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: A CDK1 PHOSPHOMIMIC MUTANT OF MCAK IMPAIRS MICROTUBULE END RECOGNITION
Review round: 1
Reviewer: 2

Output:
Basic reporting: The authors describe the role of CDK1 mediated phosphorylation on the activity of MCAK. The background information provided in the text are well described and give a full picture of the biology of the kinesin MCAK.
The main conclusions of the work are that the T537E-MCAK phosphomimetic mutant has i) an attenuated microtubule depolymerisation activity; ii) a reduced ATPase rate in the presence of polymerised microtubules; iii) a shorter residence time at the microtubule end than the WT and iv) it cannot promote ADP dissociation.
Experimental design: The experiments are very well presented and designed. However, although the raw data support some of the conclusions, the general interpretation of the results need major revisions. Please find below the list of comments that the authors can consider during the revision of their work.
Validity of the findings: 1. First set of results (described from line 99 to line 121). According to the data, the T537E-MCAK can turn over ATP in solution and bind to unpolymerised tubulin. How do the authors explain the differences in the ATPase rate of T537E-MCAK in the presence of unpolymerised vs. polymerized tubulin? Could the T537E mutation reduce the lattice-stimulated ATP cleavage due to a conformational change of T537E-MCAK which does not occur upon binding of unpolymerised tubulin?
The authors could measure the binding rate of T537E-MCAK to unpolymerised and polymerised tubulin and suggest some hypothesis on the mechanism of action of the MCAK mutant.

2. In the second paragraph of the results (lines 132-133) is written that “Wild type MCAK makes short diffusive interaction with the microtubule lattice”. It can be assumed that this is due to the initial high microtubule binding affinity of ATP.MCAK and, subsequently, to the lattice promoted ATP cleavage which weaken the MCAK interaction with the microtubules (Friel and Howard 2011, The EMBO Journal). Given the reduced ATPase rate of the MCAK phosphomimetic mutant in the presence of microtubules, it is very likely that T537E-MCAK is predominantly in the ATP-bound isoform. Thus, it is surprising that the affinity for the microtubule lattice is not significantly changed for MCAK mutant (line 138-139). Since ATP.MCAK tightly binds microtubule filaments, should not the authors expect a longer residency time for T537E-MCAK along the microtubule lattice and a reduced diffusion rate than the WT?  For this reason, the authors might consider that the attenuation of the depolymerisation activity of the phosphomimetic mutant might be also due to the loss of ability of T537E-MCAK to reach the microtubules end (see also ‘General comments’ below).

3. In the third set of results (from line 148 to line 176) is shown that the T537E-MCAK mutant has a slow ADP dissociation rate at microtubules end. However, the rationale and the conclusions of this experiment (see also ‘General comments’ below) do not seem very clear and robust.
Concerning the rationale of the experiment, I am wondering whether the number of T537E-MCAK molecules bound to ADP at the microtubule end is sufficient to test the ADP dissociation rate. The data presented in paragraph 1 and 2 of the results show that it is very unlikely that T537E-ADP.MCAK can reach the microtubule end because of i) the reduced ATPase rate of T537E-MCAK bound to microtubules (0.335±0.081s-1 compared to 4.75±0.057s-1 in WT) and ii) the short residence time of T537E-MCAK at the microtubule end (0.64±0.02s compared to 2.03±0.13s for the WT). For these reasons, I suggest moving these experiments in the supplementary data section because they are supporting previously results but do not significantly add novel information.
Additional comments: a. At lines 213-215 the authors write that “This mutant still displays the characteristic diffusive interaction of MCAK with the microtubule lattice and can still reach the microtubule end”. However, this statement is not very well supported in the text/figures in which, instead, is shown that T537E-MCAK has a reduced residence time at the microtubules end. In addition, this sentence does not sustain the conclusion that T537E-MCAK does not distinguish between the microtubule lattice and the microtubule end. Although this conclusion might be very intriguing to explain the attenuated T537E-MCAK depolymerisation activity, there is no direct proof for this and sounds too speculative at this stage of the work.

b. The conclusion that the reduced depolymerisation rate of T537E-MCAK is dependent on the attenuated ADP dissociation from T537E-MCAK at the microtubules end, might not be fully appropriate (see also point 3 above). Indeed, the authors do not consider the hypothesis that, given the reduced residence time at the ends, the mutant MCAK that does not get to the microtubule tip because is not able to diffuse along the lattice (see also point 2 above). This hypothesis is also in accordance with another work showing that T537E-MCAK predominantly localizes along the microtubule lattice of the mitotic spindle (but not at the ends) and display a very weak staining at centromeres in HeLa cells (Sanhaji et al., 2010, Mol Cell Biol).
In other words, the authors might discuss and consider the hypothesis that the CDK1 mediated phosphorylation of MCAK does not directly affect the catalytic activity of the kinesins at microtubule end but regulates the ability to diffuse along the microtubule lattice by modulating the ATP-ADP cycle on MCAK.


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: A CDK1 PHOSPHOMIMIC MUTANT OF MCAK IMPAIRS MICROTUBULE END RECOGNITION
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors have addressed all points listed during the first revision of the paper. The results are very well explained and the conclusions are robust.
Experimental design: I appreciate the authors have now performed the experiment to investigate the ability of the T537E-MCAK mutant to get to the microtubule end. This additional experiment clearly show the T537E-MCAK phosphomimetic mutant can reach the microtubule end although its residence time is much shorter than the wild type. Overall, this experiment greatly contributes to support the conclusion that the T537E-MCAK is not able to distinguish between microtubule lattice and microtubule end.
Validity of the findings: The findings about the role of the CDK1-mediated phosphorylation of MCAK are strongly supported by the data and I recommend this work to be published in PeerJ.
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: A MICROBIAL SURVEY OF THE INTERNATIONAL SPACE STATION (ISS)
Review round: 1
Reviewer: 1

Output:
Basic reporting: The submitted manuscript reports the microbial assemblage of the International Space Station (ISS), and compares the ISS assemblage to microbiomes of homes and humans. The manuscript is generally well-written with somewhat sufficient and relevant references to support their claims. However, given the very low number of samples (which is in itself understandable because of the sampling site and circumstances), one may expect more rigorous analyses to be done to further describe the ISS assemblage based on the limited number of samples. For example, the manuscript can add the following analyses/discussions to make up for the limited number of samples included:

1.1 The authors have compared their findings with the previous work by Venkateswaran et al. (2014), but do not compare their findings with that of Ichiro et al. (2016).

1.2 Given that the crew vent sample appears to differ from the majority of other samples, would be interesting to investigate this sample further at the sub-genus/strain/species level.

1.3 Greater efforts will need to be addressed to the figures. For example, in Figure 2, the title of the legend groups appear to lack consistency in capitalization ("Surface_Type" but "node"). Also, there should not be underline in the figure legend "Surface_Type." In Figure 4, it is extremely hard to visualize the different sample groups, using the current colour labelling scheme (which is very gradient-like). The authors may want to manually fix the colour for each sample group. Also, the list of sample groups currently are in alphabetical order, but this order does not help in the overall understanding of the ecology. Alternatively, sample groups can be listed by their built environment group (e.g. all sample groups within Homes listed first, then sample groups within ISS, or vice versa). Figure 5 Panels B and D, and Figure 6 suffer from the same weakness.
Experimental design: 2.1 The Methods section is described in detail.

2.2 It is implied that the authors have filled the knowledge gap by using the Illumina technology to increase the sequencing depth to explore the ISS microbiome in greater detail. Perhaps strengthening that point in the introduction and conclusion will add impact to the manuscript.

2.3 The analyses described appear to have done well, however additional analyses should be performed to strengthen the impact of the work given the very low sample number.

2.4 The lack of controls in assessing for potentially contaminating taxa is a great weakness of this work, but the authors have explained the reason for not having them. However, it would still be beneficial to include controls that the lab group has subsequently produced after the start of this work, to show readers that the authors made an effort to account for potential contamination during sample prep and sequencing. If possible, this is highly recommended. If not, please explain why this is not possible.
Validity of the findings: 3.1 Given the low number of samples, it is necessarily to indicate in discussion that the lack of replicates may affect the validity of the results.

3.2 There is no indication where the sequences of the ISS samples can be accessed. Please make that available in a public repository.

3.3 While the authors indicate that the findings will have in space exploration in the future, as most readers will not be heading to space in the immediate future, can readers learn anything about the built environment on Earth from this ISS study?
Additional comments: Line 39: change "Earth homes" to "homes on Earth"

Line 93: change from "example" to either "exemplify" or "assess"

Line 185: twelve base change to "twelve-base"

Section "Comparison of ISS surfaces in homes on Earth and to the Human Microbiome Project:" besides the point that surfaces on the ISS were selected to mirror that selected for a previous home study, please indicate more succinctly the rationale for comparing the microbiomes of the ISS to homes. Is this because humans will potentially living in the space in the future? If anything, it is my humble opinion that the ISS environment may more resemble that of cleanrooms. Unfortunately, cleanroom environments are not described in this study, and a simple taxonomic or community analysis should have been described. Also, as any differences in methodology can potentially affect sequence-based microbial community surveying results, please indicate whether these different studies adopted identical sample collection, preparation, and sequencing methods. If not, add a disclaimer that method differences may have affected the comparison of the studies.

Line 272: outside air change to "outdoor air"

Line 311: suggest to remove double negative in sentence.

Line 326-330. Is there an ecological/rational reason for the discrepant community found in the crew vent sample, and its resemblance to human gut communities?

Please also fix the in-text citation and references throughout. Additional proof-reading of the manuscript will be beneficial to minimize typos (random hash-tags appearing in manuscript, mathematical power symbol represented as ^ instead of a superscripted 2, etc.). Refer to https://peerj.com/about/author-instructions/ for more information.


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

Input:
Title: A MICROBIAL SURVEY OF THE INTERNATIONAL SPACE STATION (ISS)
Review round: 1
Reviewer: 2

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: Lang et al. present a manuscript that examines the microbiome of the ‘built environment’ of the International Space Station (ISS) using 16S rRNA sequencing on the Illumina MiSeq. Sample diversity did not cluster by sample surface. Comparisons of ISS swabs to data from homes and humans revealed that the surfaces of human homes are more similar to ISS surfaces than human body surfaces are, but that neither is significantly similar.  The proportion of known human pathogens on the ISS surfaces was comparable to those in ventilated rooms in a health-care facility.

Overall this is a clearly-worded, concise manuscript. The question of which microbes inhabit the surfaces of human-built environments is both important and interesting, especially in the case of the ISS. Many of the comments/edits that I have suggested are minor, with the exception of a few bigger concerns that I would like to address. Firstly, in the introduction where the authors mention studies that also used deep sequencing to examine ISS microbiome, it would be helpful to have a sentence or two expanding on the results that they obtained, in order to compare your results. You did have a comparison in the results section to the Venkateswaran study, so you could expand upon the Novikova and Castro studies there. At least a comparison of the surface samples that are relevant to your study. While I understand the necessity of closed OTU picking for the comparison of your data to HMP and Homes data, it would be good to include a statement about the limitations of this method. Also, you are losing a lot of your data by rarefying to 1000 or less sequences for your comparisons with HMP, Homes and mechanically ventilated areas. Could you please explain why it was necessary to rarefy to such a level? Finally, you should put the statistical numbers stated in the text in their appropriate figures too, for example the Adonis tests. Below are some smaller edits with reference to their location in the text:

-	Line 32 in the Abstract – “as plans for human exploration and colonization...come to fruition.” I think it was phrased better in line 53 of the introduction where it says “possibility of colonization”. It comes off a little strong when stated as a fact.
-	As stated above I think it would be worth expanding on the findings of previous studies in paragraphs 2 and 3 of the introduction
-	Line 97 This link leads to a site that directs you to a new link. So maybe just put the new link?
-	Line 165 – for Table 1 it might be good to have an explanation in the supplemental information on why you correlated particular Homes samples with particular ISS samples. Most of them are intuitive but for example the similarities between air vents and door trimming is not obvious
-	Line 181 – Should the EMP primers have a citation?
-	Line 192 – This is a little vague – do you mean there were equal concentrations of each product in the pooled sample?
-	Line 199 – Is there a link for the QIIME workflow?
-	Lines 201 and 209 – there are some ### and I’m not sure if some information is missing there. The sentence in 201 is definitely not complete.
-	Line 228 Describe limitations of closed OTU reference picking
-	Line 232 – you are missing a space after the bracket
-	Line 235 – Did you mean rarefy to “1000 sequences”
-	Line 243 – Why rarefy to 700 sequences here instead of using the 1000 cutoff from before
-	Line 299 – Missing a space before the bracket


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 WALL COMPOSITION AND LIGNIN BIOSYNTHETIC GENE EXPRESSION ALONG A DEVELOPMENTAL GRADIENT IN AN AUSTRALIAN SUGARCANE CULTIVAR
Review round: 1
Reviewer: 1

Output:
Basic reporting: Authors should provide the comparative analysis of lignin biosynthesis pathway genes expression data and lignin content from different cultivars available till date. This will give support to this study that how it adds additional information with the preexisting data.
Experimental design: In Materials and methods section, remove the para describing about HCT gene from line 71-82 and place it in discussion section.
Validity of the findings: Expression analyses of the genes provided by the authors did not match with the lignin content across developmental gradient. Early step genes e.g., PAL, C4H, 4CL, and C3H are also involved in biosynthesis of variety of flavonoids so their expression can not be solely related with lignin production. Downstream pathway genes e.g., CCR and CAD are highly expressed in young tissue (A), which has lesser lignin content as compared to other tissues. Similarly, CCR and CAD showed higher expression in roots but no data for cell wall component is provided. F5H and CCoAOMT are not showing any specific expression pattern across developmental tissue stages. I suggest authors to add functional validation experiments of one or more genes e.g., CCR/CAD/COMT using gene silencing or gene editing approach to support data provided in this manuscript.
Additional comments: Manuscript is written well.


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 WALL COMPOSITION AND LIGNIN BIOSYNTHETIC GENE EXPRESSION ALONG A DEVELOPMENTAL GRADIENT IN AN AUSTRALIAN SUGARCANE CULTIVAR
Review round: 1
Reviewer: 2

Output:
Basic reporting: Figure 1 Should be improved as mentioned in general comments.
Experimental design: Authors should explain better why they did chose the cultivar and also why 9 months. All these information should be added to the text.
Validity of the findings: Work here analyzed did not represent any unprecedented data as commented by authors in the manuscript. By the other hand, they add some knowledge about lignin accumulation mainly in root which for me is the main result of this manuscript. Authors also elucidate the possibility to use some promoter in further genetic manipulation basing on their expression profile. Still, would be desirable if authors could add S/G ratio values in order to check if the expression of some key enzymes (such as F5H and COMT) could be related to S/G in different parts of sugarcane culm.
Additional comments: Line 38-40: Authors should explain this sentence better
Line 86: Authors should explain why they choose this stage (9 months)
Line 98-99: Authors did not mention that RNA integrity was checked before proceeding to DNAse treatment
Line 126: Authors must include in figure 1 a picture of sugarcane cultivar that they analyzed at 9 months showing details of five sections here analyzed and roots as well. This definitely will help readers to understand which part of sugar cane were studied here
Line 132: sentence should be replaced by separated into two categories
Line 135: word fall should be replaced all long the manuscript. Inadequate word
Line 137: Change word ‘Of’  for ‘Among’
Line 139-143: Rewrite the sentence. CAD showed the lower expression difference among all five sections analyzed with different variation ranging from 25 to 40%. This example should also be used to rewrite previous sentences comparing results.
Line 171: This explanation should be added to M&M section to explain why use this cultivar. Authors should also explain if they expect that this smut-resistant feature could have or not any relation with lignin biosynthesis/accumulation.


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 WALL COMPOSITION AND LIGNIN BIOSYNTHETIC GENE EXPRESSION ALONG A DEVELOPMENTAL GRADIENT IN AN AUSTRALIAN SUGARCANE CULTIVAR
Review round: 1
Reviewer: 3

Output:
Basic reporting: The manuscript by Bewg and Coleman describes the patterns of gene expression related to lignin metabolism and the composition of stem and root materials of the Australian cultivar KQ228. The manuscript is well written in general and brings results that deserve to be published in my opinion.
The discussion about gene expression is well balanced in itself. However, the authors failed in contextualizing the existent knowledge about cell walls. As a result, the manuscripts end up quite lignin centric. This won't be a problem if authors haven´t measured cell wall composition. In this part, the manuscript is quite weak, describing methodology poorly and not discussing it adequately in the face of the available literature.
Because authors did not discuss the carbohydrate portion of the wall at the same level they discuss lignin gene expression; the manuscript fails to take most of what the results can give.
My opinion is that the manuscript is publishable, but it needs major changes so that it reports the scientific context of sugarcane cell walls, describe methods accurately and discuss more profoundly the results in relation the available literature.
Experimental design: Preparation of material: A picture or drawing of the plant and the positions sections were made could be useful for the reader and other authors that intend to repeat the experiment.

Cell wall composition:
1)    Please describe how acid hydrolysis was made instead of just citing another paper. Instead of giving the components of a solution only, please report time and temperature. Why was sulfuric acid chosen? It usually hydrolyzes cellulose and decreases the proportion of pectin and hemicellulose monosaccharides. This happened as can be seen in Table 1. What authors want to see by accessing mostly cellulose? As lignin is bound to hemicellulose – the arabinoxyl residues of arabinoxylans – wouldn´t it be better to look at the levels of arabinose and therefore use TFA instead of sulfuric acid for hydrolysis?
2)    How was acid linin extracted? What acid lignin means. There are several different methods for lignin extraction. Explain why this method was chosen. The lack of adequate methodological description prevents interpretation of the results reported in Table 1. The reader would have to find literature that describes methodologies and guess what authors have used in this paper.
3)    Usually, cell wall monosaccharides are analyzed on Dionex because other types of chromatography do not separate well some of them. Was the Waters chromatography efficient to separate them? It would be important to add a chromatogram as supplemental material to inform the reader about the accuracy of monosaccharide measurements.
Validity of the findings: Results

1)    Didn´t authors notice that there is a strong negative correlation (r2=0.89) between total lignin and arabinose? How authors interpret that?
2)    The percentage of total lignin is quite high. Could this be an artifact of the method used? Authors should comment that.
3)    Authors cannot call the composition “secondary cell wall”. Hydrolysis with sulphuric acid attacks all cell walls, including the primary ones.

Discussion
For discussion on sugarcane cell wall composition, authors failed to include De Souza et al., 2013, which would be a better comparison than maize, which is relatively distant taxonomically from sugarcane and miscanthus.
Lignin (yield only) in sugarcane roots has been reported by Leite et al. 2017, Annals of Botany. The authors found rather low  yields in roots of a Brazilian variety
Authors missed an important trend that is the inverse correlation between lignin and arabinose. It is accepted that ferulic acid, the holder of lignin in the wall of grasses is esterified to arabinose residues of arabinoxylans (the main hemicellulose in cell walls). (see De Souza et al., 2013, Bioenergy Research for sugarcane and De Souza et al., 2015 Journal of Exp. Botany). This could be interesting for the discussion of the manuscript.
Additional comments: The manuscript by Bewg and Coleman describes the patterns of gene expression related to lignin metabolism and the composition of stem and root materials of the Australian cultivar KQ228. The manuscript is well written in general and brings results that deserve to be published in my opinion.
The discussion about gene expression is well balanced in itself. However, the authors failed in contextualizing the existent knowledge about cell walls. As a result, the manuscripts end up quite lignin centric. This won't be a problem if authors haven´t measured cell wall composition. In this part, the manuscript is quite weak, describing methodology poorly and not discussing it adequately in the face of the available literature.
Because authors did not discuss the carbohydrate portion of the wall at the same level they discuss lignin gene expression; the manuscript fails to take most of what the results can give.
My opinion is that the manuscript is publishable, but it needs major changes so that it reports the scientific context of sugarcane cell walls, describe methods accurately and discuss more profoundly the results in relation the available literature.

Introduction

The introduction does not have a single word about the composition and structure of sugarcane cell walls (e.g., De Souza et al., 2013 Bioenergy Research). It doesn´t mention either important work performed on sugarcane lignin (e.g., Bottcher et al. 2013 Plant Physiology; Vicentini et al. 2015 PloS one). Another example regarding lignin is the work of Jung et al. 2013, Plant Biotechnology Journal.
Authors should contextualize better sugarcane cell walls in the introduction.

Methods

Preparation of material: A picture or drawing of the plant and the positions sections were made could be useful for the reader and other authors that intend to repeat the experiment.

Cell wall composition:
1)    Please describe how acid hydrolysis was made instead of just citing another paper. Instead of giving the components of a solution only, please report time and temperature. Why was sulfuric acid chosen? It usually hydrolyzes cellulose and decreases the proportion of pectin and hemicellulose monosaccharides. This happened as can be seen in Table 1. What authors want to see by accessing mostly cellulose? As lignin is bound to hemicellulose – the arabinoxyl residues of arabinoxylans – wouldn´t it be better to look at the levels of arabinose and therefore use TFA instead of sulfuric acid for hydrolysis?
2)    How was acid linin extracted? What acid lignin means. There are several different methods for lignin extraction. Explain why this method was chosen. The lack of adequate methodological description prevents interpretation of the results reported in Table 1. The reader would have to find literature that describes methodologies and guess what authors have used in this paper.
3)    Usually, cell wall monosaccharides are analyzed on Dionex because other types of chromatography do not separate well some of them. Was the Waters chromatography efficient to separate them? It would be important to add a chromatogram as supplemental material to inform the reader about the accuracy of monosaccharide measurements.

Results

1)    Didn´t authors notice that there is a strong negative correlation (r2=0.89) between total lignin and arabinose? How authors interpret that?
2)    The percentage of total lignin is quite high. Could this be an artifact of the method used? Authors should comment that.
3)    Authors cannot call the composition “secondary cell wall”. Hydrolysis with sulphuric acid attacks all cell walls, including the primary ones.

Discussion
For discussion on sugarcane cell wall composition, authors failed to include De Souza et al., 2013, which would be a better comparison than maize, which is relatively distant taxonomically from sugarcane and miscanthus.
Lignin (yield only) in sugarcane roots has been reported by Leite et al. 2017, Annals of Botany. The authors found rather low  yields in roots of a Brazilian variety
Authors missed an important trend that is the inverse correlation between lignin and arabinose. It is accepted that ferulic acid, the holder of lignin in the wall of grasses is esterified to arabinose residues of arabinoxylans (the main hemicellulose in cell walls). (see De Souza et al., 2013, Bioenergy Research for sugarcane and De Souza et al., 2015 Journal of Exp. Botany). This could be interesting for the discussion 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: CELL WALL COMPOSITION AND LIGNIN BIOSYNTHETIC GENE EXPRESSION ALONG A DEVELOPMENTAL GRADIENT IN AN AUSTRALIAN SUGARCANE CULTIVAR
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comments
Experimental design: No comments
Validity of the findings: No comments
Additional comments: In this revised manuscript, authors answered all the questions/comments raised by reviewers so in my opinion this manuscripts has sufficient data to publish. Authors improved this manuscript well, however; my only concern is about the English language/grammar which need to be improved for publication and it would be great if authors could provide the lignin content and cell wall composition data for roots.


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 WALL COMPOSITION AND LIGNIN BIOSYNTHETIC GENE EXPRESSION ALONG A DEVELOPMENTAL GRADIENT IN AN AUSTRALIAN SUGARCANE CULTIVAR
Review round: 2
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: No comments
Validity of the findings: No comment
Additional comments: The authors have improved the previous manuscript version and also asked all the question resulting in a better version. All the doubts regarding plant material used, developmental stages used for experiments were answered.


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 WALL COMPOSITION AND LIGNIN BIOSYNTHETIC GENE EXPRESSION ALONG A DEVELOPMENTAL GRADIENT IN AN AUSTRALIAN SUGARCANE CULTIVAR
Review round: 2
Reviewer: 3

Output:
Basic reporting: Article is relevant for the area of bioenergy
Experimental design: Authors corrected the problems pointed out accordingly
Validity of the findings: Results are sound and valid. Deserve to be published
Additional comments: Authors have changed the text and properly responded the queries. In my opinion the manuscript is now acceptable for publication.


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

Input:
Title: MICROCOS MAGNIFICA (SPARRMANNIACEAE) A NEW SPECIES OF CLOUDFOREST TREE FROM CAMEROON
Review round: 1
Reviewer: 1

Output:
Basic reporting: New species are significant scientific discoveries, and it is important that such findings be published (and for new species to be properly described and named).  This reviewer finds that such work is within the stated scope of the journal PeerJ.

The structure of the manuscript is consistent with that seen in short articles in the field of plant taxonomy.  The structure also seems to be acceptable according to PeerJ standards.

The author of the manuscript is a first-language English speaker, but this reviewer finds that the way the text is written may be difficult for non first-language English speakers to understand.  It almost seems as if the text was written in a hurry.  Let me recommend that long sentences should be shortened and the writing should be done in a more direct (telegraphic) style.

The line drawing (Fig. 1) by Andrew Brown is fine work, but the version seen by this reviewer appears to be an early draft (not a finished plate).  The version presented is not acceptable for publication.

The distributional map (Map 1) is also fine, but it would help to orientate the readers (especially those unfamiliar with the geography of Cameroon) if some additional landmarks could be added, e.g., administrative boundaries (regional and international) as well as the locations of major cities and/or regional capitals.

It would be really helpful if high-resolution scanned images of the specimens cited could be posted on the Kew Herbarium Catalogue (http://apps.kew.org/herbcat/gotoHomePage.do ) or a similar on-line database.  This way the specimen-images and associated information would be publicly accessible.

Below are references to some additional, seemingly relevant literature which the author may want to cite in the Introduction of the revised manuscript:

Brunken U, & Muellner AH. 2012. A new tribal classification of Grewioideae (Malvaceae) based on morphological and molecular phylogenetic evidence. Systematic Botany 37: 699-711.  [Grewia and Microcos as distinct genera, placed in different subclades of tribe Grewieae Endl.  The ‘Microcos subclade’ also includes Colona Cav., Goethalsia Pittier, Luehea Willd. and Lueheopsis Burret.]

Chattaway MM. 1934. Anatomical evidence that Grewia and Microcos are distinct genera. Tropical Woods 38: 9-11.

Czarnecka E, Wiland-Szymańska J, Gawrońska K. 2006. Phytogeography of the genus Microcos L. (Malvaceae, Grewioidae) in Africa. Biodiversity Research and Conservation 3-4: 269-271.

Nurul-Aini CAC, Noraini T, Latiff A, Chung RCK, Nurhanim MN, Ruzi M. 2013. Systematic significance of petiole anatomical characteristics in Microcos L. (Malvaceae: Grewioideae). Malayan Nature Journal 65 (2&3): 145-170.

Shokefun EO, Ayodele,AE & Akinloye AJ. 2016. Systematic importance of leaf anatomical characters in some species of Microcos Linn. section Eumicrocos Burret in Nigeria. American Journal of Plant Sciences 7: 108-117. http://dx.doi.org/10.4236/ajps.2016.71012

Sprague TA. 1909. The section Microcos of Grewia in Africa. Bulletin of Miscellaneous Information (Royal Botanic Gardens Kew) 1909 (2): 66-68.
Experimental design: Fine although it would be good for the reader to know approximately how many specimens of African Microcos were studied by the author in the K, P and WAG herbaria as part of the pattern-matching exercise leading to the conclusion that the plants from Mt Kupe (Cameroon) are a new species.

This reviewer tested the hyperlink provided by the author for his search of African Microcos in the herbarium of MNHN Paris, and the resulting page was not of Microcos or Malvaceae sensu lato but was instead for a specimen-record of Ledermanniella schlechteri (Podostemaceae).  This hyperlink thus needs to be double-checked and corrected if necessary.

Given that the last worldwide treatment of Microcos was published by Burret (1926), that Burret was based at the Botanischer Garten und Botanisches Museum Berlin-Dahlem, and that the Berlin herbarium was largely destroyed during WW2, it would be interesting for the reader to know to what extent our knowledge & further study of African Microcos is hampered by the type specimens having been lost.  To what extent are Burret's types still extant or duplicated in other herbaria?  Why was the Berlin herbarium evidently not consulted in the course of this study?
Validity of the findings: The author’s ‘Key to the species of Microcos tree species in Africa west of DRC & the Congo River’ includes only three species and is thus evidently incomplete. For example, the recent article by Shokefun et al. (2016) reported there are 8 species of Microcos in West Africa, and they reportedly sampled six of these species for their leaf anatomical study of Nigerian Microcos. The “missing” species in the present author’s key would thus seem to include at least M. africana, M. barombiensis, M. iodocarpa, M. malacocarpa, M. oligoneura and perhaps others as well.

Although I have no reason to doubt the author’s taxonomic judgement, the apparent omission of several West African species from the author's key leads this reviewer to think that with further checking the plants from Mt Kupe (Cameroon), proposed by the author as a new species M. magnifica, might prove to be a species previously described by a different author and under a different species name.
Additional comments: It is acknowledged there are differences of opinion on whether the major clades within the order Malvales should be treated as subfamilies within a broadly circumscribed Malvaceae or whether it is better to treat them as separate families.  In fact the choice of rank for these taxa is more-or-less arbitrary.  However, in the interest of avoiding any possible confusion, this reviewer recommends that just one family-name should be used in the TITLE of the manuscript, i.e. the family-name should be given as either Sparrmanniaceae or Malvaceae-Grewioideae, but not both.  Of course it would still be appropriate to present some background information on these alternative family treatments in the INTRODUCTION.


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

Input:
Title: MICROCOS MAGNIFICA (SPARRMANNIACEAE) A NEW SPECIES OF CLOUDFOREST TREE FROM CAMEROON
Review round: 1
Reviewer: 2

Output:
Basic reporting: There are some inconsistencies in citations and in formatting in the references, but these are minor issues.
Experimental design: The manuscript presents a description of a new species from West Africa. It appears to satisfy all of the requirements set out in the International Code of Nomenclature for Algae, Fungi, and Plants (2012).
Validity of the findings: The author has made a convincing argument that this is indeed a new species and he has placed it in context of other taxonomic and conservation research in West Africa.
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: MICROCOS MAGNIFICA (SPARRMANNIACEAE) A NEW SPECIES OF CLOUDFOREST TREE FROM CAMEROON
Review round: 1
Reviewer: 3

Output:
Basic reporting: The paper provided interesting information on the new species of an endangered tree discovered in Cameroon, Africa. The abstract of this paper was adequately summarised the contents and the keywords were well representative of the paper. The introduction, results, discussion and references were clear, adequately discussed and cited.
Experimental design: In general the it was excellent and clearly written. The author appears to comply with the provisions of the ICN (McNeill et al., 2012) that are necessary for validly publishing a new species. Was this paragraph (Lines 132-142) necessary to be included in this section or could it be shortened the paragraph by just citing provisions in ICN.
Validity of the findings: The results are reasonable given as there were no inflorescences and flowers material since 2004 from all the reported locations.
Additional comments: *Lines 1 & 62: Delete this family (or Sparrmanniaceae) in the title and abstract. A synonym of Malvaceae sensu lato.  Follow the Angiosperm Phylogeny Group IV (2016).
*Line 88-91: Author should include the subfam. Dombeyoideae as the genus Schoutenia from the ‘former Tiliaceae’ was placed in this subfamily. The article of Cheek (2007) was written for the family Sparrmanniaceae only. Better to cite Heywood et al. (2007) which was included other families such as Brownlowiaceae, Tiliaceae s.s. and Pentapetaceae.
*Line 108: Was this key to genera modified by the author based on his additional observations on both the genera.
*Line 111: Yes, in some Grewia species but it is not in Microcos.
*Line 150: Incomplete sentence, hanging.
*Line 176: The word “Verrucate” was used in the introduction and species description.
*Lines 297-298: Would the author will also consider to study the molecular phylogenetic of both Grewia and Microcos in Africa in order to establish the generic delimitation of these two genera for Africa.
**Map: Author should have a general map of Africa to show the location of Cameroon, then enlarge with this map to indicate the distribution of the new species.
***Other comments and suggestions to improve the paper, please refer to the attached PDF file.


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: MICROCOS MAGNIFICA (SPARRMANNIACEAE) A NEW SPECIES OF CLOUDFOREST TREE FROM CAMEROON
Review round: 2
Reviewer: 1

Output:
Basic reporting: New species are significant scientific discoveries, and it is important that such findings be published (and for new species to be properly described and named). This reviewer finds that such work is within the stated scope of the journal PeerJ.

The structure of the manuscript is consistent with that seen in short articles in the field of plant taxonomy. The structure also seems to be acceptable according to PeerJ standards.

This reviewer suggests that all generic and species names where first mentioned in the main text should include the relevant authority for that name.  The authority for the genus Microcos should also be cited in the Abstract, unless this would go against the journal’s editorial policy.  As it now stands, there is one generic name (Schoutenia) and several species names (e.g., the names listed under the subheading ‘Distribution and habitat’) that are provided without authority.  The generic name Microcos is mentioned in the first sentence of the Introduction, but the authority for this name doesn’t appear until the second paragraph; this problem could be solved by moving the authority to the first mention of the name Microcos in the first paragraph, or possibly by rearranging the paragraphs of the Introduction so that the background info about the genus appears first, with the specifics about the discovery of the new species Microcos magnifica coming later.  There are two species names (Microcos gossweileri and Microcos coriacea) that first appear in the key to species, but without authority; in the case of the name Microcos coriacea, the authority is provided where the name is mentioned again later in the text, but in the case of Microcos gossweileri the key is the only place where this name is mentioned.  The main point is that authorities for names are important and that these authorities should be mentioned consistently in the revised manuscript.
Experimental design: No comment.
Validity of the findings: In a previous version of this manuscript, the present reviewer pointed out that the author’s ‘Key to the species of Microcos tree species in Africa west of DRC & the Congo River’ includes only three species and is thus evidently incomplete. For example, the recent article by Shokefun et al. (2016) reported there are 8 species of Microcos in West Africa, and they reportedly sampled six of these species for their leaf anatomical study of Nigerian Microcos. The ‘missing’ species in the present author’s key would thus seem to include at least M. africana, M. barombiensis, M. iodocarpa, M. malacocarpa, M. oligoneura and perhaps others as well.

To this comment, the author has responded that ‘The key presented is to the tree species of Microcos in West-Central Africa, and not to the climbing species which include those mentioned by the paper referred to’.

This response is accepted, but this reviewer further notes it would be good for the author to mention explicitly the fact that there are additional Microcos species in West & Central Africa that are climbers, not trees (& perhaps state approximately how many species).
Additional comments: Once these minor, added comments have been addressed, then this reviewer recommends that the paper should be accepted for publication.


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

Input:
Title: MICROCOS MAGNIFICA (SPARRMANNIACEAE) A NEW SPECIES OF CLOUDFOREST TREE FROM CAMEROON
Review round: 2
Reviewer: 2

Output:
Basic reporting: The author addressed the concerns of the reviewers and the revised manuscript sontinues to satisfy the requirements of the International Code of Nomenclature for the publication of a new species name.
Experimental design: The experimental design is appropriate for the subject.
Validity of the findings: The conclusions seem appropriate.
Additional comments: There are two unresolved bibliographic citation issues -- missing journal number and questionable publication date. The attached version includes copy editing of the References especially as these were checked carefully against 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: MICROCOS MAGNIFICA (SPARRMANNIACEAE) A NEW SPECIES OF CLOUDFOREST TREE FROM CAMEROON
Review round: 2
Reviewer: 3

Output:
Basic reporting: This paper provides a new endangered tree species discovered from West Africa. The abstract, keywords, introduction, results, discussion and references are clear, adequately discussed and cited in the paper. This work is within the stated scope of the journal PeerJ.
Experimental design: It is excellent and clearly written. It follows the provisions of the ICN (McNeill et al., 2012).
Validity of the findings: The results are reasonable given by the author in the paper that this is indeed a new species in West Africa.
Additional comments: The author should follow APG IV (2016 in  Bot. J. Linn. Soc. Vol. 181: 1-20), Mabberley (2017 in Mabberley's Plant-Book) and Steven's APG website (http://www.mobot.org/MOBOT/research/APweb/) to use family Malvaceae-Grewioideae which is widely accepted by all botanical journals. Sparrmanniaceae is a synonym in Malvaceae s.l. now as mentioned in Mabberley (2017) and also in Steven's APG website. The novel dismemberment of Malvaceae by Cheek (2006) and Cheek in Heywood et al. (2007) was not well-accepted by the botanical community/journals. In addition, the Heywood et al (2007) publication was not widely distributed and had not updated since 2007 as compared to the Steven's APG website and Mabberley (2017).

Other comments and suggestions to improve the paper, kindly refer to the attached PDF file.


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: SKIN TEMPERATURE AND REPRODUCTIVE CONDITION IN WILD FEMALE CHIMPANZEES
Review round: 1
Reviewer: 1

Output:
Basic reporting: The authors investigated body temperature changes of pregnant and cycling chimpanzee females in the field. They have used a technology new to behavioral ecology to test two clearly stated hypotheses. The first is that surface body temperatures will increase throughout the swelling cycle and peaking at maximum tumescence. The second hypothesis is that the temperature patterns of pregnant females will mimic those of non-pregnant females. The manuscript is well-written, well-structured, and clearly organized raw data and Rmarkdown analyses details have been shared as supplemental information.

I have the following minor comments regarding basic reporting:

1.	If females have evolved a strategy to conceal temperature changes as part of a broader strategy to conceal pregnancy, one must assume that males can detect the slight temperature changes that would correspond with pregnancy. Is it logical to assume male chimpanzees would be able to detect such small differences in female skin temperature? Is there any literature that would suggest temperature to be a meaningful, detectable signal to male chimpanzees, or to other species? (The authors do mention that male elephants were more attracted to female elephants with increased skin temperature Hilsberg-Merz 2008 ,
but presumably the attraction could have been due to olfactory or other cues also associated with reproductive state. They also mention male primates responsive to skin color and tone, but not temperature  in the Higham et al 2011 reference).  I think it is fine to explore this hypothesis as an extension of the concealed pregnancy hypothesis, but wanted to encourage the authors to include more justification for their hypothesis that is based on temperature perception if it is available. If it is not available, this lack of knowledge should be explicitly included in the introduction.

2.	Number of cycling and pregnant females should be included in the abstract.

3.	Figure 2: Is there a reason why the y-axis does not have equally spaced intervals? These should be equally or clearly labeled on the y-axis as reflecting a specific scale.
Experimental design: The research question is well defined, relevant and meaningful. I have the following minor comments regarding experimental design:

1.	What transformations were made to the variables (lines 158-159)? This information should be included in the main text, or reference to the supplemental information should be made here.

2.	Has IRT been used before on wild chimpanzees? If so, are the methods stated in paragraph beginning line 109 based on previous studies?

3.	How much do the image analysis results depend on the polygon drawing? It seems there should be inter-rater reliability on average temps obtained due to the user-defined polygons.
Validity of the findings: While the data are somewhat inconclusive, the authors have shared important new methodological approaches and been upfront about the limitations of their results. I have the following minor comment about validity of the findings:

1.	The authors are very upfront about limitations in their design (paragraph beginning line 274). Should decisions about photographing distance/time/lighting also be included here as variables that may influence findings, given the rarity with which IRT is used in the field?
Additional comments: Additional minor comments:

Line 51: “cattle animals” – reword as cattle, livestock, or farm animals.
Line 42: parenthesis missing around citation
Line 74: “In a first step” – reword as “As a first step”
Line 75: suggest deleting “seemingly strategic”
Line 77: change “which” to “whom”
Line 123: “sampled” refer to sampled with IRT?
Line 125-6: could females with offspring <4 years of age been cycling, even at a low probability? If so, rephrase.
Line 171: “this” effect and “the” interaction – it’s not clear which variables are being referred to
Line 202: is “deflated” a common term for minimal swelling? If not, consider replacing.
Figure 1: It is difficult to discern the content of the images, is there perhaps a standard image available not showing the infrared that could be shown side by side? Alternatively, could some labels be placed on the photos for reference?


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: SKIN TEMPERATURE AND REPRODUCTIVE CONDITION IN WILD FEMALE CHIMPANZEES
Review round: 1
Reviewer: 2

Output:
Basic reporting: This manuscript had several typos and poor English construction in some parts. I would encourage the authors to make sure they carefully review a manuscript before submitting it for publication.

I was never convinced about the purpose of this study. There may well be temperature changes during the reproductive cycle – such as seen in humans and other animals – but it’s not clear why the authors have jumped to the conclusion that any temperature change would serve as a “signal” to males. Has anyone ever proposed that humans use genital temperature as a cue? Or do cattle researchers think bulls use vaginal temperature of cows as signals? I doubt it. I don’t get the significance of temperature in communication.

Also, remember that most of what’s physically causing the swelling of female chimpanzee ano-genitalia skin is the interstitial fluid (mostly water). Some parts of the manuscript seem to imply the swelling is mostly blood. That’s not true.
Experimental design: The authors admit there were several problems with the actual design. I wonder if it would have been best to first set up an experimental design that would test the validity of the technology used in that setting, at those distances, and in those environmental conditions.
Validity of the findings: Mostly this represents negative results - which is OK in this case. Graphic details were well presented.

I appreciate the fact that the authors went to great lengths to describe the shortcomings of the study, but it bordered on overkill - as though it underscored the lack of importance and planning for the study.
Additional comments: Careful observation of female chimpanzee swelling patterns allow for prediction of pregnancy very early on. When observation is made daily (which is possible at Budongo), one can easily map the irregular patterns of early pregnancy and predict delivery date. See the Wallis and Goodall 1993 paper for details on this and further discussion about the value of swelling during pregnancy.

I would recommend carefully assessing the goal of the study. Maybe I'm missing something, but it seems you are suggesting that skin temperature may be being used as a cue for males and there's no logical explanation given for this.


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: SKIN TEMPERATURE AND REPRODUCTIVE CONDITION IN WILD FEMALE CHIMPANZEES
Review round: 1
Reviewer: 3

Output:
Basic reporting: This manuscript was clearly divided into different sections: introduction, methods, results and discussion. Overall, I could follow the prose in each section.

For me, the main drawback was the set up for the rationale of the study. I did follow the logic that based on prior research (40-50), we may expect female chimpanzees’ skin temperature to vary over the reproductive cycle. However, I did not understand the rationale for predicting that pregnant females at maximal tumescence will mimic the temperature profile of non-pregnant females at maximal tumescence in order to confuse paternity. I wonder, is there evidence of this in other species? Reading the authors’ description of a study on elephants and rhinos (41-44), it was not clear whether males were more attracted to females during oestrous specifically due to skin temperature changes, or other signals (I could not access the cited article). If there is evidence that certain species use skin temperature of potential mates to assess reproductive state, it should be discussed in more detail in the introduction. If there is not literature on this topic, why should we assume that male chimpanzees can and do attend to the skin temperature of females and that females evolved a temperature profile to deceive males and confuse paternity?

Some language in the manuscript was ambiguous, causing me confusion:

201-204: “Generally, pregnant females had lower surface temperatures than cycling females when deflated and during smaller swelling stages (stages 0 – 2, Figure 2), of less than 1°C overall. This pattern changed later in the cycle, with pregnant females having higher skin temperature compared to cycling females”

It is confusing to apply the words “cycle” and “cycling” to both pregnant and non-pregnant females. The authors differentiate two groups of females “cycling vs. pregnant females” (11-12, 201-202) but then in the same sentence, mention the cycles of both pregnant and cycling females (203-204). The authors should select unambiguous phrasing for the different female reproductive groups and use it consistently throughout the manuscript (e.g. perhaps non-pregnant females).

Another example of confusing language is referring to pregnant females as non-reproductive:

94: “if pregnant females follow an evolved strategy to conceal their non-reproductive state”

Grammatically speaking, throughout the manuscript there were areas of awkward language (e.g. 40: “strands of research”; 74: “In a first step”; 293: “which has not or seldom been used”). Cleaning up these phrases will allow the reader to concentrate on the research, rather than the grammar.

53: The authors state, “we are not aware of systematic use of this technology on wild animals” but see Thompson et al. 2017, Journal of Thermal Biology, for a study on wild howler monkeys:
http://www.sciencedirect.com/science/article/pii/S0306456516302182
Experimental design: I was pleased to see research aimed at better understanding wild female chimpanzee physiology, as there is much discover in this area. In addition, I appreciate the authors highlighting how infrared thermal imaging is a tool that can be used to study animals noninvasively.

I found the authors’ two study aims to be clearly conveyed:
1. Do non-pregnant females have higher skin temperatures during estrous compared to anoestral phases?
2. Do pregnant females at maximum tumescence have similar skin temperatures compared to non-pregnant females at maximum tumescence?

The authors also included a lot of detail about the statistical methods, which was useful.

On a critical note, I have a concern about study methodology. I question how the authors designated pregnant versus non-pregnant females using the presence or absence of offspring after the average gestation period of chimpanzees elapsed following thermal image collection (114-120). During my own experience conducting pregnancy tests on wild female chimpanzees, pregnancy loss ostensibly occurred during the early months of gestation (based on several consecutive positive pregnancy tests followed by negative tests). Evidence of early pregnancy loss is also mentioned in Emery Thompson (2005, pg 147-148). This means that images of females in early pregnancy could have been included in the non-pregnant female category. I know it is not possible to get around this issue, but at least mentioning it will allow for better assessment of the results by the reader.
Validity of the findings: The authors state: “…we did not find any difference in skin temperature between measures taken from anoestral and oestral stages in cycling females. This is inconsistent with the existing literature, and casts some doubt on the possibility that fertility is associated with a general thermal signature in female chimpanzees” (242-245).

I wonder about validity of infrared thermal imaging, especially in a wild environment. Although the authors control for ambient temperature, humidity, and recording distance in their statistical models (which is good), they do not mention potential drawbacks of infrared thermal imaging.

Some captive studies indicate low reliability of infrared thermal imaging to assess temperatures in primates:

http://www.jzar.org/jzar/article/view/132

http://onlinelibrary.wiley.com/doi/10.1111/j.1600-0684.2007.00214.x/full

It may be useful for the authors to mention whether any steps were taken to assess efficacy of their thermal imaging data. For example, Pizzi et al. (2015) mention examining reliability coefficients.

http://www.jzar.org/jzar/article/view/132

Regarding the discussion, I am not convinced that because skin temperatures for pregnant and non-pregnant females were most similar during maximal tumescence, that skin temperature is necessarily part of a female strategy to remain sexually attractive and confuse paternity. The authors do not explore any alternative explanations. For example, it is possible that skin temperature is not a deceptive signal in chimpanzees, but rather, something about being maximally tumescent increases body temperature regardless of pregnancy status. There is much research on wild chimpanzee females documenting changes that occur during maximal tumescence including increased: copulation rates (Watts 2007), male sexual competition over females (Emery Thompson and Wrangham 2008), and female resistance to male solicitation (Stumpf and Boesch 2005). Could increased activity and social upheaval lead to small temperature increases during maximal tumescence? It is certainly possible. Because the authors’ dataset is modest, and they do not present the reader with clear evidence that skin temperature is a signal in animals, the discussion is not very compelling. In particular, the use of the Hiramatsu et al. 2017 citation (285) as support seems like a reach, as it is about facial coloration in rhesus macaques, as assessed by humans. The manuscript could be improved by focusing the discussion more closely on the data presented and acknowledging competing explanations for the observed temperature patterns observed.
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: SKIN TEMPERATURE AND REPRODUCTIVE CONDITION IN WILD FEMALE CHIMPANZEES
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: In this revision, the authors have addressed the minor concerns that I had with the original submission.


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: SKIN TEMPERATURE AND REPRODUCTIVE CONDITION IN WILD FEMALE CHIMPANZEES
Review round: 2
Reviewer: 2

Output:
Basic reporting: This version is much improved. The basic reporting and article structure are fine - and it appears most of the relevant literature have been included.

See below for more details.
Experimental design: I find no problems with the experimental design, although it may be useful to carefully review the methods and results section with the editorial staff; some of the wording is awkward and less clear than could be achieved with some additional effort.
Validity of the findings: I'm pleased with the new version. Many of my concerns about the initial version have been addressed. In particular, the authors have toned down their suggestions about the "signalling" potential of temperature of the genitalia.

One thing that concerned me last time that I failed to bring up: If there is anything about temperature that helps communicate information to the males and influence their behavior, we should be just as interested in how the temperature change influences the FEMALES' behavior. To imply that something going on in a female is only important to study as it relates to males is short-sighted.  In other words, this is akin to suggesting that the anogenital swelling of a female is only about communicating to the male. We wouldn't ignore the very obvious tactile stimulation being experienced by the female herself - and we have plenty of data showing very proceptive behavior by females during times of swelling.

Another thing to consider is that, though anogenital tumescence occurring during pregnancy is very likely a phenomenon that helps with sociosexual relationships, we can't say it is ONLY about confusing paternity. There are studies from captive conditions that confirm sexual attractivity and receptivity during pregnant (while swollen) - but those same studies show a difference in males' grooming and genital inspection rates. So, actual masking of pregnancy may or may not be going on. In other words, they are being treated slightly differently from the non-pregnant females - and still having affiliative behaviors (including sex) shown to them.
Additional comments: Though the manuscript is much improved and I support publication, there are still a fair number of typos and basic sentence structure problems throughout. Much of this will be caught by careful proofreading by the editorial staff.

Some specific areas of concern (these are just some examples):

line 37: extra parenthesis should be deleted
line 57: re-word this bit. You refer to a "swelling cycle" before explaining what that is. for those unfamiliar with chimpanzees, they need an introduction.
line 63: be careful when referring to swelling "size." It's not really about the physical size but the level of tumescence (and lack of "wrinkles").
line 87 (and elsewhere): You may want to avoid using "oestrus" - and just stick with fertile.  Many researchers argue that the term oestrus should be limited to those animals that have an extremely discrete period of sexual receptivity that is directly related to the ovulatory period. Clearly, chimpanzees exhibit interest in sexual behavior outside the time of ovulation (though they DO show higher interest while the swelling is present). Thus, I would caution how you use the term and - if you're going to use it, at least include a short discussion/disclaimer about the term.
line 97, 99: extra parenthesis
line 111: missing end period
line 279: You mean to write "during pregnancy"
line 326: Period is missing after "fertility" --- and similar missing punctuation occurs throughout the manuscript.

In other words, provide a careful proofreading by multiple people to catch these minor mistakes and address the other issues I've mentioned here. At that point, I think it will be suitable for publication.


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

Input:
Title: SKIN TEMPERATURE AND REPRODUCTIVE CONDITION IN WILD FEMALE CHIMPANZEES
Review round: 2
Reviewer: 3

Output:
Basic reporting: Overall, the manuscript is improved compared to the previous submission. Upon the advice of the editor/reviewers, the authors have provided clarity in several areas, including the sample size of females (both pregnant and not), as well as some of the background literature cited. I also found that this version of the manuscript was easier to read throughout all sections, as the authors made the recommended changes regarding sentence clarity and grammar. There were some minor grammar/typographical errors, which I note under "General Comments" as they did not greatly affect the manuscript's readability.
Experimental design: I appreciate the authors response to the critique about the limitations of designating pregnant versus non-pregnant females using presence/absence of offspring after the average gestation period of chimpanzees elapsed following thermal image collection. However, I do not think the possibility of pregnant females being included in the non-pregnant female dataset is explicitly stated (lines 127-136). The authors have mainly added a justification for not relying on pregnancy tests, which is not the core issue. A clear sentence would be something like, “As we relied upon the presence/absence of offspring after the average gestation period of chimpanzees elapsed following image collection, it is possible that some females we designated as 'not pregnant', may have been in the early stages of pregnancy when thermal images were recorded, and then subsequently did not carry the pregnancy to term.”
Validity of the findings: While I do think the authors were more cautious about the discussion of their findings in light of the pregnancy concealment hypothesis in this version of the manuscript, my main critique stands. The authors do not explore any alternative hypotheses for why pregnant and non-pregnant maximally tumescent female chimpanzees have similar temperature profiles.

I copy and paste what I stated in my initial review, as it still is applicable:

“The authors do not explore any alternative explanations (for their findings). For example, it is possible that skin temperature is not a deceptive signal in chimpanzees, but rather, something about being maximally tumescent increases body temperature regardless of pregnancy status.”

Considering that a) this study has a very small sample size of pregnant females b) the temperature changes recorded throughout the study are very small in magnitude, and c) there is no evidence that male chimpanzees can detect changes in skin temperature of females, it seems like a huge misstep to completely ignore alternative explanations for the authors’ findings.

It is certainly more simplistic (Occam’s razor) to conclude there is something about being maximally tumescent that increases body temperature regardless of pregnancy status, rather than arguing that female chimpanzees have evolved a strategy to mimic tiny temperature changes that males can somehow attenuate to.
Additional comments: The authors have done a good job responding to and addressing the previous critiques. Moving forward, the most important thing the authors can do is acknowledge alternative explanations for their results (other than the pregnancy concealment hypothesis). This can be done easily in the discussion.

Secondly, minor changes include being explicit about the designation of pregnancy status, and finally, cleaning up the grammatical and typographical errors.

34: or dogs -> and dogs

35: deployed -> employed or utilized

56: may be useful to add “wild” before “female chimpanzees”

150: fur -> hair

226: “surface temperatures” -> skin surface?

235: body temperature -> skin surface temperature

288-294: Very confusing section. What are these studies about? How were they conducted? Needs more explanation.

314: The line about difficulty getting hormonal samples is a bit confusing to me. There’s plenty of hormonal work from Emery Thompson, Deschner, Crockford and others (at Budongo and elsewhere). Perhaps it was not feasible for this study’s timeframe or budget?

326: "skin" is capitalized and should not be


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: COMPARATIVE ANALYSES OF PUTATIVE TOXIN GENE HOMOLOGS FROM AN OLD WORLD VIPER, DABOIA RUSSELII
Review round: 1
Reviewer: 1

Output:
Basic reporting: Although the English has been improved from the previous version of the same paper, which I also reviewed, there is still some repetition between sections. Zoological details are also frequently inaccurately given: eg Protobothrops mucrosquamatus is not a New World pitviper; on line 101, the word “crotalin” should be “crotaline” while on line 230, the word “crotalinae” should be capitalised. Line 331: the correct spelling of the Latin name of Russell’s viper is Daboia russelii. Line 345: correct spelling is Viperidae. There are too many figures of dubious value (even if the analysis was considered sound, for which see following sections).
Experimental design: In a previous review of this study for another journal, I pointed out that while a major comparison made in the paper was between "Old World vipers" and "New World vipers", crotalines are present in the Old World too, and it was unclear whether they were being included in the OWV category, or whether the comparison was in fact between the Viperinae and the Crotalinae subfamilies (since all the NWV are crotalines). The authors have amended the analysis to apparently compare crotalines and viperines instead, but they now describe Protobothrops mucrosquamatus as a New World pitviper, which it is not (note also that I also doubt that any re-analysis has actually be done since the results reported for the comparative analysis are identical (word for word) to the previous version.
Validity of the findings: Although the units being compared have apparently been improved, compared to the previous version, and the wording slightly changed so that they no longer claim the “fished” sequences to be “venom-associated” as they did in the former version, there are still some unjustified assumptions being made which invalidate the analysis. Foremost among these is that the genes fished out of genomic DNA extracted from the skin have anything to do with expression in the skin…they do not. Without transcriptomic studies, we have no idea where they are expressed. They may be expressed in the venom gland and they may be expressed in the skin, but could also be unexpressed or expressed all over the body. This invalidates all the conclusions being drawn and I therefore will not comment on them further.
Additional comments: Although the authors have deleted a comment suggesting that conventional sampling can adversely affect the snakes from this version as requested by me  in my previous review, I have recently become aware that according to Indian Wildlife Protection Act, 1972, and its subsequent amendments, even the shed skin (not exuviate, which is an incorrect term as I have already pointed out) is the property of the Government. Hence, it does not really circumvent the need to obtain permits. Nevertheless the ability to recover high quality DNA from the shed skin is certainly worthy of a note in a journal focusing on methodological studies. However, additional details will be needed such quality of the assemblies (N50, % coverage etc.).

As I have already suggested in my previous review, it would perhaps be of interest to do a phylogenetic analysis to see if those encoding proteins that have been found in the venom of Russell's viper or related spp in the past (ie from EST or transcriptomic studies) for which the tag "venom- associated" can be justified, are more closely related to each other than to non-toxic housekeeping genes (e.g. Jacobo Reyes-Velasco, Daren C. Card, Audra L. Andrew, Kyle J. Shaney, Richard H. Adams, Drew R. Schield, Nicholas R. Casewell, Stephen P. Mackessy, Todd A. Castoe; Expression of Venom Gene Homologs in Diverse Python Tissues Suggests a New Model for the Evolution of Snake Venom. Mol Biol Evol 2015; 32 (1): 173-183. doi: 10.1093/molbev/msu294; Casewell NR, Huttley GA, Wuster W. Dynamic evolution of venom proteins in squamate reptiles, Nat Commun. 2012, vol. 3 pg. 1066). However, you would need to bear in mind that you just have coding sequence data, which will be confounded by strong selection pressure (see Malhotra A, Creer S, Harris JB, Thorpe RS. 2015. Toxicon 107(Pt B):344-58). The noteworthy finding in this work is that DNA suitable for NGS can be obtained from shed skin and the report ought to focus on this aspect, but probably additional analyses would be needed to compare the quality with other more standard sources.


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: COMPARATIVE ANALYSES OF PUTATIVE TOXIN GENE HOMOLOGS FROM AN OLD WORLD VIPER, DABOIA RUSSELII
Review round: 1
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: When the residue identity was compared and discussed, the authors seemed to use hydrophobic vs polar as the only criteria, which is useful but not complete. For instance, in figure 2 and page 16, F changing to I removes the bulky aromatic ring, whereas S could be a phosphorylated site as opposite to the N in the same position. This could bring bigger difference in the protein structure and function than just changing the polarity. The authors need to address this to improve the argument.

In figure 2, residues 67 and 68 don’t align with the original sequence (above figure 2B). It is hard to figure out the corresponding counterpart residue. The author can either change the font of the sequence or point out simply by adding arrow. Same issue in figure 6A, it is not clear to pinpoint residue 117, 18 and 19. Adding an arrow to point to the secondary structure would be helpful.

In figure 4 and page 18, ’ Of the residues that are evolved in the members of crotalinae, the second residue, a positively charged one, alanine (A) is present only in the members of viperinae, which is replaced by a hydrophobic residue, proline (P), in the crotalines and elapids’, which is the positively charged residue? Ala is not charged. Is this supposed to be Arg (R)?

In figure 6 (B and D) and page 19 ’The pockets appeared small in all cases for the elapids, and largest in the case of viperines’. It would be useful and straightforward to quantitatively describe the size of pocket.

In figure 6 E and page 19, ’ Similarly, residue 46 of the CAP domain and residues 4 and 31 of the CRISP domain showed rotamer conflict for the viperines’. Residue 4 is in the loop region, which could experience highly dynamics motions and might be different rotamer configuration. How significant of this? Does different rotamer configurations imply anything in the protein function or it is purely due to the dynamics in the loop. It would be useful to show the side chain in the figure to clearly display the rotamer conflict between different speicies.

Several references are missing in the reference section. For instance, in page 23, ‘..When we compared the 4 published studies (Kalita et al. 2017; Mukherjee et al, 2016; Sharma et al. 2015; Tan et al. 2015)…’ Kalita et al. 2017; Mukherjee et al, 2016 and Tan et al. 2015 are not listed in the literature cited. This happened in other places too and the literature cited is very short considering the reference talked in the maintext. The authors need to read full text carefully and add the corresponding references accordingly in the literature cited 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: SDMTOOLBOX 2.0: THE NEXT GENERATION PYTHON-BASED GIS TOOLKIT FOR LANDSCAPE GENETIC, BIOGEOGRAPHIC AND SPECIES DISTRIBUTION MODEL ANALYSES
Review round: 1
Reviewer: 1

Output:
Basic reporting: This manuscript provides detailed documentation concerning the release of a new version of SDMtoolbox: 2.0. As the use of geospatial analyses is continually increasing in many ecological fields, the development and introduction of new tools such as this that can be used for robust study design is highly important.  Generally, this manuscript and the associated “Getting Started” and “ User Guide” are clear and well written. However, I have provided detailed edits in the attached document that can improve organization and clarity of the manuscript, getting started, and user guide documents. The User Guide needs page #s to match the Table of Contents. Additionally, some of the language is unprofessional and needs to be changed as I noted in the detailed edits. Overall, the User Guide was straight-forward, however I received some toolbox errors when following the User Guide as closely as possible, and I have included the error logs for reference. I think that if a better description of the files that are being used for each step and their relative location are added, these errors may be avoided. Finally, there is a lot of detail in the User Guide concerning Maxent, however a description of the new Clog Log function is absent; this should be added.
Experimental design: N/A
Validity of the findings: N/A
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: SDMTOOLBOX 2.0: THE NEXT GENERATION PYTHON-BASED GIS TOOLKIT FOR LANDSCAPE GENETIC, BIOGEOGRAPHIC AND SPECIES DISTRIBUTION MODEL ANALYSES
Review round: 1
Reviewer: 2

Output:
Basic reporting: Please follow correct citation style (sometimes publication year is within brackets and other times it is not)
Experimental design: Ok
Validity of the findings: Ok
Additional comments: Reviewer 1:
SDMtoolbox 2.0: The next generation python-based GIS toolkit for landscape genetic, biogeographic and species distribution model analyses.
I congratulate the authors for creating and updating SDMtoolbox 2.0. The toolbox aids the automation of rigorous spatial analyses; thus, it is highly desirable among geospatial modelers and conservation professionals. My recommendation is to accept with minor revision. I encourage the authors to make suggested changes and resubmit for publication. Here are my comments.
Detailed Comments
Line 36, a total of 79 scripts
Line 40, future climates,
Line 55, a series of
Line 56, complicated spatial analyses in ArcMap (ESRI) and python
Line 55, line 108, and others, please write abbreviations in full at first use.
Line 74, Rewrite the last sentence.
Line 89, e.g.,
Line 101, importance of Bias files in Maxent
Line 117, delete brackets, ..tools batch project or define projections of input rasters….
Line 118, delete ‘aims to’, another set of tools facilitate batch exportation of images or aid in RGB band visualization of multiband rasters
Line 156, rewrite. Sentence starting As following is not grammatically correct.
Line 163, make sure all figures are mentioned in the text.
Line 164,insert ‘in’,  it can be done in several ways
Line 191, “lower levels”, did you mean resulting from lower regularization multiplier values
Line 196, delete “(i.e. Bio1)”
Line 205, that is more sensitive details of ? sentence appears incomplete
Line 207, “which subsequently is implement in the”, sentence appears incorrect
Line 217, tests and evaluates?
Line 241, if the journal allows this should be written as footnote or in the acknowledgment section.
Please follow correct citation style (sometimes publication year is within brackets and other times it is not)
I installed the tool using the software installation guide provided in the supplemental material. The user guide needs some editing as well. Example, first sentence needs the preposition “to”. It should read like “designed to automate”. The second paragraph needs a comma immediately after SDMtoolbox 2.0.
Table of contents lists page 215 while the document is only 95 pages.
General comments:
Line 213, the latest maxent default combination is:  L, Q, P, H which appears to be more appropriate than the previous maxent versions that included all of them (i.e, L,Q,P,H and T). Are the users able to use this new maxent default combination in SDMtoolbox 2.0?
The methods section is very brief, can the authors expand the methods section a little bit.
ESRI is an institution that frequently changes its software versions. Given this fact, what is the authors long-term plan to keep SDMtoolbox running on new ArcGIS software versions? Can SDMtoolbox become a standalone tool?


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: SDMTOOLBOX 2.0: THE NEXT GENERATION PYTHON-BASED GIS TOOLKIT FOR LANDSCAPE GENETIC, BIOGEOGRAPHIC AND SPECIES DISTRIBUTION MODEL ANALYSES
Review round: 2
Reviewer: 1

Output:
Basic reporting: This manuscript provides detailed documentation concerning the release of a new version of SDMtoolbox: 2.0, and will be an excellent contribution to PeerJ. Following the edits and suggestions of the reviewers, the authors have greatly improved the manuscript and the associated “Getting Started” and “ User Guide” for the toolbox. They also made changes to the script to correct previous errors. I fundamentally disagree on the continued use of "The 10 commandments of SDMtoolbox 2.0", especially by beginning each line with "Thou shall". This is, in my opinion, the only unprofessional part of the document. I have no further edits or suggestions.
Experimental design: No comment
Validity of the findings: No comment
Additional comments: No additional comments


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

Input:
Title: SDMTOOLBOX 2.0: THE NEXT GENERATION PYTHON-BASED GIS TOOLKIT FOR LANDSCAPE GENETIC, BIOGEOGRAPHIC AND SPECIES DISTRIBUTION MODEL ANALYSES
Review round: 2
Reviewer: 2

Output:
Basic reporting: Ok
Experimental design: Ok
Validity of the findings: Ok
Additional comments: I have minor comments.
The discussion section reads well but other sections need additional work.
Line 111, sentence not clear, rewrite.
Line 122, sentence not clear, particularly use of the verb visualizing
Line 130, incorrect use of punctuation marks. Delete the colon and all semi-colons, and replace the last phrase with "to name a few". Or rewrite.
Line 155, a coma is need after OR. Or rewrite
Line 203, delete (i.e mean annual temperature)

79 scripts in the main document vs 78 in the user guide. Which is correct?
User guide table of content still refers to page 215


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: SDMTOOLBOX 2.0: THE NEXT GENERATION PYTHON-BASED GIS TOOLKIT FOR LANDSCAPE GENETIC, BIOGEOGRAPHIC AND SPECIES DISTRIBUTION MODEL ANALYSES
Review round: 3
Reviewer: 1

Output:
Basic reporting: Ok
Experimental design: Ok
Validity of the findings: Ok
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: CONSTRUCTING A COMPREHENSIVE GENE CO-EXPRESSION BASED INTERACTOME IN BOS TAURUS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The article is acceptable in this area
Experimental design: 1-	The authors claimed that they constructed the first multi-tissue gene co-expression network in cattle (Lines 1,23,68,162,289,231 and 323), which is not true. The first large-scale multi-tissue gene co-expression network in cattle has been already constructed by Beiki et al (2016).
2-	Combining a large number of experiments into a single robust analysis will minimize the effects of variables that can plague individual experiments. In contrast, the authors just used gene expression information from single animal (one sample per tissue) to construct the cattle multi-tissue network. Why not use all available gene expression data for this species?
3-	It is well known that unwanted noise and un-modeled artifacts such as batch effects can dramatically reduce the accuracy of statistical inferences in high-throughput experiments. Unfortunately, the authors did not adjust the data for these sources of noise, which may have biased all the results of this study.
4-	The version of the reference genome used in this study need to be added in the method section (line 80).
5-	What’s the rationale behind the selection of the most variable genes? Filtering genes based on their variability will result in information loss during network construction.  For example, while transcription factors may have very subtle expression changes between different biological conditions, the may have a very large phenotypic impact. Variation filtering can easily lose this useful information.
Also, line 141-143, the authors mentioned that because the large number of genes were not differentially expressed between samples (tissues?), they decided to filter genes based on their variability. Differential expression analysis results are highly dependent on the number of samples used in the study. How many samples used per tissue in this study? If only one, how can differential expression analysis be performed based on a single sample per tissue?
6-	Eigen value definition needs to be corrected on line 110. In WGCNA, Eigenvalues are calculated based on Singular Value Decomposition (SVD) not PCA and defined as the first left singular vector (referred to as the eigenvector) that explains the maximum amount of variation in the expression matrix.
7-	Instead of the description of network topology based of different network statistics specifically developed for WGCNA networks (network heterogeneity, network density, network centralization…) why did the authors use topological centrality analysis in Cytoscape (line 119)?
8-	What is the benefit of the shortest path analysis (line 121)  while TOM based neighbor analysis can be easily conducted on the data?
9-	the Results and methods sections are not fully separated in the manuscript. For example, lines 128-177 described the method used in the study while included in the results section.
10-	The reference gene set used in the functional enrichment analysis (KEGG pathway and GO term analysis) was not included in the method section.
11-	The significant level of connection between genes needs to be selected based on the TOM values distribution. What basis did the authors use -  0.01 as the significant TOM connection strength (line 215)?
12-	The sentence at line 130-131 needs to be re-written as it unclear.
Validity of the findings: I have enough concerns with the methods used that I am not confident in the validity of the finding of this project.
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: CONSTRUCTING A COMPREHENSIVE GENE CO-EXPRESSION BASED INTERACTOME IN BOS TAURUS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper from Chen et al. is overall written well with however some typos and/or unclear sentences (e.g., L105-107, confusing the “as more gene as possible”; L115: “interested genes” should be “gene of interest”) throughout the whole manuscript.
The authors are right in pointing out the importance of having an interactome in bovine. The author’s hypothesis was “that the complex genetic traits related to cattle production are reflected by the perturbation of gene-gene co-expressing networks”. The method used (Weighted Gene Co-Expression Network Analysis) in the transcriptome of 92 tissues of bovine without any type of animal production data associated with them does not seem to be able to attempt to demonstrate the hypothesis. I suggest the authors to change the hypothesis and, maybe, provide a statement of need instead of a hypothesis, based on the fact that such large co-expression database is missing.
What provided in this paper is a co-expression dataset using transcripts. The transcripts are, in general, mature mRNA (or other types of RNA); thus, the coexpression analysis using the transcriptome somewhat disregards post-transcriptional regulations and, therefore, do not really reflect the real co-regulation at DNA level. I would like the authors to consider this point.
It is unclear to the reviewer why the authors had selected the genes with the highest variability between tissues considering that the purpose was to study co-expressed genes.
Experimental design: No comments
Validity of the findings: The authors did not provide any validation of their findings. Because they purpose was to find co-expressed genes I suggest to check if any of the networks detected present enrichment of up-stream regulators. If the genes are really co-expressed they should have commons up-stream regulators.
Additional comments: L119: unclear what is “degree”. Please, clarify
L134: unclear the word “mature”
L142: how the statistical analysis was run to identify differentially expressed genes?
L171: unclear the word “friends”
L210: the method used can aid in identify co-expressed genes but cannot really identify communication between genes. I suggest changing in “coexpression”
L290-292: unclear how the method used by the authors can characterize subcellular localization and complex formation of genes products.


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: CONSTRUCTING A COMPREHENSIVE GENE CO-EXPRESSION BASED INTERACTOME IN BOS TAURUS
Review round: 2
Reviewer: 1

Output:
Basic reporting: Acceptable
Experimental design: Acceptable
Validity of the findings: acceptable
Additional comments: This statement in the abstract “By using robust WGCNA (Weighted Gene Correlation Network Analysis), we described the gene co-expression network of 13,405 protein-coding genes from the cattle genome.” Is not correct given this statement “Using 19,064 genes with expression values, we ran a quality control step and removed those genes without expression values in more than half of 92 tissues. This provided a list of 13,405 genes with expression across 92 tissues. However, a large number of these genes were not differentially expressed between samples. Therefore, the data set with 13,405 gene expression was processed further by focusing on the 5,000 most variant genes (Table S1). The remaining 8,405 genes, which showed no or very low changes in expression between samples, were not used for WGCNA analysis.” In the materials and methods section. If I am understanding correctly, the network is for only 5000 genes.  If this is correct, the abstract needs to be corrected.

I am confused by this statement “However, a large number of these genes were not differentially expressed between samples”.  Based on the authors response, no differential gene expression analysis was conducted.  Given that how can this statement be made?