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: WOLF SPIDER BURROWS FROM A MODERN SALINE SANDFLAT IN CENTRAL ARGENTINA: MORPHOLOGY, TAPHONOMY AND CLUES FOR RECOGNITION OF FOSSIL EXAMPLES
Review round: 1
Reviewer: 3

Output:
Basic reporting: The work is a description of wolf spiders burrows morphologies linked with ecological and soil data. The purpose of the work is 1) to compare those descriptions of burrows with fossils records and 2) discuss the ecology of wolf spiders’burrows.
I like this work because of the serious literature revision about modern spiders’ burrow, the precision and variety of the data, the complete discussion. Information about ecology of the spiders’ burrow is very interesting. I feel a little bit frustrated as I thing this work may be improved if giving more data about fossils information (using previous works) mostly because it is presented as the first goal of the study and is finally spotted only in the discussion and ever not mentioned in material and methods. I suggest author explain how the will generate and discuss or compare the information about comparison for fossil information to have a better integration of this goal. However I thing that the work just need this adjustment to integrate better the goal about fossils identification, and that the work deserve to be published.
I recommend this publication.

Summary
-	Summary describe with clarity the observations, results and implications. I suggest at the beginning of the summary, add a sentence to introduce the further comparison with ichnogenera and understand in the beginning the focus of the work.
Introduction
-	The introduction present a very well description about modern spiders’ burrows architecture/form.
-	The introduction give well described information about wolf spider burrow in fossils records.
-	The purpose of the work in clearly exposed.
-	In the previous description of modern wolf spider burrows, authors give plenty and complete information about wolf spider burrow morphologies.

Material and methods
-	The site in where burrows where observed and spiders captured is well described.
-	The methodology for burrows descriptions is also well described.
-	I was looking for information about comparison between those burrows and fossils to have an idea of how authors will respond to the principal focus of the work as explained in the introduction. Please give in material and method information necessary to understand how this question will be answer. Even if this is not part of the field work.
Results
-	Line 180, the comment about rains looks important but what is the relation between rains and frequency of burrows entrance?
-	Description of sandflat sediment is well done.
-	The description of burrows is complete.
Discussion
-	Discussion in complete and well written.
Experimental design: Complete and easy to read. I particularly like the precision and the complete approach of the burrows descriptions.
Validity of the findings: The finding is interesting as it is a whole approach and description of wolf spiders burrows. Also this results may have great implication for fossils identification.
Additional comments: I like this work because of the serious literature revision about modern spiders’ burrow, the precision and variety of the data, the complete discussion. Information about ecology of the spiders’ burrow is very interesting. I feel a little bit frustrated as I thing this work may be improved if giving more data about fossils information (using previous works) mostly because it is presented as the first goal of the study and is finally spotted only in the discussion and ever not mentioned in material and methods. I suggest author explain how the will generate and discuss or compare the information about comparison for fossil information to have a better integration of this goal. However I thing that the work just need this adjustment to integrate better the goal about fossils identification, and that the work deserve to be published.


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

Input:
Title: RE-EMERGENCE OF THE LEAF CLIP GESTURE DURING AN ALPHA TAKEOVER AFFECTS VARIATION IN MALE CHIMPANZEE LOUD CALLS
Review round: 1
Reviewer: 1

Output:
Basic reporting: This describes the re-emergence of leaf-clipping, a behaviour previously described in this population in combination with pant-hoots, during a period of instability. The authors provide a detailed account of the re-emergence of the behaviour, its transmission, and the associated variations in acoustic parameters of the pant-hoots. The rarity of the events described in the paper make it interesting and valuable.

Given the focus on the combination of leaf-clipping and pant-hoot in a multimodal display, I think the introduction would benefit from including a brief review of the literature on multimodal communication in primates and other animals. This would help the reader to understand the aims and predictions.

Overall the paper is nicely written and complete. The figures and table are informative.
Experimental design: The design of the study is clear and straightforward. The research question is clearly defined and addresses a rare aspect of chimpanzee behaviour that has received little attention so far.

The methods used seem appropriate, but more details are required at times. Specifically, it would good to explain why separate models were built for each acoustic parameter measured rather than using factors of correlated measures, as the authors have done in the past (e.g. Kalan et al. 2015).

I also think that the analysis of the dominance hierarchy is not transparent enough. There aren't any details about how the rank of each individuals were obtained. I suggest the use of Elo-ratings (Neumann et al. 2011; R package: Neumann & Kulik, 2014), which is suitable for analyses of changes in short intervals and provides a quantitative measure of social stability.

I am not an expert in acoustic analyses, but they seem to have been conducted adequately.
Validity of the findings: The analyses seem appropriate, although the number of males in the group is small, appropriate measures have been taken to ensure the validity of the analyses. The conclusions are well stated, and although I am not totally convinced by some of the interpretations, they remain possible and the authors are cautious.
Additional comments: See annotated pdf for detailed 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: RE-EMERGENCE OF THE LEAF CLIP GESTURE DURING AN ALPHA TAKEOVER AFFECTS VARIATION IN MALE CHIMPANZEE LOUD CALLS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The authors documented the re-emergence of a gesture which had not been observed in this chimpanzee community for several years, and made use of this valuable opportunity to investigate how the acoustic properties of pant hoots (well-explored loud call of chimpanzees) might be altered when preceded by the leaf clipping gesture. Furthermore as this re-emergence accompanied an alpha take-over within the group, the authors recognised the importance of also investigating the effects of this instability (within the dominance hierarchy) on the acoustic parameters.

Collecting data during rare circumstances such as these is incredibly valuable in helping us to understand the possible conditions which may lead to the emergence of specific behaviours/signals. This is especially so for behaviours which are seen relatively rarely and appear to have different cultural variants – such as leaf clipping.

The manuscript is well-written, well-structured, easy to follow, with clear and professional language used throughout. Background literature on pant hoots and leaf clipping provided the necessary context to set up the hypothesis and predictions. Tables, figures, supplementary material and raw data are provided and appropriately referred to in the text. Table and figure headings/titles/axes are generally labelled with sufficient detail to enable the reader to understand the data displayed.

A few minor comments on basic reporting:

1)	I was surprised that the title does not include anything relating to instability in the hierarchy/the alpha take-over, as this is featured in the article in equal measure as leaf clipping
2)	Throughout I was sometimes confused as to which data came from the focal follows, and/or were collected ad libitum. On Table 1 it appears that aggression numbers are based on focal follow data – however leaf clipping and pant hoots were collected ad libitum (although there was also focal data available?). On line 349 and 382, you mention pant hoot rates – here it would be important to make sure to note that these rates are presumably derived from focal follow data only, or otherwise explain how these were calculated
3)	Similarly it would be useful to clarify whether ‘Number of aggressive interactions’ refers to instances when the individual was the aggressor OR victim (i.e. involved in any kind of aggressive interaction), or whether these were only the instances where the individual was the aggressor. Lines 259-260 would suggest the latter – this should be reiterated for the relevant tables (Table 1, Table S1), as otherwise this phrasing can be somewhat ambiguous/misleading
4)	I would be really interested to know how common leaf clipping was before the respiratory outbreak – and whether it was also mainly observed before pant hoots. Equally I was wondering whether this was the first alpha take-over since the outbreak, or whether there had been others which had not triggered the reappearance of leaf clipping. If you have this information available, even just from personal observation or communication, it would be nice to include to complete the picture a little more.
Experimental design: The research focus and predictions were clearly defined, and sufficiently backed up by relevant material covered in the Introduction. It is evident how this research addresses a gap in our existing knowledge of this behaviour. Observational focal follows, in addition to ad libitum data collection, and pant hoot acoustic recordings are a suitable means of addressing the research goals here.

The definition of ‘during’ alpha take-over is also very clear, and a good measure of when the instability among the males is likely be at its highest.

I have a few comments and suggestions for clarifications in terms of experimental design:

1)	More detail could be included on the specific method of calculating dominance ranks from pant grunts (e.g. lines 138-141). Also whether rank was assessed/calculated every few months, or continuously – as it seems that for most of the males the rank changed during the 11 month study period
2)	It would have been nice to take the behavioural context of the pant hoot into account as several of the studies cited have shown that context has an impact on acoustic properties such as fundamental frequency (e.g. Notman & Rendall, 2005; Fedurek, Zuberbuehler & Dahl, 2016) – hopefully future research can explore this.
3)	I was not aware that the climax phase could consist purely of drumming, with no vocal elements (lines 178-179) – it would be good to cite a relevant paper here where the climax has been defined like this before, or to provide a justification for defining it in this way.
Validity of the findings: The manuscript is very thorough in explaining how the acoustic parameters were extracted using Praat, and I found Figure 1 very useful in depicting this.

It is easy to understand that several acoustic variables were investigated as response variables (Table S2), and these have shown variability in the past – thus being appropriate when the aim is investigate variation in pant hoots. Equally the fixed effects are intuitive and directly addressing the hypothesis.

The statistical analysis is incredibly comprehensive, and the results are then also explained in more easy-to-digest terms – making clear what the main and most important findings were. Table 2 is especially handy in showing the contrasting effects of instability and leaf clipping on the response variables.

A few comments on the findings:

1)	The findings on leaf clipping are fascinating – however perhaps somewhere in the discussion it would be good to underline the fact that this gesture is nevertheless very rare (only seen 36 times in 11 months), and the vast majority of pant hoots are still produced without being preceded by this
2)	I am intrigued as to why Romario started leaf clipping at the point when he did (several months after the alpha and beta, line 287) – if you have any speculations as to why this might be then this could be an interesting point for the discussion
3)	It would be worth mentioning the potential role of social learning in the spread of this gesture (e.g. with reference to other gestures shown to have cultural variation and the possible influence of social learning in these – for example grooming hand clasp), especially if all males have now been observed to leaf clip (lines 433-435).
4)	I found the first sentence of the conclusion (lines 430-432) a little vague – I would rephrase ‘associated with an overall conspicuousness’, or simply state that several acoustic properties were significantly impacted by the occurrence of leaf clipping before the pant hoot, then going into specifics in the next sentence.
Additional comments: Additional minor comments:

-	Line 25-26: ‘leaf clipping… almost always preceded a pant hoot vocalisation’ – this might be better rephrased to something like ‘leaf clipping was observed almost exclusively immediately  prior to pant hoot vocalisations’ – as otherwise could be misread to be stating that almost all pant hoots were preceded by leaf clipping. This is a very minor comment – but something that threw me off on the first read.
-	Line 28: ‘affecting variation in loud calls’ – if space, I would say ‘ affecting variation in the acoustic properties of loud calls’
-	Lines 35-37: I think this sentence is less important and could potentially be cut – it is generally well-documented that pant hoot and aggression rates will be high during high male-male competition. Equally if leaf clipping typically occurs before pant hoots it is not surprising that it is more likely to be observed on days when there is a lot of pant hooting. This is also mentioned again on lines 367-368.
-	Lines 61-62: extensive list of primate studies, and then the next sentence covers primates again. Perhaps it would be possible to combine them – also because the term ‘primates’ is used before it is noted that ‘primate’ will be used to refer to NHPs.
-	Lines 112-115: could be explained more clearly why leaf clipping males were predicted to produce pant hoots with lower F0, longer duration etc.
-	Line 118: ‘a critical social context for signals associated with male loud calls to be modulated, including pant hoots’ – this seems a bit circular when reading, as male loud calls are pant hoots… maybe rephrase for clarity.
-	Line 140: I suggest modification ‘pant grunt is uniquely produced towards more dominant individuals’, or something similar which makes it clear that they would not be produced e.g. from alpha to beta (who is also a dominant individual)
-	Lines 165-166: at this point it has not yet been explained that you will only be looking at three (of the normally four) phases – this is only mentioned on lines 175-177. Maybe mention briefly or already explain fully here.
-	Lines 181-183: ‘as well as drumming’ – clarify here whether drumming is included or excluded for the durations. Could be re-written as ‘Durations were measured for the total pant hoot and for each of the three phases as well as the drumming bout, excluding any leaf clipping, if it occurred’.
-	Lines 187-188: I would think it would make more sense to describe which call was chosen in the event of an even number of calls.
-	Lines 284-285: I think this sentence is unnecessary – Table 1 shows that ‘after’ instability three of the males were leaf clipping (not all five), and these cases are already explained.
-	Line 340: be clear as to what is meant by ‘instability period’, and what this is being compared to.
-	Line 397: needs full stop instead of comma
-	Lines 407-410: explain more explicitly how it is relevant that another party is still in vocal reach. The previous sentences talk about leaf clipping being a potential attention grabber; however it is difficult to follow how this might still be the case over a longer distance.
-	Table 2: rephrase ‘full null model comparison’. Perhaps ‘full versus null model comparison’
-	Figure S1: X-axis might be more accurate as ‘Standardised male rank’


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: RE-EMERGENCE OF THE LEAF CLIP GESTURE DURING AN ALPHA TAKEOVER AFFECTS VARIATION IN MALE CHIMPANZEE LOUD CALLS
Review round: 1
Reviewer: 3

Output:
Basic reporting: Related to one of the major issues, the abstract indicates the mismatch between the information provided there and the conclusions of the manuscript.  In the abstract, the authors write “We suggest that elevated arousal and aggression during the alpha takeover triggered the re-emergence of leaf clipping and the associated acoustic changes in pant hoots.” In the main text, however, this issue is raised only in the final paragraph. Although it is claimed that arousal seems a less likely explanation, the sudden re-emergence of the leaf-clipping behavior, the more frequent and longer pant hoots along with the other changes of several acoustic parameters and the increased rates of buttress drumming seem to be closely related to the increased levels of arousal caused by the instability of the group. I am not suggesting that this might be the only explanation, but I think it is a very likely one and should be considered to a much greater extent than it currently is.

The second major issue is that the focus of this manuscript and the issue the authors really wanted to tackle did not become clear. The manuscript seems to meander around many different aspects of chimpanzees’ social behavior and their communication, but although the authors describe a precise research question, I found the way it is “framed” and derived from existing studies rather confusing. For example, although the title directs the readers’ attention to the re-emergence of the leaf-clipping, most of the introduction focusses on the vocal behavior of chimpanzees, with leaf-clips only mentioned for the first time in line 88. Furthermore, the authors introduce the source-filter theory and that based on this, “larger males are expected to produce lower pitched calls, which represent reliable cues of their body size and competitive strength”. Then they continue that for nonhuman primates, findings are rather inconsistent, with some studies showing that male quality is associated with low fundamental frequencies, while others found higher fundamental frequencies. At this point, I wondered whether this study aimed at contributing to this debate – which turned out not to be true. In other words – after reading the introduction, and even more so after reading the discussion (and conclusion!) of this article, I was simply not sure anymore what exactly the authors want to tackle. Was the aim to investigate whether the combination of pant hoots with the leaf-clipping display increases the quality of the males’ signaling and whether this influences their (future) position in the hierarchy? Or was the focus on the impact the males’ signaling might have on the audience, depending on whether pant hoots are produced in isolation compared to when they were produced in combination with leaf-clipping? Or alternatively, were the authors interested in whether preceding leaf-clippings modify the acoustic parameters of the following pant hoot? None of these questions was explicitly asked, but as the introduction covered many different aspects, not all of them relevant for answering the research question, it was difficult to understand the focus of the study.

Can you please specify a bit more what exactly defines “male quality”? You link this to body size and “competitive strength”, but what does the latter mean? Is this limited to physical strength and therefore the likelihood of winning a fight and/or becoming a high-ranking individual? In defining male quality, are other measures considered, such as the number of alliances/support from others or the number of offspring sired? For this study, I think this is not necessarily required, as these are most likely not measures that can be linked to acoustic parameters of pant hoots. However, how male quality is conceptualized in this study and what aspects it includes – and which not – is not fully clear.

Minor issues:
Leaf-clipping as a “socio-cultural trait”: This is already mentioned in the title and raises expectations which seem not really related to the aims of this study. I recommend not using the term “socio-cultural trait” as it is not related to any claims made by the study. The underlying mechanisms of how leaf-clipping is acquired and how it spreads across group members is (to my knowledge) not entirely clear. In this study, no claims are made in this regard, and the sudden re-emergence could be “merely” explained by the increased level of arousal. Therefore, linking leaf-clipping with this label does not contribute to explaining the current findings. If the authors want to use the term, I suggest rephrasing this a bit and to state clearly that other studies found leaf-clipping to be a socio-cultural gesture, while this cannot be concluded from the current study.

In general, I think the title might be somewhat misleading, as a large portion of this study was on the acoustic variation of pant hoots, and the relationships with leaf-clipping seemed to be a more secondary aspect.

Line 88: “Here, we documented the re-emergence of the leaf clipping gesture…”: This paragraph needs a somewhat smoother transition, as the previous paragraphs only introduced pant-hoots, so this sudden transition to leaf clipping comes as a kind of surprise. I suggest something along the lines “In addition to vocalizations like pant hoots, chimpanzees also use rich gestural repertoires. One type of gesture is the leaf-clipping signal, which re-emerged….” (or something similar)

Line 127: “The sub-adult males were included in the study once it became clear they held important rank positions in the chimpanzee hierarchy due to…” Can you please specify what “important rank positions” means? Does this exclusively refer to high rank positions?

Line 157: “Pant hoots were recorded while chimpanzees were feeding or arriving at feeding tree (n=42), resting (n=46), or traveling (n=124). For this analyses we did not distinguish between each of these contexts due to the lack of sample size per individual per category and because it was not directly related to our hypotheses.” You mentioned earlier that you were interested in how pant hoots change/are related to male-male competition. But these contexts (feeding/resting/traveling) are not related to male-male competition to any larger extent? Can you please explain why you think uttering pant hoots in such situations is somehow linked to competition/rank changes between males? Furthermore, please correct “this analyses” into “these analyses” or “this analysis”.

Line 69: “…‘pant hoot’, is acoustically sexually dimorphic…”: Does this mean they are structurally dimorphic or in terms of their usage (as the features that are mentioned seem to relate largely to the usage of such calls)?

Figures: The legend for Figure S1 seems to be missing?

Line 376: “Nevertheless, the results of Fedurek and colleagues (Fedurek, Zuberbühler & Dahl, 2016) who found rank related information encoded in pant hoots of another chimpanzee subspecies, strengthens our findings that pant hoots may contain some information relevant for male-male competition.” I found it difficult to accept this interpretation of your findings, given that rank seemed to have no effect on the patterns of changes found in the vocal behavior of chimpanzees. Can you please justify your conclusion in some more detail?

Line 391 “However, it is clear that leaf clipping before a pant hoot usually necessitates individuals to stop moving for a few seconds up to a minute (pers. obs.) before vocalizing which in itself could help to conserve some energy and rest the respiratory system right before producing the loud call and buttress drumming.” This aspect seems not really relevant for explaining the current findings?

Keywords: I suggest adding “chimpanzee” and removing “multimodal communication”

Line 173: “The pant hoots were visually separated into the introduction, build-up and climax phase that are well described and easily discernible (Marler & Hobbett, 1975; Mitani & Brandt, 1994; Crockford et al., 2004; Notman & Rendall, 2005) .” Please delete the space before “.”

Please check spelling of some references:
Barelli C., Mundry R., Heistermann M., Hammerschmidt K. 2013. Cues to androgens and quality in male gibbon Songs. PLOS ONE 8:e82748. DOI: please change Songs into songs

Fedurek P., Donnellan E., Slocombe KE. 2014. Social and ecological correlates of long-distance pant hoot calls in male chimpanzees. Behavioral ecology and sociobiology 68:1345–1355: please change Behavioral ecology and sociobiology into Behavioral Ecology and Sociobiology
Experimental design: Experimentally and in terms of analysis, I think this study has been conducted rigorously and to a high standard. Methods have been described clearly with great detail, and statistical analyses are conducted at a very high level. Therefore, I have only few comments/questions.

Line 206: “Before fitting models, the value for male rank was standardized to range from 0 to 1 to correct for the number of males in the group” But how did you take into account that the males’ ranks changed across the different phases of recordings (before, during, after rank changes)?

Furthermore, the observation periods were not really balanced regarding the total number of observational hours (237 hours before, 76 hours during, and 353 after the instability). Was this considered in the analysis?

How did you determine that rank changes were “completed” – only based on the direction of pant-grunts (with the previous alpha-male suddenly directing this vocalization towards the previous beta-male?)?
Validity of the findings: I have some remarks about the conclusions of this study:
Line: 396: “…by combining the gesture and pant hoot into a more complex multimodal signal.” I think it is important to not confuse a multimodal (or better: multi-component) signal wit sequences consisting of several signals of different modalities. Leaf-clipping followed by a pant hoot is not a multimodal signal, as both signals do not co-occur, but are separated by approx. 3 s (as described by the authors). This communicative pattern is better described as a sequential combination consisting of two signals of different modalities.

Lines 440-447: this comes rather out of the blue and I suggest deleting it, simply because this was not the focus of this paper and as I have mentioned already, this is not a multimodal signal. The observed communicative pattern does not resemble orofacial movements, as those are facial movements simultaneously combined with a vocal utterance. Therefore, this conclusion is way too far-stretched and does not follow from the data.

Is it possible to include that some information about the statistics for each of the 18 models? Also, although the raw data are provided, there is no code included (although I don’t know if this is required), so it is a bit difficult to understand how exactly analyses were conducted.

If I understand Figure 3 correctly, then the male Utan, who called most often and showed most aggression during rank instability, was the only male who was not effected by rank changes. Is there any explanation for this?
Additional comments: I have read this manuscript with great interest. It was very interesting to learn that leaf-clipping suddenly re-emerged in this chimpanzee population and that the vocalizing behavior of the males seemed to change somehow related to the changes in their rank hierarchies.

However, there are two major issues that need to be resolved, along with several more minor tasks. The two biggest problems are that first, the focus of this manuscript and the issues it is targeting are not really clear, as the introduction mentions several aspects not relevant for answering the question raised by the authors. Second, the conclusion that this observed pattern is the result of an increased arousal due to the instability of the group because of the rank changes seems much more plausible then it is currently presented  (as this is only mentioned in the very last paragraph). In my comments, I explain my concerns in some more detail. Most importantly, to improve this manuscript, I suggest first, re-structuring the introduction to tailor it more to the actual research question being asked; second, to put more emphasize on the explanation that the observed communicative patterns might be the result of increased levels of arousal at the time of observations, and third, to delete some of the distracting terms, such as "socio-cultural trait", or the link to orofacial movements/theories on language evolution, as they raise the wrong expectations and/or do not really follow from the current findings.


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: RE-EMERGENCE OF THE LEAF CLIP GESTURE DURING AN ALPHA TAKEOVER AFFECTS VARIATION IN MALE CHIMPANZEE LOUD CALLS
Review round: 2
Reviewer: 1

Output:
Basic reporting: I am satisfied the authors addressed the previous comments and points made on basic reporting.

Specifically the title now better reflects the topic of the article, with the alpha takeover being included. One further, small suggestion here would be to include ‘…affects variation in the acoustic properties of male chimpanzee loud calls’. However if you feel this makes the title too long (and only adds slightly to clarity), then please ignore.

Thank you for clarifying which data were collected through focal follows, and which ad libitum. It is helpful to have these separated in Tables 1 and 2. Including more details on leaf-clipping behavior in this group (and surrounding groups) before and after the study period gives the findings a little more context in terms of the types of conditions under which leaf-clipping emerges, and I think this has improved the flow of the ‘story’.

Some minor points on basic reporting on the new version of the manuscript:

I’m glad to see you have changed the transition between paragraphs on lines 88-89, however I wonder if it could be smoother by starting the next paragraph (line 89), with something along the lines of ‘As well as buttress drumming, several other gestural signals have been observed to be produced in conjunction with chimpanzee pant hoots. In the Tai forest in Cote d’Ivoire, the chimpanzees will occasionally ‘leaf-clip’…’ (or something similar to what Reviewer 3 had previously proposed).

Line 102 could be read to suggest that signals with limited temporal overlap are ‘free’ multimodal signals. Perhaps this sentence could be restructured to say ‘…example of multisensory communication in chimpanzees, also referred to as a ‘free’ multimodal signal (), albeit with limited temporal overlap between the two signals in this case.’

Lines 159-162 would be more clear if rephrased to ‘…before the start of a pant hoot. Soft, intermittent ‘hoos’… leaf clipped (Video S1), however only if these ‘hoos’ graded into the start of a pant hoot (<3s) were they considered part of the pant hoot.’

Line 272 – instead of saying ‘We tried to include behavioural activity…’, it might be better to say ‘We first included behavioural activity…led to model instability’
Experimental design: The continuous calculation of dominance ranks is now explained in greater detail, which is helpful for the reader.

I am happy with your justification of not including behavioural context in the models due to fear of destabilizing them too much, however I’m a little confused as to whether Table S1 and/or Table S2 include behavioural context. You mention in your response that Table S2 shows full null model comparisons including behavioural activity, and lines 198-199 explain why behavioural activity was not included, then saying, ‘but see Statistical Analyses and Table S1’. However I can’t seem to find anything in either table relating the activity as a control… though I think it might be that this is clarified in the table heading/descriptions(?), which I seem to be missing.

Thank you also for including a short paragraph on the reasons for including drumming as part of the climax phase. I expect some researchers may disagree that it is truly a part of the pant hoot itself, as opposed to a separate behavior that simply frequently co-occurs with pant hoots (such as swaying during the build-up, branch shaking etc.) but I think  this is reasonable, and useful for future researchers to take into consideration (/fuel debate).
Validity of the findings: The authors made changes in line with previous suggestions. I agree including the more detailed analysis on why Romario might have started leaf-clipping at the point at which he did would be unnecessary.

I still feel the first sentence of the conclusion could be stronger, as the summarised conclusion that leaf-clipping combined with pant hoots are associated with an overall conspicuousness of pant hoots is a little unclear as a take-home message. ‘Conspicuousness’ is quite vague, and not really mentioned in the rest of the manuscript. But perhaps changing this to ‘associated with increased conspicuousness…’ would at least give some indication of the direction? Or something more similar to the first line of the discussion.
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: RE-EMERGENCE OF THE LEAF CLIP GESTURE DURING AN ALPHA TAKEOVER AFFECTS VARIATION IN MALE CHIMPANZEE LOUD CALLS
Review round: 2
Reviewer: 2

Output:
Basic reporting: I have no new comments in this section, but want to refer to a previous comment:

MY ORIGINAL COMMENT: "Related to one of the major issues, the abstract indicates the mismatch between the information provided there and the conclusions of the manuscript. In the abstract, the authors write “We suggest that elevated arousal and aggression during the alpha takeover triggered the re-emergence of leaf clipping and the associated acoustic changes in pant hoots.” In the main text, however, this issue is raised only in the final paragraph. Although it is claimed that arousal seems a less likely explanation, the sudden re-emergence of the leaf-clipping behavior, the more frequent and longer pant hoots along with the other changes of several acoustic parameters and the increased rates of buttress drumming seem to be closely related to the increased levels of arousal caused by the instability of the group. I am not suggesting that this might be the only explanation, but I think it is a very likely one and should be considered to a much greater extent than it currently is."

THE AUTHORS' REPLY: "We understand the mismatch described by the reviewer. We have kept the sentence in the abstract as is and in the discussion we now present the arousal explanation earlier and before discussing other alternatives (2nd paragraph of Discussion). In addition to removing some aspects of the old discussion that were distracting, we hope the reviewer finds these changes agreeable."

MY NEW REPLY: I am afraid I am still not convinced by these changes, not content-wise, but in terms of the coherence of the results’ interpretation. Yes, the discussion now earlier refers to displacement behavior caused by stressful situations. However, you conclude that “…displacement behaviours in animals are usually more self-directed, such as scratching or self-grooming (Maestripieri et al., 1992), and this would not explain why leaf clipping was specifically coupled with pant hoots.”. Furthermore, in the final section of your discussion, you are still writing that it is “…difficult to assess how much of the acoustic variation observed in pant hoots preceded by leaf clipping can be attributed to greater arousal alone. However, according to Morton’s motivation structural rules (Morton, 1977) we do expect lower fundamental frequencies when animals signal aggressive intent which is supported by our results.” If I understand this correctly, you doubt that arousal is the main explanation for the re-emergence of leaf-clipping. However, in the abstract, you “…suggest that elevated arousal and aggression during the alpha takeover triggered the re-emergence of leaf clipping and the associated acoustic changes in pant hoots.” So, I hope I do not understand this incorrectly, but I cannot see a coherent line of argumentation regarding the contribution of arousal for your observed behaviors.
Experimental design: I have comments.
Validity of the findings: I have comments.
Additional comments: This manuscript has been properly revised and the reviewers' comments have been considered/incorporated thoroughly.

Apart from my comment in the "Basic reporting" section, I have no additional comments, apart from some minor issues:

Some typos:
- lines 72, 83: please add commas after )
- line 264: please remove  space after )
- Line 283: insert space after ).


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

Input:
Title: THE ANTIMICROBIAL ACTION OF POLYANILINE INVOLVES PRODUCTION OF OXIDATIVE STRESS WHILE FUNCTIONALISATION OF POLYANILINE INTRODUCES ADDITIONAL MECHANISMS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript is well prepared. Literature are actual and relevant. Figures have adequate quality.
Experimental design: Experimental design as well as used methods are relevant.
Validity of the findings: The novelty of the results are high. Conclusions are based on the results.
Additional comments: Manuscript „The antimicrobial action of polyaniline involves production of oxidative stress while functionalization of polyaniline introduces additional mechanisms“ focused on highly discussed topic regarding the biological properties of polyaniline. The study is well designed and all used methods are relevant. The manuscript provide new results which can significantly contribute to our understanding of antibacterial effect of PANI. The conclusions are based on gained results. I have only one minor suggestion: the results show the PANI activity is connected to the production of ROS. It could be interesting to discuss this more even in context to the previously found impact of PANI on eukaryotic cells (e.g. http://dx.doi.org/10.1016/j.colsurfb.2014.01.027). I have no substantial concerns about this manuscript and therefore I do recommend it for publication in its present form.


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

Input:
Title: THE ANTIMICROBIAL ACTION OF POLYANILINE INVOLVES PRODUCTION OF OXIDATIVE STRESS WHILE FUNCTIONALISATION OF POLYANILINE INTRODUCES ADDITIONAL MECHANISMS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript describes the antibacterial activity of polyaniline (PANI) and and a homopolymer of poly(3-aminobenzoic acid). Activity on single gene deletion mutants was used to demonstrate that these two molecules have different effects on E. coli cells. The introduction provides sufficient back ground information and the use of English is clear and professional. There are a few points that need to be addressed. One of the major issues is that there is a lot of discussion included in the results, for example the discussion of bedaquiline.  This makes the results section difficult to follow. If two separate sections are going to be provided they need to be separate. Additional point that need clarification are below
Line 325. It is unclear what the statement that “the E. coli deletion mutants were more affected” means. Was the phenotype more pronounced? Were more strains affected?
Line 330-365. The detailed discussion of each strain is unnecessary. This was not done for the strains with altered sensitivity in the other experiments and should be summarized similarly.
Line 367. The results of the mutant screening indicate that PANI likely induces an increase in free iron but the results from P3ABA in minimal media indicate that the cells are likely undergoing iron starvation.
Line 402. Product needs to be changed to production
Line 427. It would support the claims if the values were included in the text. This applies throughout the paper.
Line 429-434. Is this the same statement twice or are these supposed to provide different comparisons. Either way the meaning of these statements needs to be clarified.

The results section describing the activity of PANI and P3ABA in aerobic vs anaerobic conditions is very hard to follow. This section would benefit from a more focused approach to drive home the point the authors are trying to highlight from this data. Alternatively this could be separated into multiple sub sections to make the conclusions more clear.
Experimental design: The methods are for the most part well described and appropriate for each experiment. However I do have some concerns about the rationale for certain experiments.
Line 122. It would be helpful to include a brief statement on the rationale used to select the deletion mutants. Why not include some with deletions in other cellular functions as controls?
Line 292. Again how was this subset selected?
Table 1. The authors should provide the data used to determine the sensitivity of each strain as opposed to merely stating less or more sensitive. This needs to include statistical analysis.
Why were the EPR experiments only done in LB?
There are a lot of claims made about the induction of ROS using indirect evidence. Detecting ROS in cells is a relatively simple experiment to do using probes such as DHR123 or DCFDA. Is there a reason these experiments have not been included?
Figure 4. The data is presented in a very confusing way. It would be helpful to change the y axis to log2 of the fold change in MBC or something similar
Validity of the findings: The findings described in this manuscript suffer from a lack of focus in their description. In the introduction a simple question was posed on the difference in the mechanism of two antimicrobials. There is a lot of unnecessary information in the results section which makes it difficult to follow. There are also some comparisons that take away from the initial question posed. A reorganisation of the results and discussion may help with the inclusion of more headings that highlight the key finding similar to the section “P3ABA treatment causes an increase in free iron in E. coli”. Some specific concerns are listed below.

Line 391. The EPR data that shows the increase in free iron in P3ABA treated cells contradicts the statement in line 314-315 where the authors found no change in sensitivity to P3ABA in strains with deletions in genes related to iron homeostasis. This needs to be explained

The authors need to acknowledge that only screening a small subset of deletion strains biases their results. It is possible that there are other mechanisms at play that have been missed due to the strains selected. This is particularly evident in the lack of altered sensitivity of any strain to PANI in minimal media. There must be another mechanism at play that could also be contributing in rich media. Similarly there are only two strains with altered sensitivity to P3ABA in LB.

The conclusion statement over simplifies the findings of the paper. The mechanisms described for PANI is the one identified in LB whereas the one for P3ABA is the one for minimal media.
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: THE ANTIMICROBIAL ACTION OF POLYANILINE INVOLVES PRODUCTION OF OXIDATIVE STRESS WHILE FUNCTIONALISATION OF POLYANILINE INTRODUCES ADDITIONAL MECHANISMS
Review round: 1
Reviewer: 3

Output:
Basic reporting: Roberson and colleagues perfomed studies to determine the mechanism of action of the novel antimicrobial agents polyaniline (PANI) and functionalised polyanilines (fPANI). Their work shows that PANI antimicrobial activity is due to hydrogen peroxide production and consequent oxidative damage, while P3ABA (fPANI) targets ATP synthase, disrupting respiration and metabolic processes.

I commend the authors for their extensive data set (including the raw data file). The manuscript is well written, with detailed methods and a good state of the art introduction.
If there is a weakness, it is in the lack of independent replicates for some experimental procedures, which should be improved upon before Acceptance.
Experimental design: Materials and Methods section was well written and detailed.

1. In general, some of the methodology was not performed in 3 independent experiments, which weakens the work. For example, the EPR iron determination was assessed only once (n =1) with 2 biological replicates.
2. A statistical analysis paragraph compiling all analysis made for the entire methodology would help the reader following the materials and methods section.
Validity of the findings: 1. The initial screening of the mutant’s Keio library was very helpful to pinpoint the most plausible mechanisms behind the PANI and P3ABA mode of action. However, I had trouble understanding the results in Table 1. It was very confusing because there are a lot of bank spaces (which I supposed meant there was no difference compared with the parental strain). The data set could have a better visual aid by using a column plot for example.
Have the authors tested whether each mutant strain has growth defects in both media, without any treatment?

2. Free iron determination by EPR is lacking independent replication of the data (Figure 2), with only one experiment performed (n=1). This strongly makes me question this result. I would encourage repeating again to get (at least) an n = 2 independent replicates.

3. Again, in Figure 3, no information about n, SD (standard deviation) and statistic analysis made (I presume the Mann-Whitney is the non-parametric Mann-Whitney U-test but this should be in the statistic analysis in the materials and methods).

In general, the findings are well supported by the data presented in figures and in the supplemental materials.
Additional comments: In general, figure captions were lacking important information regarding the data set (e.g. statistical analysis, n number, standard deviation, concentration of treatments).

line 470 – bedaquiline is mentioned for the first time and the authors only explain what it is later in line 483.

line 774 – The overall conclusion that P3ABA may cause PMF collapse, when no experimental data investigating membrane damage and deregulation of murein hydrolases, is too bold of claim.

The authors’ recently published work (Robertson J, Gizdavic-Nikolaidis M, Swift S. Investigation of Polyaniline and a Functionalised Derivative as Antimicrobial Additives to Create Contamination Resistant Surfaces. Materials. 2018;11(3):436. doi:10.3390/ma11030436) should be cited in this manuscript since it has relevant data on another tested bacteria species (Staphylococcus aureus) which further demonstrates the antimicrobial effectiveness of these compounds against not only E. coli but also S. aureus, in addition to tests for surface application.


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: TRIPLE STABLE ISOTOPE ANALYSIS TO ESTIMATE THE DIET OF THE VELVET SCOTER (MELANITTA FUSCA) IN THE BALTIC SEA
Review round: 1
Reviewer: 1

Output:
Basic reporting: The article is written in good, professional English but a further revision by a native speaker would be desirable.

Literature references and sufficient field background/context are provided.
A professional article structure is provided.  Raw data are shared.

Figures are relevant to the content of the article, but figure and table legends are missing.

Self-contained with relevant results.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: A useful and well designed study. Can you add a figure comparing the results of the two methods (e.g. pie chart)?


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: TRIPLE STABLE ISOTOPE ANALYSIS TO ESTIMATE THE DIET OF THE VELVET SCOTER (MELANITTA FUSCA) IN THE BALTIC SEA
Review round: 1
Reviewer: 2

Output:
Basic reporting: 1. Grammatical errors are present throughout the manuscript and the manuscript would require close editing by a fluent English speaker prior to it being suitable for publication.

2. Please increase the amount of information included in Figure and Table legends. Both should have sufficient information to make the Figure or Table interpretable and understandable without reference back to the text. So all species names, abbreviations and units should be clearly described.
Experimental design: 1.	Spatial information is central to many isotope studies and is often the key to understanding why animals show the isotope values they do. I raise this point because the isopod crustaceans were sampled c. 40km from the ducks and other prey and were also quite a bit deeper (c. 35m vs 15-20m; Figure 1). Differences of 15-20m can potentially have a strong influence on C and N isotope values. Were there no isopods to be sampled near the ducks? Presumably not, but the authors need to be explicit about the fact that the spatial offset of the different prey is a potential source of variability in their results.
Validity of the findings: 1.	Consistency in sample preparation is key for most stable isotope applications. In this case, the blood of the ducks was freeze-dried but the invertebrates were dried in a conventional oven. There is literature that suggests freeze drying and oven drying can yield different N isotope values for the same organism/tissue (Carabel et al. 2006). Using different methods on predators vs prey could pose yet another potential source of variability that must be addressed, and if not corrected for, at the very least described and considered. It is incumbent on the authors to defend the use of different preservation techniques either by reanalyzing a subset of samples to verify there is no difference, going to the relevant literature and finding suitable mathematical conversions if they exist, or finding previous studies that support their current approach.

2.	The use of the Caut et al. approach to estimating prey-specific TEF values is not widely accepted. Perga and Grey (2010) provide convincing counter arguments against the blind use of a variable TEF without specific knowledge of the predator-prey fractionation dynamics. I think most readers would question the application of the approach here, or at the very least, want to see what effect using the Caut et al. model had on the final outcome. Did it alter the number of scoter retained from the mixing model polygon analysis? To what extent did it change the estimated dietary proportions from the different prey groups using SIAR? I would suggest that the apparent dearth of information on velvet scoter TEFs would suggest a more conservative approach based on a single, common TEF appropriate for avian blood (such values are documented in numerous waterbird-specific studies as well as several meta-analyses on the subject). If the authors feel strongly that the Caut et al. variable TEF model is the most appropriate, then I would strongly suggest running the analysis again with a single generic TEF, and describing the differences (or better, providing the results as supplemental material) so that readers are aware of how this approach influenced the findings reported in the paper. I also think that there needs to be an acknowledgement that this approach is controversial and a statement given as to why the authors feel the approach is justified here.
Additional comments: I want to encourage the authors to pursue this work, particularly the approach of using three isotopes and multiple statistical 'checks and balances' to study the trophic ecology of this duck species. Coupling the isotope work with the diet analysis is powerful and a strong component of this study.


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

Input:
Title: TRIPLE STABLE ISOTOPE ANALYSIS TO ESTIMATE THE DIET OF THE VELVET SCOTER (MELANITTA FUSCA) IN THE BALTIC SEA
Review round: 1
Reviewer: 3

Output:
Basic reporting: This is an interesting paper and one of few that have explored the use of stable-sulfur isotope measurements in seaducks to infer dietary patterns. In general, the reporting is clear and straightforward but there are several cases where the English can be improved and the manuscript would benefit from editing by a native English speaker. Nonetheless, the writing is still perfectly intelligible and unambiguous.
The literature cited is generally relevant but the reliance on the Caut et al. approach to assigning TEF values could have benefitted from reporting of derived blood TEF values for species with similar ecology(Canvasback: Haramis et al. Auk 118:1008-1017;King Eiders: Opel and Powell J of Ornithol. 151:123-131; Spectacled Eiders: Federer et al. Cdn J, Zool 88:866-874; see also the paper by Lovorn et al on isotopes in eiders in the Chuckchi Sea, Progress in Oceaography 136:162-174).
The table and figures are appropriate although I did expect to see the Siar or MixSiar output probability distributions for each of the relevant dietary inputs.
There were no significant hypotheses stated as this was largely an exploratory study.
Experimental design: The paper presents the results of original research in keeping with the aims of the journal.
The research question is extremely straightforward (namely use a 3 isotope mixing model to estimate dietary inputs to scoters). Moreover, justification for the study was clearly the extreme population decline of the species in these waters.
The authors generally followed a well defined protocol of applying the SIAR model. This requires estimates of TEF, isotopically distinct dietary endpoints etc. I think the presentation could have been improved by applying variance estimates about the TEF values (if done, I did not detect that). That would have made better use of the Bayesian approach to propagating error. As stated above,the TEF estimates were adopted rather uncritically and the specific diving duck work done in captivity needs to be considered or at least presented to see how well they fit the Caut estimate (for the carbon and nitrogen isotopes, I agree that an assumption of no TEF for sulfur seems appropriate). On a similar note, the authors need to quote the credibility intervals for their predictions throughout (not just the means). Stable isotope methods reveal that largely inorganic standards were used in the lab and this is frowned upon when measuring organic materials (principle of like materials), although I doubt if this will influence the results. Would have been nice to ground truth the Post lipid correction algorithm by simply running a few samples with lipids actually removed. I have much less faith in the C:N correction approach.
Validity of the findings: The findings seem to confirm other, non-isotopic, data regarding scoter diet.
Unfortunately, the sample size for the live-caught birds is extremely low and it is just not clear how well this study represents the bulk of wintering birds. On that note, I was surprised to determine that the authors did not make use of the dead scoters from the bycatch. Presumably, their muscle and liver tissue would have been excellent for dietary reconstruction using stable isotopes. In addition to presenting results of the stomach content analyses, SIAR and, more currently MixSiar could readily use those data as a Bayesian prior in the diet estimate analyses.Not at all sure why the authors did not do that.

Overall, the paper could have ended with a stronger concluding statement regarding the importance of these findings. How exactly are such findings relevant to deciphering the declines of scoters in this area?
Additional comments: This is a nice study. I do recommend that you use the MixSiar package and provide the output that shows the probability distributions of various dietary inputs. It would also be instructive to see how the estimates change when using the Bayesian prior based on the gut contents analysis. Do bring the paper up-to-speed by including directly the isotope studies done to date on diving ducks (mostly in the North American literature).


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: TRIPLE STABLE ISOTOPE ANALYSIS TO ESTIMATE THE DIET OF THE VELVET SCOTER (MELANITTA FUSCA) IN THE BALTIC SEA
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors have sufficiently addressed all concerns.
Experimental design: The authors have sufficiently addressed all concerns.
Validity of the findings: The authors have sufficiently addressed all concerns.
Additional comments: Thank you for your obvious efforts in responding to the reviewers' 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: TWO SUGAR BEET CHITINASE GENES, BVSP2 AND BVSE2, ANALYSED WITH SNP AMPLIFLUOR-LIKE MARKERS, ARE HIGHLY EXPRESSED AFTER FUSARIUM ROOT ROT INOCULATIONS AND FIELD SUSCEPTIBILITY TRIAL
Review round: 1
Reviewer: 1

Output:
Basic reporting: The article is devoted to the urgent problem of search and identification of candidate genes participating in the reaction to biotic stress forms. As an object, the important food crop, sugar beet is used, and the pathogen is the fungus Fusarium, which causes a widespread disease of roots. It was previously shown that chitinase genes are one of the first to be included in response to the plant pathogens. The authors set a reasonable task to identify the association between certain isoforms of these genes and both resistant and fusarium-sensitive plant forms, and also to analyze the gene expression in response to specific fungal strains most common in Kazakhstan.
The article is nicely written in English, all terms are correctly used. It includes sufficient introduction with complete and clear review the scientific problem under study. However, some paragraphs can be rearranged. Since it starts with description of Fusarium pathogen, so paragraphs under lines 98 and 132 (which disrupt the description of chitinases) can be combined with the corresponding part of Introduction.
The structure of the article agrees with appropriate form. Figures are relevant to the content of the article and have sufficient resolution, except Fig.2 where numbers at X- and Y-axes look very small.
Minor remark. Line 334- amino acid substitution should be indicated for non-synonymous case.
More serious comment. One of the main tasks of this study is identification of genes and their markers suitable for the selection of plants most resistant to the pathogen. However, in my opinion, the part devoted to SNP-targeting of alleles looks separate from the analysis of expression and phenotyping. There should be some clarification, is there association between the SNPs found and resistance to Fusarium, or they are neutral? There is a  phrase  in conclusion: “A strong association with two SNP Amplifluor-like markers with BvSP2 and BvSE2 was found in our study”. But any other SNP may serve as a marker of these genes, but not a marker for resistant forms. You found rise of expression of these genes, but could you discriminate between different plant forms using your markers? Explain, please.
Experimental design: Original research is within Aims and Scope of the journal. Experimental design agrees well with the proposed tasks and the study contributes to resolve these tasks.
Validity of the findings: Data is robust, statistically sound and controlled. Conclusion is well stated, linked to original research question and limited to supporting results.
Additional comments: As a whole, the article is ready for publication after a minor editing will be done.


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: TWO SUGAR BEET CHITINASE GENES, BVSP2 AND BVSE2, ANALYSED WITH SNP AMPLIFLUOR-LIKE MARKERS, ARE HIGHLY EXPRESSED AFTER FUSARIUM ROOT ROT INOCULATIONS AND FIELD SUSCEPTIBILITY TRIAL
Review round: 1
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: The manuscript represents the original research devoted to the determination of the role of BvSP2 and BvSE2 genes in resistance of sugar beet to Fusarium root rot. The association of sugar beet resistance with SNPs and expression of the genes has been shown. In general, the manuscript is well structured and written in a professional way, the references are sufficient and the figures are clear. The results were obtained with the use of representative sample sets and rigorous techniques and correctly interpreted. However, there are several issues that should be addressed:

1) Figure 3A – Why there are asterisks only over 2210 line? Hundred-fold expression increase in 2182, 2236, and KWS2320 lines is not statistically significant? Also, it is better to present Y-axis in logarithmic scale, it is impossible to understand what values are shown slight above 0.
2) Table 1 – Strange upper row – “A” and “B”, it can be concluded that genotyping for BvSP2 gene was performed only for laboratory-grown plants and that for BvSE2 gene – only for field-grown plants. Is it correct? Please, correct or explain. Why are “R”, “In”, and “S” abbreviations presented in columns 3 and 5 “Genotyping”? Please, correct or explain.
3) Lines 358-359 – “All genotypes of KWS2320 plants fell into the homozygote class a1a1 (Fig. 2).” I cannot find any mention on KWS2320 neither in Figure 2 nor in Figure 2 legend. Please, correct or explain.
4) Lines 296-297 – “Probabilities for significance, P<0.95 and P<0.99, were calculated using Student’s t-test.” This looks strange for me, what do you mean?
5) Line 279 – R2 value has the relation to correlation coefficient, but it is not correlation coefficient. Please, correct.
6) qPCR is used as synonym to real-time PCR, while qRT-PCR is used to abbreviate quantitative reverse transcription PCR. It should be corrected where applicable. Also, the correct name of Bio-Rad CFX96 device is “Real-Time PCR System” not “Real-Time qPCR System”. Please, correct.
7) Lines 335-336 – “the SNP [Y = C/T] was non-synonymous” The SNP is synonymous. Please, correct.
8) Line 261 – “ThermoFisher, Almaty, Kazakhstan”. Is it correct?
9) Lines 515-516 Strange conclusion on association of SNP markers with genes. Did you mean the association of genotype with the resistance to root rot?

I recommend to publish the manuscript after minor revision.


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

Input:
Title: TWO SUGAR BEET CHITINASE GENES, BVSP2 AND BVSE2, ANALYSED WITH SNP AMPLIFLUOR-LIKE MARKERS, ARE HIGHLY EXPRESSED AFTER FUSARIUM ROOT ROT INOCULATIONS AND FIELD SUSCEPTIBILITY TRIAL
Review round: 2
Reviewer: 1

Output:
Basic reporting: ok
Experimental design: ok
Validity of the findings: ok
Additional comments: I'm completely satisfied with the author's answer.


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: TWO SUGAR BEET CHITINASE GENES, BVSP2 AND BVSE2, ANALYSED WITH SNP AMPLIFLUOR-LIKE MARKERS, ARE HIGHLY EXPRESSED AFTER FUSARIUM ROOT ROT INOCULATIONS AND FIELD SUSCEPTIBILITY TRIAL
Review round: 2
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: The authors have addressed all the comments. I recommend to accept the manuscript for publication in PeerJ.


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

Input:
Title: THE EFFECT OF BIOCHAR AMENDMENTS ON PHENANTHRENE SORPTION, DESORPTION AND MINERALISATION IN DIFFERENT SOILS
Review round: 1
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: After reading, the manuscript entitled " The effect of biochar amendments on phenanthrene sorption, desorption and mineralisation in different soils ", I think the paper should be accepted as it. The topic is interesting for the scientific community and for the industry and it falls in the journal scope.
I think the work is quite novelty because of the biochar uses. The biochar is a form of charcoal obtained from wastes that it is being used as soil amendment. Despite of the thermic stabilization, the biochar is a material quite heterogeneous, strongly related to the type of the initial material used and pyrolysis conditions. Due to these characteristics, the studies under controlled conditions can provide information to understand and predict the biochar effect on soil properties and xenobiotic behaviour. The objective of this paper is to study the potential effect of biochar produced from three different feedstocks on phenanthrene (Phe) sorption/desorption properties and on its mineralisation. The experiment is performed according a classical design. This methodology is easily reproducible in laboratory conditions and allows to compare the results obtained from experiments made with other biochars and soils to evaluate the Phe sorption/desorption; but also, to compare results to evaluate the mobility of other organic xenobiotics with both soil and biochars studied in this experiment, but in different labs. The mobility of the organic xenobiotics from soils to the underground waters are controlled by the adsorption-desorption mechanism according to Freundlich isotherms. Finally, the use of 14C-labelled Phe to evaluate the mineralization provides precise information about the C mineralisation. In brief, the authors have presented a robust and classical model to describe the Phe mobilization in two soils and one sand amended with three different biochars. Both soils and biochars have been fully characterised according to routine lab protocols. The methodology is accurate to get the objectives proposed by the authors under lab conditions proposed. Soils, sand and biochars have not been sterilized, in principle, the role of the autogenous microorganism has not been quantified, the presence of controls can minimize the error. Results cannot be reliable to field conditions. However, the results can support the work hypothesis and the final conclusions in which as each biochar behaved slightly differently between soils, soil-biochar interactions should be considered in future research and caution is needed when extrapolating to other soils.


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

Input:
Title: THE EFFECT OF BIOCHAR AMENDMENTS ON PHENANTHRENE SORPTION, DESORPTION AND MINERALISATION IN DIFFERENT SOILS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript is written in clear English, at times the wording is slightly misleading and could be improved (e.g. lines 335-336, the use of “sorption capacity” when this parameter was not measured or calculated, for helpful insights into discussion of sorption data see e.g. https://doi.org/10.1016/j.watres.2017.04.014). Figures are relevant to the content and appropriately labeled. Unfortunately, during the introduction, as well as during the discussion of the results the authors neglect a portion of  previous work on PAH sorption and degradation in the presence of biochar. For example, the fact that desorption from biochar is a rate limiting step for PAH degradation in biochar amended soils has previously been reported but was not discussed in the introduction and not used for the identification of knowledge gaps (e.g. http://dx.doi.org/10.1016/j.envpol.2013.06.026 and https://doi.org/10.1016/j.jhazmat.2017.11.010). Thus, it remains unclear to the reader what is already known, and how this study contributes to the field (see below for some suggestions). Accordingly, the sections at times appear to be less connected to the research aim than they could be and could be more focused on results relevant to the research aim(s).
Experimental design: The aim of the study is clearly stated, however, based on previous literature the authors could expect that phenanthrene sorption will depend on biochar type and soil properties. The data which were obtained fulfill high technical standards and surely have the potential to go beyond these expectable findings.

 Thus, more attention should be given to the identification of existing knowledge gaps in the field, which could be useful to reshape the discussion and conclusion section of the manuscript. The results sections should be organized accordingly to better lead towards the answering of the previously identified knowledge gaps (currently for the first two sections this is not the case). The general aim of the first two sections could be to provide a more detailed mechanistic discussion on biochar-soil interactions with a special focus on the differences between soils and biochars to subsequently help to explain the effect of soil type and biochar type on the sorption and degradation of phenanthrene.
The discussion of Freundlich fits, especially differences in observed sorption nonlinearity (n) could be further elaborated in regards to sorption interactions and the effects of soil fractions on sorption to biochar. At the end of the sorption section the authors indicate that pH may have affected sorption of phenanthrene, but fail to explain why a neutral hydrophobic contaminant would sorb differently in dependence of soil pH.
The data presented in the phenanthrene mineralization section are very interesting and may offer more insight than is presented. For instance, the authors could look into the possible facilitation of abiotic phenanthrene transformation by biochar in the sand- biochar system to explain the different trend compared to soil systems. The section “integrative comments” is very helpful for the discussions of both sorption and mineralization measurements and the authors may consider to merge the two paragraphs with the respective previous sections. The concluding remarks could be sharpened in regards to key findings and how this study may be useful for further research in the field.
Validity of the findings: The data is robust, statistically sound and the key findings are valid with few remarks that need to be addressed (e.g. see comment on the effect of pH on phenanthrene sorption). The conclusion section should be sharpened towards the key findings and the meaning of these findings for the larger field.
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: THE EFFECT OF BIOCHAR AMENDMENTS ON PHENANTHRENE SORPTION, DESORPTION AND MINERALISATION IN DIFFERENT SOILS
Review round: 1
Reviewer: 3

Output:
Basic reporting: This is an interesting paper that studied Phenanthrene sorption in biochar-amended soil. The results can be very valuable for people to understand the effect of biochar amendments on phenanthrene sorption, desorption and mineralisation in soil. The paper is well organized and largely written in proper English.

The authors wrote a long introduction, however, the significance and the innovation were not well presented. Great efforts should be done to improve it.

About Materials and methods, I have a question: What guideline or method did the authors used for performed Phenanthrene sorption experiment?
And  I have a suggestion: Please, add the reference for the Phenanthrene mineralisation experiment.
Experimental design: This paper presents all the necessary requirements for the experimental design.
Validity of the findings: In think that this paper presents all the necessary requirements for the validity of the findings.
Additional comments: This is an interesting paper that studied Phenanthrene sorption in biochar-amended soil. The results can be very valuable for people to understand the effect of biochar amendments on phenanthrene sorption, desorption and mineralisation in soil


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

Input:
Title: THE EFFECT OF BIOCHAR AMENDMENTS ON PHENANTHRENE SORPTION, DESORPTION AND MINERALISATION IN DIFFERENT SOILS
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: please see attachement


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: METHODS MATTER: THE RELATIONSHIP BETWEEN STRENGTH AND HYPERTROPHY DEPENDS ON METHODS OF MEASUREMENT AND ANALYSIS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The paper is well written and follows a clear structure. Relevant literature is referred to with few relevant omissions. The author's clearly present their research question, and how it differs to those of previous investigations, and then offer a clear hypothesis for which the results specifically relate to.Relating to the basic reporting and writing of the manuscript I have only a few suggestions below in the General comments section.
Experimental design: The authors should be commended for the sharing of their analysis code alongside their data permitting others to replicate their study. There are some elements that I believe may need clarification in the methods.

1) Can you provide more detail on the CSA measures taken. I can imagine that taking clear biceps brachii CSA measures with ultrasound is difficult without a sufficiently wide linear probe and even then I often find that overlap with the contours of the surface of the upper limb means that contact with the probe can be lost. Was a panoramic image taken? I have checked the original manuscript and the details reported are the same? Further information would be appreciated.

2) Where any measures of the reliability of between day ultrasound measures determined?

3) How have you interpreted your statistical analysis? e.g. for correlations what was considered, weak, moderate, strong etc.
Validity of the findings: Results are presented clearly. Conclusions are stated clearly and relate to the original research question and hypothesis.
Additional comments: I think the authors should note and discuss the concerns of other authors around study design in determining 'cause and effect' relationships, as opposed to merely identify whether two things are related. The study of Mattocks et al.is discussed, but other papers highlighting and discussing this have not been referred to e.g. https://www.ncbi.nlm.nih.gov/pubmed/28819744

Line 53 - replace the comma after "...not limited to..." with a semi-colon.

Line 130 - change use of the term 'intensity' to 'load'

Line 208 - Add 'relationship' after 'strength-hypertrophy'

Lines 279-281 - I would be careful with statements such as this. The emergence of traits from an evolutionary perspective is determined by their 'net' effect on reproduction. Traits can emerge despite them having associated costs as long as their effect is a net positive upon reproductive success. These are often referred to as being 'costly' traits.

Line 295 - Although I agree with the statement that the time-course of adaptations likely varies between individuals, I'm not sure that the Churchward-Venne et al. paper supports this. There is not to my recollection data presented on an individual basis for any thing more than two time points - either 0 and 12wks, or 0 and 24wks.

Line 297 - I would suggest changing 'ensuring' to "...thus meaning that there is a greater chance that measurement error exceeded..."


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: METHODS MATTER: THE RELATIONSHIP BETWEEN STRENGTH AND HYPERTROPHY DEPENDS ON METHODS OF MEASUREMENT AND ANALYSIS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The Basic reporting of the manuscript was at a high standard, with appropriate references cited and the level of English professional and concise throughout.
Experimental design: I was impressed with most aspects of the experimental design; with these sections well described throughout.
Validity of the findings: The data presented in this manuscript is robust and clearly presents how a variety of data collection/analysis and/or statistical approaches can result in quite substantial differences in the results and ultimately the clinical interpretations of these results. Such findings have massive potential to influence our understanding of the relationship between hypertrophy and strength as well as the way that future researchers will need to examine this relationship in future studies.
Additional comments: General comments
This manuscript outlines a very well described rationale for how exercise and sport science researchers need to perhaps rethink our approaches to modelling the relationship between muscle mass and strength, be it in cross-sectional or training studies. I’m impressed with many aspects of this manuscript including the overall research question they sought to examine, the methods chosen to address this question and the way the manuscript is presented. A few small ways in which the manuscript can be improved are included below in the specific comments section.

Specific comments
line 45 – 46: please feel a bit more explicit and provide some examples of what some of these inter-individual differences may be.
Line 257: I think this sentence would be better written as “of the changes in these parameters did not correlate significantly over a training period”.
Line 271 – 273: you appear to have made a convincing argument for the importance of measuring PCSA, however this is not easily measured by most researchers and practitioners. Is there any possible way that this can be estimated based on other more easily obtained body composition measures?
Line 277 – 279: I think this sentence could be rephrased to improve its readability.
Line 290: I’m not sure what you mean here by the phrase “neural measures are more accurate than dynamic ones”. Please rephrase is to make it clear to the reader.
Line 294 – 298: this sentence is a little bit too long and challenging to read and I therefore suggest you break it into two or three smaller sentences to improve readability.
Line 313 – 325: one thought I had in relation to the challenging question of whether single joint or multi-joint strength exercises should be used in the context of the questions addressed in this paper may reflect the multifactorial determinants of strength across various joints and the roles of other muscles that act as synergist or stabilisers to the agonist muscles. As an example, could the results of a study in which you assess the hypertrophy of a variety of quadricep and gluteal agonist muscles and changes in squat 1RM be influenced by the potentially varying changes in hypertrophy and strength of muscles that contribute to trunk stiffness as these trunk muscles might be seen as the weak link in regards the potential to maximise the force production capacity of the lower limb in the squatting motion? As the hypertrophy and strength of these muscles influencing trunk stiffness are generally not measured in such studies, is this something that also warrants more discussion on this manuscript?
Overall: you have made a pretty strong case for the assessment of PCSA as the preferred measure of muscle hypertrophy, are you able to make such a case for the optimal method to measure muscle strength? Would this optimal measure differ for studies in which the relationship between strength and hypertrophy is the primary outcome compared to studies just concerned with improving strength?


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: METHODS MATTER: THE RELATIONSHIP BETWEEN STRENGTH AND HYPERTROPHY DEPENDS ON METHODS OF MEASUREMENT AND ANALYSIS
Review round: 2
Reviewer: 1

Output:
Basic reporting: Nothing additional to add.
Experimental design: The authors have added a reference indicating that ICC(2,1) was reported and that this supports the reliability of the rater in the study. While this is true, I personally would feel more comfortable with the authors at least noting that the lack of reliability data for the specific rater in this study is a potential limitation.
Validity of the findings: Nothing additional to add.
Additional comments: I am happy that the authors have adequately addresses my comments. This will be an interesting addition to the debate around this topic and I expect that it will likely stimulate further discussion and consideration of how to better answer the question of whether, and to what degree, changes in muscle size contribute to changes in strength. The authors included discussion regarding causality offers a balanced nuanced consideration of the topic.


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: METHODS MATTER: THE RELATIONSHIP BETWEEN STRENGTH AND HYPERTROPHY DEPENDS ON METHODS OF MEASUREMENT AND ANALYSIS
Review round: 2
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: Congratulations on addressing my previous criticisms with the initial version of this manuscript. The only tiny revision I request is that you break a large paragraph into two smaller paragraphs. The paragraph I refer to starts on line 279 and finishes on line 329. This will help improve the readability of this section of the manuscript.