have made substantial edits that have significantly improved upon the quality of the manuscript. The authors have addressed many of the concerns brought to their attention in the previous review process. For the most part, the methods and results sections are in great shape, as are the figures and tables (a few minor adjustments are needed). Nevertheless, issues remain in the current version of the manuscript. The authors need to seek out additional assistance composing the introduction and discussion sections. Currently, these sections are the most difficult to read and understand (see specific comments in the “basic reporting” section).


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

Input:
Title: CHARACTERISATION OF BACTERIA ISOLATED FROM THE STINGLESS BEE, HETEROTRIGONA ITAMA, HONEY, BEE BREAD AND PROPOLIS
Review round: 2
Reviewer: 2

Output:
Basic reporting: no comment.
Experimental design: no comment.
Validity of the findings: no comment.
Additional comments: Minor comments:

Line 29: change "from phylum Fermicutes (...)" to "from the phyla Firmicutes (...)". Firmicutes needs to be corrected in the entire manuscript. Including figures;
Line 48: change to "Stingless bees are important pollinating agents (...)";
Line 62: change "Stingless bee products such as honey are" to "Stingless bee products, such as honey, are". "such as XXX" has to be between commas. This needs to be corrected in the entire manuscript;
Lin 96: change "Investigations on the association of bacteria in stingless bee products have been focused mostly (...)" to "Investigations of bacteria associated to stingless bee products have been focused mostly (...)";
Line 399: “limited and common bacterial species” is confusing.


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: SEASONAL DYNAMICS OF MICROBIAL DIVERSITY IN THE RHIZOSPHERE OF ULMUS PUMILA L. VAR. SABULOSA IN A STEPPE DESERT AREA OF NORTHERN CHINA
Review round: 1
Reviewer: 1

Output:
Basic reporting: See general comments
Experimental design: See general comments
Validity of the findings: See general comments
Additional comments: The article by Liang et al. investigates the seasonal dynamics of the microbial communities (fungi and bacteria) found in the rhizosphere of Ulmus pumila.

The article is interesting because this tree species, which inhabits arid areas of northeast Asia, plays a major role in reducing wind erosion, accelerating vegetation restoration, and increasing nutrient accumulation.

However, the study has several important limitations:

Your introduction needs to focus on what is known on the rhizosphere of other tree species and less on the ecosystem under study (L42-59). Also, the section about other methodologies is unnecessary (L97-109).

You did not include control (bulk soil) samples, which is a common practice in rhizosphere studies. Why? Without control samples you do not know which OTUs are overrepresented in the rhizosphere compared to the bulk soil.
You stated that the sampling was representative (L404). I do not agree with this. The number of samples (n=12) is quite low. Also, you collected all the samples in one site and soil is spatially very heterogeneous. Including more sites will make the study more representative and robust.

In your material and methods you should include information about ANOSIM and RDA, as they are mentioned later in the manuscript.

You should clarify the analysis of the sequences. What do you mean by “clean tags” and “effective tags”? How many sequences were finally used? Did you rarefy your data? Most studies use PERMANOVA instead of AMOVA. Did you test all pairwise comparison in you beta-diversity analysis (L348-354)?

Quite often, the discussion is a repetition of the results. The discussion should relate the findings of your study to previous studies. That is, you should contextualize the contribution of your study. For example L420-424.

I do not see how “these results provide valuable context to inform the ecological restoration of this area, and provide significant data to evaluate the ecological functions of common and rare microorganisms in such ecosystems in future studies” (L496-499). I would say that the low number of samples and the sampling design make this almost impossible.

Minor comments:

Did you use 18S rRNA genes (L113) or ITS (L23) for the study of fungal communities? By the way, the ITS is not a gene but a region between the 16S and 23S rRNA genes.

L357-360. “In the LEfSe … relative abundance”. This information should be in a figure legend and not in the results section.

L398-401. “A total of … respectively”. This information should be part of the results section.

L426. You mention that you sequencing depth was quite limited, but earlier (L400-401) you stated than the coverage was high? This seems a bit contradictory, isn’t it?


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: SEASONAL DYNAMICS OF MICROBIAL DIVERSITY IN THE RHIZOSPHERE OF ULMUS PUMILA L. VAR. SABULOSA IN A STEPPE DESERT AREA OF NORTHERN CHINA
Review round: 1
Reviewer: 2

Output:
Basic reporting: Literature references:
Referencing should be checked as for e.g. mothur, wrong reference was supplied:
line 234 : ... within Mothur (Kropf, Ulrich, Tebbe, 2007).
Experimental design: Materials and methods:
Please clarify the section around line # 43 ... Thus, a total of 12 soil samples were collected among the three seasons.... Comment on the size (mass) of the samples collected. How representative were these samples? Have the authors additional information that supports the notion that such an approach is sufficiently robust for the type of analyses they performed?

Please consider using correction for multiple comparisons in significance tests such as Benjamini-Yekutieli, or Benjamini-Yekutieli-Hochberg.

With respect to data usage, I would also suggest to extend the analyses of bacterial 16S rRNA genes using functional imputation (programs Piecrust, Tax4Fun, or other) that would shed the light into functional gene distribution of these soils and provide an additional insight. This could be accomplished just by including a short section within Electronic Supplementary Materials.
Validity of the findings: The authors are urged to assess their significance thresholds by adopting the correction for multiple comparisons.

Conclusions are otherwise well suited.
Additional comments: Please check Figure caption as some mistakes were found.
Figure 4 -> stress values are hardly seen
Figure 6 -> legend is corrupt and the lines are broken

Figure captions -> consider extending the description of the names of your samples in figure captions:
GSP: bacterial communities in spring samples; GSU: bacterial communities in
summer samples; GFA: bacterial communities in autumn samples; FSP: fungal communities in
spring samples; FSU: fungal communities in summer samples; FFA: fungal communities in autumn samples.


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: SEASONAL DYNAMICS OF MICROBIAL DIVERSITY IN THE RHIZOSPHERE OF ULMUS PUMILA L. VAR. SABULOSA IN A STEPPE DESERT AREA OF NORTHERN CHINA
Review round: 2
Reviewer: 1

Output:
Basic reporting: See below
Experimental design: See below
Validity of the findings: See below
Additional comments: Most of my concerns have not been properly addressed.


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

Input:
Title: SEASONAL DYNAMICS OF MICROBIAL DIVERSITY IN THE RHIZOSPHERE OF ULMUS PUMILA L. VAR. SABULOSA IN A STEPPE DESERT AREA OF NORTHERN CHINA
Review round: 2
Reviewer: 2

Output:
Basic reporting: The revised (R1) version of this manuscript is a significant improvement over the originally submitted manuscript.

Some references are still not correct, e.g. the correct reference for mothur program is
https://aem.asm.org/content/75/23/7537
Introducing mothur: Open-Source, Platform-Independent, Community-Supported Software for Describing and Comparing Microbial Communities
DOI: 10.1128/AEM.01541-09

Do correct this and other references.
Experimental design: The number of samples is rather low, however authors were urged to put this low number of samples into a wider context.
The provided explanations described within their rebuttal letter could form a part supplementary material, to clarify this issue sufficiently.

Otherwise the research question was well defined and fits the scope of the Journal.
Validity of the findings: Authors improved significantly their analyses, included permanova and functional gene prediction set, provided correction for multiple comparisons.
Once the background explanation (see#2. Experimental design) is provided and included as part of the ESM, the findings will be easier to contextualize.

The findings are valid, but need to be placed within the wider scope due to characteristics of the local environment where sampling was performed.
Additional comments: Correct the references again.

Discussion section on Predicted functional genes ln 559-573:
However, inferred metabolic functional analysis indicated that season did not significantly influence inferred bacterial metabolic functions, unlike the results for diversity. Nevertheless, these analyses still indicated rich bacterial functional diversity in these rhizospheres, with the detection of 41 level two KO groups. It should be noted that there are considerable limitations in the inference of community metabolic functions via the PICRUSt analytical approach. Consequently, further studies are needed to evaluate the functions of elm rhizosphere microorganisms using other analytical tools like metagenome sequencing.

Please rephrase this section:
Functional gene distribution gives clues about metabolic potential, not the exact metabolic functions, metabolic activities.
There have been a number of reports where significant changes have been found at the level of taxonomic descriptions, but metagenomic analyses showed basically rather comparable functional gene distribution, giving rise to the conclusion, that it is the management of this genetic potential, i.e. the gene expression and regulation, that generates the observed functional differences at the ecosystem level -> nutrients for plants, plant growth, plant health, ...

Variation in soil temperature, humidity, pH, and the level of organic and inorganic nutrients, among other factors that are associated with different seasons, can all affect the structures of microbial communities (Thoms, Gleixner, 2013).  water and K content were important in this study.

environment changes -> microbes respond with adjustment in expression of their genetic material and enzymes produced -> changes in microbial physiology, activities ->some taxa grow, some don't, some die -> hence the change in microbial community structure -> yet the functional gene distribution may well remain the same, except for the fine-tuning elements of genetic regulation; the same microbes behave differently under different environmental settings; microbes from the tail of their abundance distribution may become more dominant, but they largely contain the same functional genes, just express them differently.
For environmental settings there is a need to move away from the classical medical model of one/few microbe/s one disease/effect.

This is the part that I feel would need to be included as part of the manuscript, as this gives an extended view of the importance of the presented 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: SEASONAL DYNAMICS OF MICROBIAL DIVERSITY IN THE RHIZOSPHERE OF ULMUS PUMILA L. VAR. SABULOSA IN A STEPPE DESERT AREA OF NORTHERN CHINA
Review round: 3
Reviewer: 1

Output:
Basic reporting: See below
Experimental design: See below
Validity of the findings: See below
Additional comments: In my opinion, there is not real improvement in the revised version of the manuscript.


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

Input:
Title: SEASONAL DYNAMICS OF MICROBIAL DIVERSITY IN THE RHIZOSPHERE OF ULMUS PUMILA L. VAR. SABULOSA IN A STEPPE DESERT AREA OF NORTHERN CHINA
Review round: 3
Reviewer: 2

Output:
Basic reporting: I would suggest to soften the claim in line 87-88, as the cited review only reports 'up to 30.000' species, not that the rhizosphere generally contains that many species. Also I would suggest citing the primary research article (Mendes et al. 2011) instead of the review.

The language in the two paragraphs from line 481 to 538 needs to be improved, as some sentences are hard to parse in the current form (e.g. line 506-508).
Experimental design: I am not sure it is clear from the manuscript if the same 3 trees per sampling location were sampled for the 3 sampling times or if 3 different trees were sampled each time. Please explain this more clearly.

I think that a survey of primer coverage (e.g https://www.arb-silva.de/search/testprime/ for 16S) would help in discussing why certain taxonomic groups might be missing or could be proportionally more abundant than others.

I would be interested to see an ecological/functional characterization of the fungal communities as well, by using a tool such as FUNGuild (https://github.com/UMNFuN/FUNGuild) or simply discussing the ecological roles of Fungi detected here (i.e. are they saprophytes or symbionts etc.). In my opinion that could improve the coherence of the manuscript, but might not be crucial either.
Validity of the findings: In table 3 (cited in line 483-484), please provide the values for the fungal communities, even if they are not significant.
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: MIDDLE EAST RESPIRATORY SYNDROME CORONAVIRUS AND THE ONE HEALTH CONCEPT
Review round: 1
Reviewer: 1

Output:
Basic reporting: This manuscript covered a relatively broad topic and aimed to discuss multiple aspects in Middle East respiratory syndrome coronavirus (MERS-CoV) field. The manuscript itself is quite extensive which deserves appraisal. However, this manuscript lacks focus rendering the messages to be unclear.

It is important to acknowledge that there are already several reviews out there on animal/human interaction aspect of MERS-CoV. One of this review is written by Dr. Hemida and colleagues, i.e. https://onlinelibrary.wiley.com/doi/full/10.1111/tbed.12401. Dr. Hemida’s current manuscript seems to offer a slightly different twist, i.e. using One Health perspective to assess the current MERS-CoV situation. However, the One Health aspect does not seem to be clearly outlined in the abstract or in the manuscript. Even in section 2, line 83-88, the One Health concept is narrowed into animal/human interaction, making it quite overlapping with his previously published review.

I suggest the author do a careful check-up for grammatical errors throughout this manuscript. These mistakes might seem minor but sometimes could give a different meaning. For example, in line 50, the author wrote, “… I used to do a literature search of the most up-to-date published articles…”. I believe the author intended to write, “…I did a literature search…” instead. I also suggest omitting using “we”, since this manuscript is written by one person. In the abstract, the author used “we” quite a lot, but in the manuscript, it changes into “I”.

It will be prudent for the author to consult a scientific writing consultant or to collaborate with another expert in the field, to increase both the readability and the reliability of this manuscript. Besides that, rearranging the content of this manuscript to accommodate a more One Health perspective, and adding some insights/suggestions on One Health-based intervention to stop MERS-CoV outbreaks would be beneficial to increase the value of this manuscript.
Experimental design: Several statements written in this manuscript are not well-supported by current references and/or not carefully phrased thus likely causing misinformation. Due to a limited amount of time I have to review this manuscript, I would only give several examples on this point. I highly suggest the author, either alone or with the help of collaborators or scientific writing consultant, to carefully re-evaluate this manuscript to filter out these mistakes.

Line 145-146: "The RNA may act as a potential source of infection since MERS-CoV is a positive-sense RNA virus."
There is no evidence that RNA on its own is enough to transmit the virus.

Line 160-163: "Only some members of the Camelidae family (dromedary camels, alpacas, and llamas) appear susceptible to MERS-CoV infection, which occurs naturally in dromedary camels and experimentally in alpacas and llamas (Corman et al. 2014; Vergara-Alert et al. 2017)."
This statement is not true since alpacas and llamas can be naturally infected as well like dromedary camels, as reported in https://wwwnc.cdc.gov/eid/article/22/6/15-2113_article and https://www.sciencedirect.com/science/article/pii/S2352771418300053?via%3Dihub.

Line 166-168: "Whether the absence of detectable MERS-CoV antibodies in Bactrian camel sera is due to the tested animals’ geographical location in Mongolia far from the Middle East and Africa remains unknown." It is not clear what is unknown then.

Line 169-172: "Another possibility is that this might be due to genetic factors that contribute to the resistance of Bactrians to MERS-CoV infections, which requires further investigation but suggests that genetic factors play roles in susceptibility to the viral infection." It is not clear what the sentence means.

Line 172-173: "Experimental MERS-CoV infection in both alpacas and llamas showed a  similar pattern to that of dromedary camels (Vergara-Alert et al. 2017)." This study does not do experimental infection in alpacas, thus the referenced study is not correct.

Line 188-190: "Meanwhile, the clinical profiles and viral shedding curve during the course of the MERS-CoV infection in these bats was highly similar to that in dromedary camels (Munster et al. 2016)." This statement is not fully correct nor supported by the reference.  The amount of infectious virus shedding in bats is still less compared to dromedary camels.

Line 191-193: "Interestingly, another study revealed that MERS-CoV receptors (dipeptidyl peptidase-4, DPP4) were expressed in the respiratory and digestive tracts of some insectivorous bats (Vergara-Alert et al. 2017)." Wrong reference. This study is on livestock animals, not bats.

Line 214-217: "The roles of dromedary camel milk, meat 215 products, and by-products in MERS-CoV transmission is debatable. Experimentally introducing MERS-CoV into raw milk revealed little difference between the viral stock in the milk and that maintained in Dulbecco’s modified Eagle’s medium (DMEM) (van Doremalen et al. 2014)." The author should acknowledge that this study is performed with high virus concentration. Secondly, in this study, https://www.eurosurveillance.org/content/10.2807/1560-7917.ES2014.19.23.20829, viral RNA is detected in a limited concentration in camel’s milk. Thus, at this moment, the majority of experts in MERS-CoV field agree that the risk of virus transmission through milk is really low, as also stated in FAO report.

Line 260-263: "Seroprevalence of MERS-CoV was reported in dromedary camels from different countries in Africa and Asia (Ali et al. 2017; Hemida et al. 2014); however, feral camels from Australia and the Canary islands were found to be seronegative (Crameri et al. 2015). The reasons behind this phenomenon are unclear." The author stated previously that geographical location could be one of the important factors. So saying that this phenomenon is unclear without further explanation is not correct.

Line 274-275: "The genetic susceptibility of some human populations, especially of blood relatives is unclear in the context of MERS-CoV infection." The sentence is unclear. I assume the author would like to state there are some variations in susceptibility among humans. But it is important to remember that such variation does not always do to genetic differences. Other factors, such as age and underlying comorbidities, have been proposed in many papers to cause this variation between individuals. Thus, the sentence in line 274-275 above is not only unclear but also not well-supported by current evidence.

Line 275-276: "Meanwhile, development of a risk scoring 276 system for human exposure to dromedary camels is urgently needed." It is not clear what scoring system that the author meant, and it is not clear why such a scoring system will pose as a solution for MERS-CoV outbreaks in the field.

Line 305-321: the whole section 9. It is not clear how the five progress in the control of MERS-CoV could cause the drop in the number of cases being reported, especially the third to fifth progress being mentioned. The therapeutic and control approaches, for example, are mostly not implemented in the field yet.
Validity of the findings: The manuscript itself does not have an Introduction section. The aims of this manuscript, however, are slightly outlined in the methodology section in line 54-57, i.e. "I identified some important gaps in the research dealing with MERS-CoV/human/environment in the context of the One Health concept. Meanwhile, I summarized the current acceptable theories on the emergence and evolution of MERS-CoV. Finally, I highlighted the progress made for the control of MERS-CoV."

For the conclusion, the author wrote "Nearly 6 years after its emergence, reports of MERS-CoV infection are ongoing. This may be related to the many unknown aspects of viral evolution and pathogenesis. More research is urgently needed to explore the unknown aspects of the MERS-CoV/human/animal network." This conclusion leaves a lot to be desired and does not seem to have a clear added value to the current MERS-CoV field.

I suggest the author provide an introduction section in this review to clearly outline the expected outcome generated from this review or why it is important to have this review written and published. The conclusion, ideally, would be the main insights generated from this review, based on the outline/goal described in the introduction section.
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: MIDDLE EAST RESPIRATORY SYNDROME CORONAVIRUS AND THE ONE HEALTH CONCEPT
Review round: 1
Reviewer: 2

Output:
Basic reporting: This review discusses the One Health concept as it relates to MERS-CoV. This topic was previously reviewed in 2017 by Dr. Haagman's group, who did a wonderful job summarizing different aspects of MERS-CoV circulation and different One Health intervention strategies to control transmission.
Experimental design: The author reports a methodology consistent with a comprehensive, unbiased coverage of the subject. However, this reviewer wonders if key manuscripts have been omitted from the review. For example, multiple group have looked at the potential role that goats, sheep, and horses could play but none of these references are cited. These species would be a critical part of the One Health concept and need to be addressed. Additionally, the author is missing citations describing screening in Bactrians on line 165 as well as a seropositive 'naturally infected' alpaca on line 163.

There are multiple sections that may be incorrectly cited. Please double check the citations on lines 145, 153, 1576.

This review is organized into multiple sections that flow nicely. However, each section needs to be broken down into multiple paragraphs. A few examples include:
- MERS-CoV in humans: This section starts with a description of MERS-CoV in humans, moves to viral genetics and circulation, and then back to clinical information. This section could be strengthened by only describing human clinical data and moving the clinical information described around line 119 to the beginning of the section
- MERS-CoV in animals: line 194 - experimental models should be moved to a different section and expanded or removed
- line 206, 232 can be broken into different paragraphs or removed
Validity of the findings: This review focuses on the One Health concept as it relates to MERS-CoV. This relationship is extremely important and should absolutely be explored.

However, the author makes a few claims that may not be supported by primary literature.
- The author mentions multiple times that the research rate has declined - this should be removed.
- line 151: the authors suggest establishing an infection model but then describe doing this in naturally infected populations – is this really an infection model?
- The author mentions multiple times that different exposure rates are likely due to genetic factors. To this reviewer's knowledge, there is no published research supporting this. Human differences could be explained by cultural, medical, etc factors. Additionally, a lack of positive samples in camels could be due to a lack of exposure  - the review should be modified to reflect this. Some of these claims are purely speculative, and should either be modified with supporting evidence or labeled as speculation.
- The author writes about an undiscovered reservoir, but does not offer any evidence supporting this.
-
Additional comments: A lot of really good work clearly went into this review.

There are a few areas that could be improved with additional editing for English grammar.

For example:
- run-on sentences: examples on lines 62, 170
- the tense is not consistent: example on line 74
- grammar editing: examples on lines 12, 184, 186, 229, 281, 307-309
- line 203: MERS is the human syndrome, MERS-CoV is the virus
- line 142: please change 'runny nose' to an appropriate clinical description