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

Input:
Title: HABITAT AND LANDSCAPE FACTORS INFLUENCE POLLINATORS IN A TROPICAL MEGACITY, BANGKOK, THAILAND
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript 'Habitat and landscape factors influence pollinators in a tropical megacity, Bangkok, Thailand', is an extremely well-written report of pollinator abundance and diversity, as well as the factors that promote or impeded abundance/diversity, in Bangkok, Thailand.

I have a few comments for improvement, related to references and one figure. These comments are relatively minor.

***Line 271: Lowenstein was conducted in Chicago, IL, which many would consider to be a large city.
***Line 268 and Line 275: Matteson and Langellotto (2011) is cited in these two lines. However, I believe the correct citation is Matteson et al. (2009). The 2009 paper is where we report on bee diversity in NYC gardens. Our 2011 paper secondarily cites our 2009 data.
***I hate to self-promote, but I do believe that Matteson and Langellotto (2010, Determinates of inner city butterfly and bee species richness, Urban Ecosystems 13(3): 333-347) would make a nice addition to this paper, in lines 296-297, and also in line 343. We used a different analysis (Bayesian analysis, rather than GLMM), but also found that garden size (patch size) and floral abundance best explained bee richness in NYC. We found that landscape level greenspace had no impact on bee richness). Since the results align with what the authors found in Bankok, Thailand, I thought it might make a good addition.
***In figure 2, is there any way to change the gray-scale lines to various dashed or dotted lines? I personally had a difficult time distinguishing between the two lightest scale grays.
Experimental design: In the manuscript 'Habitat and landscape factors influence pollinators in a tropical megacity, Bangkok, Thailand', the authors report the results of a four month study of pollinator abundance and diversity across 52 plots. Although the time scale for the study is fairly short term, the spatial extent of the study is impressive. The large number of pollinators observed over the course of the study (>18,000 pollinators) suggests that the authors sufficiently sampled the sites.

Although there are an increasing number of published studies on pollinator diversity from temperate cities, the authors correctly point out that the number of published studies on pollinator diversity from tropical cities is a void in current literature.

I have a few minor comments on the methods.

***Line 110: what methods were used to compare pollinator abundance and diversity between the two time periods? Specifically, how many patches were observed, and how many times?
****Line 127: pollinator diversity would be more accurately described as pollinator richness
****138-139: attractive plants are listed as plant species, rather than as ornamental cultivars. I would be surprised if wild type plants, rather than cultivars, were planted in these public spaces. If that is the case, but the authors identified plants to species, rather than cultivar, please say so. Or, if these were truly wild-type plants, not bred for ornamental displays, please say so.
****In the pollinator observation sections, could you please provide more details on the pollinator sampling? Were all plots sampled once between January and April 2017? Were plots sampled multiple times during this time period? Were all plots sampled every day or every week during this time period? It is hard for the reader to understand the sampling extent, without these additional details.
Validity of the findings: I have no comments for improvement on the data or conclusions.
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: HABITAT AND LANDSCAPE FACTORS INFLUENCE POLLINATORS IN A TROPICAL MEGACITY, BANGKOK, THAILAND
Review round: 1
Reviewer: 2

Output:
Basic reporting: 1. Despite being an overall well-written article, I had an initial negative impression of the writing. This is likely because the very first sentence (lines 20-22) is the most poorly written sentence of the entire article. The sentence is both vague (e.g., urban area biodiversity is relatively limited compared to what?) and inaccurate (i.e., your results and all others cited show that a lot more than a "few" pollinator species are found in cities) and therefore, requires editing or rewriting. Lines 29-30 should also be made less vague, for example by stating the direction the most influential factors had (i.e., positive). A stronger and more clear abstract will give readers a better sense of the article's merit before diving in for the full read.
2. The authors have provided adequate introductory material/ context and have covered their bases in terms of relevant papers. However, a reference may be needed at lines 140-141. Have other studies excluded non-attractive plants from floral abundance measurements? If so, an example should be cited.
3. Line 225 remove the word smaller
Experimental design: A meaningful exploration of an important (and large) knowledge gap is addressed through this study of urban pollinators in a tropical city.
1. The overall study design appears sound, however, some vital details are missing. A time range is indicated for when the data were collected (Line 97), but no other information is provided about how sites were sampled over this period. E.g., was each plot only sampled once during this period or multiple times? Were all plots in a green area visited on the same day? Were multiple green areas visited on the same day? What was the rationale behind these sampling decisions? My main concern here is that some areas may lack continuous blooms and therefore frequency of sampling may impact results. The Pollinator Observations section (Line 107) should be expanded on by answering the above questions, providing rationale for temporal sampling decisions, and making sample sizes less ambiguous.
2. Lines 137-139 are confusing. The preceding sentences detail the methods used for determining landscape-level characteristics which led me to think that floral abundance was recorded at a similar scale. I later realized that it was recorded at the plot-level. Please add this detail to these lines.
3. Lines 196-199 provide results on pollinator visitation per flower. It is unclear what per flower means because the methods describe plot-level pollinator recording not flower-level. More description is needed in the methods section to make these results comprehensible.
4. Although some rationale is provided for sampling in the morning (Lines 109-111), it is unclear how it was determined that morning vs. afternoon sampling are equivalent.
Validity of the findings: 1. Without knowing the exact protocol for sampling across space and time, it is impossible to assess the validity of the findings. Sample sizes need to be made less ambiguous in the methods as well as reported in tables/ figures (and/ or their captions). For example, it is unclear what each point represents in Figs 1 & 2. Does a single point represent a site average across plots? Or does a single point represent a plot average over multiple observation periods?
2. In addition, the validity of the findings are put into question by the inclusion of an outlier data point. The floral abundance panels in Fig. 1 and Fig. 2 show that there is an outlier point that may be affecting results. Further visual inspection of the data should be completed to confirm outlier status. It is advisable that if this point is an outlier, it should be removed and all analyses should be re-run. Changes to the results due to the exclusion of this outlier should be reported and subsequent interpretations updated to reflect these changes. The outlier site (School Sumran Wittaya) was only sampled at two plots which may be leading to an extreme result. There also may be biological reasons for excluding this sample (e.g., one of the plots contains a vine species with thousands of flowers that appear to be relatively unattractive to pollinators).
3. Based on the inclusion of the outlier, I have to wonder if the cut off for determining attractive flowers was inadequate. In addition to citing papers that have removed unattractive flowers from floral abundance counts before, it might be worth reviewing how attractiveness cut-offs have been determined in other papers. How do your results change if the threshold for attractiveness is changed?
Additional comments: This paper has the potential to spur much needed research on pollinator diversity in tropical cities. Unfortunately, a few major flaws prevent it from immediate publication. Some of the flaws are easily fixed by re-running analyses, however, without more information on how plots were sampled across time it is hard to judge whether the data are also plagued by poor experimental design.


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: TRENDS IN BACTERIAL AND FUNGAL COMMUNITIES IN ANT NESTS OBSERVED WITH TERMINAL-RESTRICTION FRAGMENT LENGTH POLYMORPHISM (T-RFLP) AND NEXT GENERATION SEQUENCING (NGS) TECHNIQUES—VALIDITY AND COMPATIBILITY IN ECOLOGICAL STUDIES
Review round: 1
Reviewer: 1

Output:
Basic reporting: Some of the methodological details were unclear to me, but most of the text was well-written.
The captions for the tables and figures need to be more comprehensive. I was confused by some of them and they are not self-contained.
For the fungi, the primers were the same for T-RFLP and MiSeq (fITS7 and ITS4). However, the bacterial primers differ (T-RFLP: 27F and 1387R; MiSeq: 27F, pD). I would like an explanation of why the bacterial primers differed for the different methods and outline how this could impact results in the Discussion.
How TRFs were aligned to OTUs is not clear to me. How were the sequences aligned with the virtual TRFs? Which program? How similar were sequences from MiSeq considered to be the same as the virtual taxa?
I am confused about the functional organisation analysis and why it is necessary.
Bioinformatics: I need a bit more information here. There is no information on the quality filtering and the number of reads. This is useful information for people who may want to use these methods in the future so they can get an idea of the necessary sampling depth. Also, what length were the sequences cut to before clustering? Was any denoising done?
Experimental design: No comment
Validity of the findings: I would argue that the curves do not show similar patterns in the bacterial communities for the different methods and that MiSeq has done a better job of capturing this. Note that the curves do not reach asymptote when using TRFLP for either bacteria or fungi – this should be discussed in the Discussion because it suggests undersampling.
“Regardless of the molecular method, bacterial communities were more comprehensively sampled than fungal communities, judging by how rapidly the asymptote was reached by the bacterial vs. the fungal curves (Fig 2).” – This is not true – asymptote was only reached for the bacteria in MiSeq
Some more discussion on how this approach compares to the traditional cloning library would also be worthwhile.
Additional comments: Lindström et al provide a novel methodological insight into comparing a traditional DNA fingerprinting technique, T-RFLP, with next generation sequencing, Illumina MiSeq, in bacterial and fungal communities from ant nests. They found that there was reasonably strong congruence in results when using both methods, but more taxa were able to be delineated from the MiSeq, which they note as unsurprising.

This is a topic of interest and the experimental design and methods are generally well-written. I found the first part of the manuscript very well written and clear, but there needs to be more detail in some parts of the methods and results for me to be able to follow how things were done.

One aspect that is mentioned in the introduction but provides clear support for the approach is the possible benefit of combining NGS with T-RFLP in longitudinal studies. For example, the first measurement could use both methods to get comprehensive taxonomic information and relate NGS OTUs to TRF virtual taxa, then in subsequent sampling we may be able to rely on just TRFLP. It could potentially overcome some of the criticisms involved in fingerprinting alone because we would still have taxonomic information, enabling us to discuss ecology. This could substantially reduce costs and I think this is a key strength that supports the novelty of the study.

I found most of the data analyses to be well-chosen but it is unclear how the virtual TRFs were assigned to taxa, which is clearly a very important part of the study. The functional organisation measure is unclear to me and I am not sure what the information it provides other than information about dominance, which seems to be easy enough to assess by just looking at read counts.

The captions for the tables and figures need to be more comprehensive. I was confused by some of them and they are not self-contained. The readers need to be reminded how many samples are being analysed and also that OTUs are from the MiSeq.

I suggest depositing the raw data into an online database, such as dryad, rather than providing it as supplementary material.

Introduction
L52: It should be noted that quantitative information from these fingerprinting methods is not always considered appropriate, requiring rigorous standardisation techniques that are not always used (Green SJ, Leigh MB, Neufeld JD (2009) Denaturing Gradient Gel Electrophoresis (DGGE) for Microbial Community Analysis. In: Handbook of Hydrocarbon and Lipid Microbiology (ed Timmis KN), pp. 4137–4158. Springer, Heidelberg, Germany). This is why many authors choose to use presence-absence. The same concerns have been raised about NGS data (Amend AS, Seifert KA, Bruns TD (2010) Quantifying microbial communities with 454 pyrosequencing: does read abundance count? Molecular Ecology, 19, 5555–5565)

L60: NGS acronym needs to be defined.
L80: “Similarly to microbes…”. I suggest removing this part of the sentence because microbes are much more ubiquitous than ants
This paragraph could be linked better with the molecular method information in the first paragraph. Perhaps bringing the microbial relationships with ants into the first sentence as a link would make this link clearer. After reading the rest of the manuscript, I think this paragraph could potentially be cut down, since this information is not really relevant for the methodological aspect of the study.

Methods
L144: “lusher patches of vegetation” is vague. I suggest giving a broad overview of common plants in the area and/or state the biome. I am also interested in the soil type, given that the ants nest in soils.
I suggest a slight restructuring of the Methods. Combine subheadings “DNA extraction and PCR amplification for T-RFLP” and “Analysis of T-RFLP data” into “T-RFLP Analysis” subheading. I suggest the same for the MiSeq methods. Also, put the MiSeq part first, then the T-RFLP information, so that the virtual T-RFLP section is encompassed in the larger T-RFLP section.
For the fungi, the primers were the same for T-RFLP and MiSeq (fITS7 and ITS4). However, the bacterial primers differ (T-RFLP: 27F and 1387R; MiSeq: 27F, pD). I would like an explanation of why the bacterial primers differed for the different methods and outline how this could impact results in the Discussion.
Bioinformatics: I need a bit more information here. There is no information on the quality filtering and the number of reads. This is useful information for people who may want to use these methods in the future so they can get an idea of the necessary sampling depth. Also, what length were the sequences cut to before clustering? Was any denoising done?
L193: I am inferring that the most common 200 OTUs were chosen because these are the ones that would be expected to be captured in the T-RFLP analysis. I’m interested why this number was chosen and if other numbers were tried – different iterations of this could certainly strengthen the validity of this approach.
L197: This part is not clear to me. How were the sequences aligned with the virtual TRFs? Which program? How similar were sequences from MiSeq considered to be the same as the virtual taxa?
L204: Please provide version numbers for the packages used and provide a citation for R. It is also helpful to provide the function names. E.g. I cannot find a function in vegan for the Good’s estimate.
L212: What does this functional organisation analysis tell us? Does it tell us about functional groups?
L228: Which dissimilarity measure was used in the PCoA?
L232: At what point was rarefying done? Prior to all of the statistical analyses, and to what depth?
Was there any point where the full OTU information from the MiSeq were analysed? It is not clear from the statistical methods.
L235: spelling: “abundancies” change to “abundances”

Results
L247: I would argue that the curves do not show similar patterns in the bacterial communities for the different methods and that MiSeq has done a better job of capturing this. Note that the curves do not reach asymptote when using TRFLP for either bacteria or fungi – this should be discussed in the Discussion because it suggests undersampling.
“Regardless of the molecular method, bacterial communities were more comprehensively sampled than fungal communities, judging by how rapidly the asymptote was reached by the bacterial vs. the fungal curves (Fig 2).” – This is not true – asymptote was only reached for the bacteria in MiSeq

L271: Suggest adding this to the end of the previous paragraph and reframing: “The Mantel tests showed good correspondence between the T-RF and the OTU data, being significantly correlated for the bacterial (R = 0.743, P≤0.001) and fungal (R= 0.574, P≤0.001) data sets.” – It is worth noting that although the correlations are significant, they are not really very high.

Table 1: I am confused by the headings here. What do the “T-RFs HaeIII T-RFs MspI” columns relate to and how do they differ from the TRFs column overall? I think it also needs to be clearer here that the OTUs are from MiSeq. Please provide more detail and remind us how many samples were analysed.
Table 2: Why are the df different for the TRF analyses. Were some samples lost? It is very interesting that the same effects come out as significant, regardless of the method.

Fig 1: I find this map is not very helpful without an outline of the wider area.
Fig 2: These graphs are great. I find it very interesting that the species accumulation for fungi is similar for the two methods, but the MiSeq has clearly done better in the bacterial community in fewer samples. The curves do not reach asymptote when using TRFLP for either bacteria or fungi. This warrants mention.
Fig 3: I do not understand these graphs and need more interpretation in the text.
Fig 4: It is not clear how the monthly samples lay over this and it seems that the sites are not different in different years. There are also clearly artefacts in the ordination in 4B and D, with curves. I suggest trying to transform the data or try a different dissimilarity measure.

Discussion
The discussion can use some re-structuring and focus. The interesting information is all there but it is difficult to find. I would focus the first part of the discussion heavily on the aims of the study, i.e. the comparison of MiSeq and TRFLP and how they aligned and where they did not. Then after this, move on to the patterns that were shown to be similar in both methods (i.e. the PERMANOVAs and PCoA). Then I would move on to how these taxa relate to wider studies. At the moment this all seems a bit jumbled together.
Really, the key outcome is that T-RFLP can tell us about common species in the communities, and these are the ones that drive the multivariate analyses used. Indeed, often the rare species are removed from NGS data in order for us to see a clearer pattern (it is not clear if this was done for the current data).
Some more discussion on how this approach compares to the traditional cloning library would also be worthwhile.
L324: spelling “reactive” to “relative”
L334: For MiSeq, the length the sequences were cut in the bioinformatics is more important than the primer length, in terms of getting phylogenetic information.
The second paragraph of the discussion is comparing bacterial and fungal communities. I feel like this detracts from the aim of the paper and the TRF vs MiSeq comparison is lost in the detail here.
L353: ‘high functional organization signals numerical dominance by a few species” – this explanation of the metric should be moved to the Methods.
L355: “This agrees with our finding that 50% of the fungal sequences, and 60% of the bacterial sequences were found among the 200 most abundant OTUs.” – This statement makes me wonder the value of the functional organisation method, since this more simple assessment has provided the same answer. I had also expected the functional organisation analysis to provide information about functions of taxa in the communities, but it seems to only provide information about dominance.


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: TRENDS IN BACTERIAL AND FUNGAL COMMUNITIES IN ANT NESTS OBSERVED WITH TERMINAL-RESTRICTION FRAGMENT LENGTH POLYMORPHISM (T-RFLP) AND NEXT GENERATION SEQUENCING (NGS) TECHNIQUES—VALIDITY AND COMPATIBILITY IN ECOLOGICAL STUDIES
Review round: 1
Reviewer: 2

Output:
Basic reporting: Paper by Lindström et al. is well written, clearly structured and research questions well defined. If there is a weaknesses it is in the presenting results. Firstly, there is many figures and tables, could you combine some of them or even provide information in the text? For example, Figure 1 could be transferred in the supplementary material, also a small map of Finland could be added to the figure 1 to illustrate where study areas in Finland are located. Table 2 could be also added to supplementary material, however the key PERMANOVA results including  F, P and df should be added in the text. Also, figure 4 would need ellipses to point the key results in the figure i.e. island and nest. Furthermore, figure 4 is missing x and y –axis labels, they should be added. Please, report P-values in italics.
Experimental design: Article meets PeerJ standards. Please specify why 200 most abundant OTU’s were used to match the Illumina OTU’s and their identities with the experimental T-RFs. Also, specify used 16S reverse primer for T-RELP and Illumine MiSeq, do they differ between the methods? Line 229 specify PERMANOVA is one-way nonparametric permutational multivariate analysis of variance and add citation to Anderson 2001. In line 232 do you mean rarefying?
Validity of the findings: Lindström et al. state that the bacterial and fungal communities in the F. exsecta mounds have not been studied previously, however community structure of fungal and bacterial communities in F. exsecta are not thoroughly discussed. In particular, Tremellales incertae sedis and Venturiaceae fungal families which are not currently defined as having any association with ants could be discussed further, this would increase novelty of the work and fills profoundly identified knowledge gap. Otherwise, advantages and disadvantages of the used methods are extensively discussed, also their validity and compatibility in ecological studies are well discussed. However, discussion could stated more clearly that the method used for studying microbial communities can have effect on the results i.e. for rare and perhaps endemic taxa. Therefore chosen method should be based on the aim of the ecological study. Also, cost and time of the methods could be discussed in more detailed.
Additional comments: Paper by Lindström et al. is well written, clearly structured and research questions well defined. The article clearly states and responses  identified knowledge gap, however this could be improved with detailed discussion.  It meets PeerJ standars, but still before mentioned small changes should be provided upon before acceptance.


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: TRENDS IN BACTERIAL AND FUNGAL COMMUNITIES IN ANT NESTS OBSERVED WITH TERMINAL-RESTRICTION FRAGMENT LENGTH POLYMORPHISM (T-RFLP) AND NEXT GENERATION SEQUENCING (NGS) TECHNIQUES—VALIDITY AND COMPATIBILITY IN ECOLOGICAL STUDIES
Review round: 2
Reviewer: 1

Output:
Basic reporting: I appreciate the authors for the work they have in to account for my previous comments. I find the aims of this study very interesting and addresses very current issues surrounding molecular techniques. The changes that have been made have greatly clarified my previous concerns and have strengthened the manuscript.
Experimental design: The great contribution of this paper is to provide others with the ability to do TRFLP and have confidence that the general community patterns will be the same as the more expensive NGS MiSeq. Rewording the last sentence in the abstract and also emphasising this in the introduction and Discussion could strengthen the paper.
Validity of the findings: I still find the details of the bioinformatics sequencing too sparse for this study that is focussed on comparing molecular methods. These methods and decisions during sequence processing could greatly determine similarity of the results between TRFLP and MiSeq. I am not suggesting a reanalysis but more information on how it was done. E.g., what kind of quality control was done after the sequences were obtained? Were paired-end reads used and how? How long were the final sequences? How were chimeras detected and removed? How were OTUs defined (e.g., 97%)? What was the lowest number of reads (L217 indicates samples were rarefied to this)? What were the range in read numbers for different samples? Were samples with very low reads omitted?
This recent paper highlights some of the issues that should be covered: https://www.nature.com/articles/s41579-018-0029-9
Additional comments: Fig. 2. Thank you for clarifying the interpretation of these panels. In each graph, is the dotted line the results from the NGS and the solid line from TRFLP? Or vice-versa?

The addition of the explanation of the different primers used due to methodological considerations would be better placed in the Methods because this is where the reader is wondering why they are different.


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: ADVERTISEMENT CALL OF BRACHYCEPHALUS ALBOLINEATUS (ANURA: BRACHYCEPHALIDAE)
Review round: 1
Reviewer: 1

Output:
Basic reporting: This manuscript present a description of the advertisement call of a microendemic Neotropical frog, which is poorly know. The knowledge about acoustic properties of different species are especially important for anurans taxonomy and behavior, and, then, papers like this can help to improve our biodiversity understanding. I am very excited to see good manuscripts with call descriptions coming to be published in PeerJ. This group of tiny frogs from Brachycephalidae family have many species with calls unknown, which raises the importance of this manuscript. The authors present a manuscript with a legitime intentionality in a well-written text. However, some issues, basically related to the acoustic and data analysis, were listed and should be improved upon before acceptance.
Experimental design: The sample effort is satisfactory and matches with the objective of the paper.
Validity of the findings: Questionable, considering the issues pointed specifically in the general comments.
Additional comments: Although the results are compelling, the note-centered approach used by the authors for recognize different advertisement calls of the same male is questionable, because it is not clear how the authors make the distinction of a call unit inside a sequence of calls. Other detail, more problematic, is that the concept of uninterrupted units of sound are not well interpreted for pulses analysis, once that, using this context, pulses need to be fused and not separated by space as the authors were using. In this case, they are counting notes, and not pulses. Considering this, the temporal analysis of advertisement calls is ruined, and should be reformulated or rethought. One of the main issues is that spectral data were, basically, neglected by the authors. Range, minimum and maximum frequency were not included, because the authors found a strong dependence of this data with the quality of recordings. So, why didn't they use only the good recordings for obtaining these values?
Other special issue is that dominant frequency presented an uncommon high variability. It could be real, but I understand that pre-editions and adequate use of a sample value in Fast Fourier Transform (FFT) for spectral measurements would alleviate this variation, and potentially may generate reliable measurements. Finally, the way that the variation on call properties were presented is out of the regular pattern used for describing acoustic data in such matter. Call properties are regularly classified as static or dynamic, depending on the coefficient of variation calculated by: (standard deviation / average) multiplied by 100 (see: Gerhardt HC. 1991. Female mate choice in treefrogs: static and dynamic acoustic criteria. Animal Behaviour 42(4):615–635). There is a well-structured discussion in the literature about why some call traits present high variability, while others are very stereotyped, mainly concerning to social context, species recognition and temperature effects. See the discussion in Forti, L.R. et al. 2017: The advertisement call of Sphaenorhynchus caramaschii. Further, the variation in the species level may help to establish boundaries among sister species. To the moment, we do not know if species from the pernix group are insensitive to calls, and, while someone do not prove something different, calls still are sexual signals used for intraspecific communication, and they are useful for species diagnosis. Such subjects are totally missing in the manuscript.
Some specific issues are: The authors said that “We made numbered markings close to the recorded individuals” for avoiding the recordings of the same males. However, how were made this “markings” for such tiny frogs? How was this controlled? Were the distance among neighbors measured? Their territory size was previously calculated? Were studied the males movement?
In the conclusion the authors said that some call traits may be related to individual arousal levels. And, they have concluded that, the variation on calls composition are possibly related to defense of territory and female preference. However, they do not have evidences to link these relationships, and once these thoughts are only speculations, it should be out of the conclusion.  All these issues have to be addressed in 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: ADVERTISEMENT CALL OF BRACHYCEPHALUS ALBOLINEATUS (ANURA: BRACHYCEPHALIDAE)
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper describes the advertisement call the recently described Brachycephalus albolineatus. The paper is well written, and relevant data is shown.
I found the introduction to be quite long, way beyond what would be expected for a call description paper. For example, it discusses in detail the evolutionary history of the genus, and the differences among its three phenetic groups (lines 51-93). Even though it is interesting, it induces the reader to expect a comparative analysis based on call parameters, which would allow for the investigation of the evolutionary history of the group. As put by the authors themselves on line 104: “Given that Brachycephalus is a group with mostly allopatric species, it is of great interest to investigate the evolution pattern of their calls”. However, no formal comparative analysis was made, and the discussion comparing the described call to those of other species is not compelling, and lacks of focus. The authors also mention that: “Over the course of our studies on mountain frogs from the southern Atlantic Rainforest, in which we discovered several new species of Brachycephalus (Pie & Ribeiro 2015, Ribeiro et al. 2015, Bornschein et al. 2016b, Ribeiro et al. 2017), we recorded the advertisement calls of nearly all of them”, but here they described the advertisement call of a single species. The authors are clearly missing the chance of making the evolutionary investigation (what is seems to be proposed in the introduction), while describing the advertisement calls of several Brachycephalus species in the process. As I see, there are two distinct directions for the paper. Either the authors simplify the manuscript by making a call description paper with a straightforward introduction, results and discussion; or really investigate call evolution within the group, describing the calls they do have, and making a comparative analysis that might include distances comparisons (phylogenetical, acoustical or geographical), or examining the presence phylogenetic signals in species’ calls.

I really hope the suggestions made here does not disappoint the authors, while helping them in preparing a new improved version of the manuscript for submission.
Experimental design: The study aims to investigate the evolution pattern of the calls of the genus Brachycephalus, but fails to do so on its present format. Nevertheless, it elegantly describes the advisement calls of Brachycephalus albolineatus. The way I see, there are two possible roadmaps to be followed. The paper can either be simplified, aiming to describe the advertisement call of the species, or it could formally include a comparative analysis, which could formally investigate the call evolution patterns of the group.
I feel most of the tables should be moved to supplementary materials, for they fail to support the paper’s discussion and objectives, even though the data could provide helpful information for upcoming work. A single table could give full support for a call description paper, by describing the mean (or median) of each parameter (e.g. dominant frequency, pulse rate, note rate etc.) of the call. Additionally, I feel figure 1 could be improved by the use of a measurement map, which shows, by using a sonogram/oscilograma of a call, the measurements made. I really don’t feel the scheme of fig 1. has worked. I had a hard time trying to understand what was represented there. I also don’t see the necessity of figures #2 and #4. If the authors wish to show the macrostructure of the call, they could do this in figure 3, by showing a spectrogram of a call with a longer time window. For instance, spectrogram D works well to show the pulse number variation showed in the first column (A, C, E), while an even longer spectrogram (maybe with 30s or more) could show the intended macrostructure in figure 2. Either way, the spectrograms are great. As for figure 4, I really don’t see its purpose, what is the intention in showing individual variations in dominant frequencies? These differences are present in most calls (the coefficient of variations are usually between 10-20%), and unless the authors have a clear objective for the inclusion of figure 4, I would advise to remove it.
Validity of the findings: The paper should either be reformulated to a call description paper, or to a comparative analysis. In its current form, it seems to propose a comparative analysis, which was not made.
Additional comments: l.61-63: Since this is a paper on acoustical communication, it might be important to cite that the process of miniaturization might also affect species hearing abilities (SILVA, H. R., CAMPOS, L.A., SEBBEN, A. 2007. The auditory region of Brachycephalus and its bearing on the monophyly of the genus (Anura: Brachycephalide). Zootaxa 14122: 59-68.)
l.66-93: Unless the paper really tackles the acoustical evolution of the group, I feel these two paragraphs are beyond the objectives of the paper, and should be completely removed.
l. 104 Even though the authors recognize the importance of call descriptions, and sustains that the lack of descriptions are surprising due to the conspicuous acoustic behavior of the group (l.97), they only describe the call of a single species. This is surprising, specially as the authors clearly announce that they have recordings of at least 10 species of the genus (l.108-111)!
l.119-220: There is no need to mention discarded recordings.
l.121-124: There is no need for SISBIO licenses for sound recordings, unless these are made within federal parks. Not really sure why the information on these licenses are necessary.
l.124: Please consider starting the methods by describing the study area. From the text I am not sure whether the recordings were made within the type locality.
l.132: It seems some of the spectrograms were build with edited files, in which the intensity was normalized to 0dB before the analysis. Please clear out what the editing consisted of.
l.137: Even though noise filters could affect the signal, a high pass filter at 2kHz, for example, could reduce low frequency noise such as depicted in spectrograms B, E & F (Figure 3). Please consider the use of high pass (sometimes band pass) filters followed by normalization as a standard editing procedure. This procedure allows for direct comparisons between the analyzed calls. Please  (http://dx.doi.org/10.1016/j.anbehav.2012.04.026)
l.143: I am not sure what the authors considers to be a “conspicuous spectrogram”, and have no idea what they mean by “compare to the oscilogams”. Compare how? Please elucidate.
l.145: If a note is composed by pulses, it cannot be composed of “uninterrupted units of sound”, for silence should be found between the pulses that forms a note.
l.178: It is not clear to me what the authors named isolated notes. It does not seem to be a single note, but rather notes issued with a much lower emission rate (even though the inter note interval seems to be around 6s for both; l. 221). If this is the case, and considering that such differences in the emission rate could code for distinct messages, it seems to me there are two repertoire components being described here, not a single one. Both components are named as advertisement calls by the authors, but discrete acoustical differences such as displayed here are usually associated with two messages, not a single one. For instance, differences on emission rates and number of pulses are the main alterations found between territorial and advertisement calls of B. pitanga (Araújo et al. 2012, cited by the authors). Did the authors considered the possibility of two repertoire components? Either way, please better describe what are you calling isolated notes.
l.202: Calls from different individuals are rarely so stereotyped, and a similar variation are found elsewhere. For example, Verdade et al. 2008 (cited by the authors) describes a standard deviation of about 1kHz within B. hermogenesi dominant frequencies. Hence, unless the authors wish to test the use of these calls to transfer information on individuals (what does not to seems to be the case), I suggest removing this portion of the ms.
l.240: Even though we agree that the absence of standardization prevents a detailed comparison, there are call parameters that are present in most call descriptions of the group and could be uses in such comparisons, such as dominant frequency, number of pulses, pulse rate, note rate, note duration and inter-note interval. Additionally, as the authors already possess recordings of nearly 10 species, the description of those calls could allow for species comparisons.
l.242: Most call descriptions of Brachycephalus were made based on “call-centered approach”, and it seems the authors have not measured the entire call, as defined here (e.g. Verdade et al. 2008, Araújo et al. 2012). The analysis of a portion of the advertisement call (as defined here) has been widely used for species with long calls, such as Rhinella (http://dx.doi.org/10.11646/zootaxa.3784.1.9), even though the description of the entire call have also been made for the genus (http://dx.doi.org/10.2994/057.005.0209). It could be that the calls are too long, making it difficulty to record from the start. Nevertheless, it is possible to make comparisons with the note parameters described here (even though it would be considered a call in other studies).
l.256: the authors have not measured call intensity.
l.258: Even thought Sandra Gautte’s paper is quite interesting, I would take it cautiously. There is substantial morphological modifications in the hearing apparatus of the group (Zootaxa 1422: 59–68 (2007)), probably related to its minituriarization (Biological Journal of the Linnean Society 99: 752-767 (2010)). The authors did not examine in full the possibility that m. opercularis would have a central role in Brachycephalus hearing abilities, not bony elements. Additionally, due to the presence of multiple repertoire components (e.g. Araújo 2012), it would be quite counter intuitive for these frogs to have lost their hearing abilities. In sum, even though the quality of the work done by Sandra Goutte and its collaborators, I would take it cautiously, and wait for further papers with the group before assuming the frogs do not hear.


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: ADVERTISEMENT CALL OF BRACHYCEPHALUS ALBOLINEATUS (ANURA: BRACHYCEPHALIDAE)
Review round: 2
Reviewer: 1

Output:
Basic reporting: In general, the work have advanced in quality, the inclusion of a table comparing acoustic properties among species is very informative and useful as a “short review” about the current knowledge of bioacoustics in the genus. I congratulate the authors by the detailed review and improvements. However, some appointments in the first review have not been solved, even being necessary as showed in this new review. I really want to see this paper published as soon as possible, because it is a very important contribution (handled with a clear determination), but, first, some details should be adjusted before a final acceptance.
Historically, terms as pulses, notes, calls, chirps already have been used to label the same kind of basic acoustic units. Even after reviews of the subject as Toledo et al. (2014) and Köhler et al. (2017), still there are authors with particular interpretations. Such arbitrariness is always subject of confusion, and I understand that the authors defined call units by the note-centered approach described in Köhler et al. 2017, and that is ok. However, there is an unclear conceptualization yet. The authors are so emphatic that comparisons are limited due to the lack of a standard analysis procedure, but how can someone reproduce the measurements if there is no precision to define how long should be the silence interval among two different calls? Calls periodicity should be well described, once further works may test their functions.
I agree with the authors that pulses can be separated by silence interval (which is clear in “Köhler” et al. 2017), but the criteria adopted for notes as “uninterrupted sound units” was contradictory, once that using this definition and seeing the figure 3, each note would be an isolated pulse, because they are not fused. However, listening the calls present in the supplement files, I could better understand the authors’ view, once the note (using their definition) sounds very quick, even considering discrete intervals of silence among pulses. The interval of silence among pulses is noticeable only in the waveform (not by human hearing). The decision of take off the detail “uninterrupted sound units” to avoid confusion is a reasonable option. Although, there is a suggestion for classifying individual notes by a single cycle of airflow back and forth from the lungs to the vocal sacs (see Gerhardt, 1998). I don´t know if authors have saw males calling (because they apparently emit calls under the leaf litter), but this definition for notes, in this case, sounds very comfortable, and may avoid confusion. Besides, nothing changes in the results.
	The authors wrote: “maximum and minimum frequency, are highly dependent on the recording conditions” - which conditions are those? For justifying the absence of these variables in the first version of the manuscript the authors argue that other papers have not included it. This is a naive and scientifically poor argument. If other authors have failed in such respect, they gonna fail too. This journal and society expect the best of knowledge, not just the acceptable.
Seems that the authors have included these properties in the manuscript without understand how they could be measured, once they declare "there is no clear limit of the beginning and ending of minimum and maximum frequency". I must say, all acoustic signals, in all spectral gradient, has a maximum and minimum frequency very accessible if they are not masked by background noise. Professional bioacoustics software, as Raven, measures it with precision. In Raven you should use a tool in the “choose measurements” called “Frequency 5% (Hz)” and “Frequency 95% (Hz)”. Once you selected your call units, the values will appear in a table. This tool measures the minimum and maximum frequency based in the energy distribution along spectral domain, considering a confidence interval of 5% inside the selection. Peak normalization process, which I suggested in the first review (not carried), it is an important step for standardization of amplitude among notes, which may avoid biases related to the variation on intensity, making call units more comparable and this tools (Freq 5% and 95%) more reliable. The method used by the authors (made by eyes, directly inspecting a colorful spectrogram) is very inaccurate, as they themselves assumed. I suggest the way I commented above.
About the variability in dominant frequency, the authors argue “We could expect this variability, since it reflects individual variation, but we do not understand how a pre-edition and an adequate use of a specific value in FFT size could change this result and yield more reliable measurements.” And they follows with a comparison of DF based in rough graphical interpretations with different FFTs. If the authors know the significance of FFT, they must understand that spectrograms generated by high FFT sizes should increase precision in spectral measurements, because the energy will be sampled inside smaller spectral classes (frames), see the figure 1 in the zenodo repository for understanding (one note of B. albolineatus represented by two FFTs).
Figure 1 in: https://doi.org/10.5281/zenodo.1193816
Then, it is clear that more accurate spectral measurements were achieved with FFT of 1024. When we transpose it to the right way of obtaining these variables in Raven, some differences could be noticed. Then, I repeated the test applied by the authors:
Test 1 – FFT = 126: DF = 5857 Hz, MaxFre =7235 Hz , and MinFreq = 5512 Hz
Figure 2 in: https://doi.org/10.5281/zenodo.1193816
Test 2 – FFT = 256: DF = 5857 Hz, MaxFre =7062 Hz , and MinFreq = 5512 Hz
Figure 3 in: https://doi.org/10.5281/zenodo.1193816

Test 3 – FFT = 512: DF = 5857 Hz, MaxFre =6976 Hz , and MinFreq = 5512 Hz
Figure 4 in: https://doi.org/10.5281/zenodo.1193816

Test 4 – FFT = 1024: DF = 6847 Hz, MaxFre =7019 Hz , and MinFreq = 5598 Hz
Figure 5 in: https://doi.org/10.5281/zenodo.1193816

In all examples, we find spectral differences among the FFTs tested.
The authors declared: “it is possible to see differences in the resolution of spectrograms” – Of course we might like to have fine temporal and spectral resolution in a spectrogram, although these two demands are almost incompatible. However, adjustments in window overlap enable considerable resolution improvements without lost of data.
See the spectrograms in the figure 6 (Zenodo repository below) comparing the same call generated by FFT of 1024, but with different window overlap.
Figure 6 in: https://doi.org/10.5281/zenodo.1193816
Clearly a simple adjust in the window overlap value recovered the image resolution, and values of frequencies are exactly the same.
In theory, lost of resolution with a larger FFT window is only on the time scale and this can have consequences in visual inspections if the overlap is not increased (usually it is fixed at 50% in Raven). I usually do the temporal measurements using the waveform, and spectral analysis with readable spectral composition in possible higher FFTs, explored by settings in the "window overlap". Then, as the authors can see by the figures above, a higher FFT should have been used. I hope, this time, the authors would interpret my suggestion with good eyes, that usually lower FFTs can affect spectral measurements, because they are less precise.
	The authors refused the suggestion of a proper variation analysis, saying that they do not have a large number of recordings for each individual. This is a weak argument. Many acoustic properties could be explored in their material, since there are properties that not involving variations among calls, as spectral variation among notes, notes duration and pulses by notes.
In the comment 6, the authors manifested: “There is no guarantee that calls are always useful for species diagnosis” as other justification for the absence of a proper variation analysis. The sentence cited by Köhler et al. 2017 is justified mainly because body size can affect frequencies, however, sexual signals are generally good evidences for diagnosis (not guarantee), and should help to raise interesting questions about taxonomy. Further works may take advantage of such evidences to test if different populations, with different calls, could be different species, for example.
I have a particular final worry about the same subject, because the authors used a superficial view about acoustic variation declaring: “we simply believe in individual variation and not in environmental or population interferences.” First of all, in science there are no “beliefs”, there are facts, evidences and suggestions. Second, such sentence is inconsistent with ecological trends as the acoustic adaptation hypothesis or the Lombard effect, which have already been verified in previous works (see: Shen & Xu, 2016; and Goutte et al., 2016). I recommend the reading of Wilkins et al. (2012) - Evolutionary divergence in acoustic signals: causes and consequences. This is a complete review about how acoustic signals are possibly modulated.
Experimental design: Acoustic analysis have some issues to solve.
Validity of the findings: No comment
Additional comments: Some very punctual suggestions were made directly in the text, and, in my view, the manuscript presented a good advance, which included important corrections raised by the other reviewer too.


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: ADVERTISEMENT CALL OF BRACHYCEPHALUS ALBOLINEATUS (ANURA: BRACHYCEPHALIDAE)
Review round: 2
Reviewer: 2

Output:
Basic reporting: I have carefully read the revised version of the manuscript "Advertisement call of Brachycephalus albolineatus (Anura: Brachycephalidae)", and I am extremely happy with the work done by the authors. They have considered most of the suggestions made by both referees, and as a result the paper have improved much. I have no further comments, and as I see, the paper is now ready for publication.
Experimental design: no further comments.
Validity of the findings: no further comments.
Additional comments: I was very happy to see this second version of the paper, and have no further comments on 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: MORPHOSPACE SATURATION IN THE STEM-GNATHOSTOMES PTERASPIDIFORMES HETEROSTRACANS: AN EARLY RADIATION OF A ‘BOTTOM’ HEAVY CLADE
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: The authors utilize data from a previous systematics paper for the disparity analyses. The discrete data included here is presumably cladistics data used to build the phylogeny of the previous paper. The use of cladistics characters undermines one of the stated goals of the paper: to test whether the use of discrete or continuous characters show similar results for morphological disparity. The problem is that the discrete characters used here were originally selected for their value to phylogenetic analyses. Not surprisingly, when the morphospaces are plotted, the discrete characters separate the various taxonomic groups into distinct regions, the continuous characters do not. The authors discuss why this might be and suggest more convergence amongst continuous characters than discrete ones. However, the more likely answer is that the discrete characters were originally selected to separate clades not quantify overall variation. Previous published work has discussed this aspect of cladistics characters as phylogenetic analyses actively remove characters that would be considered convergent, and so fail to fully describe morphology. This needs to be discussed in the paper as I don’t not believe that the difference between discrete and continuous characters is about the form of the data, but about what the data was originally collected for.
Validity of the findings: I disagree that the data supports some of the conclusions being drawn by the authors. Specifically, the conclusion that there is concordance between the taxonomic and morphological data. These data are compared in four permutations illustrated in figures 1 and 2. The first two compare the discrete morphological data to diversity, which do show concordance. However, given the strong phylogenetic signal within the cladistics discrete data used, this is not surprising. For the continuous data, only the sum of ranges showed concordance. The total variance dataset shows almost opposite trends between the two. This is mentioned in passing in the discussion, but should be given more attention. At the very least, the data is not fully supportive of the concordance hypothesis.
Additional comments: 1.	Pg. 6; Ln 119: How many continuous characters were used?
2.	Pg. 7; Ln 128: In line with the previous comment, I am unclear how you get 22 PCs from your analysis. Were there 22 original variables?
3.	Pg. 8; Ln 155: The text mentions that the Pridolian forms occupied a different area of space than the rest of the taxa in later time bins for continuous characters. However, looking at figure 3, there is quite a bit of overlap in the center of the space between these time periods. There is certainly a shift in space, but there is common shapes being seen.
4.	Figure 4: Just a stylistic suggestion, but it would be good to have some silhouettes showing the shapes of these groups, to give context to the morphospace.


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: MORPHOSPACE SATURATION IN THE STEM-GNATHOSTOMES PTERASPIDIFORMES HETEROSTRACANS: AN EARLY RADIATION OF A ‘BOTTOM’ HEAVY CLADE
Review round: 1
Reviewer: 2

Output:
Basic reporting: There is not much background provided on the clade, nor are there any images of headshields or visualization of characters in the main text. Thus, this study is difficult to follow for readers not already intimately familiar with the previous study which generated this dataset (Randle and Sansom, 2017) and the various genera and families within Heterostraci. There should be at least some images of fishes, perhaps from different parts of morphospace.

In addition, there is no reporting of what the main components plotted in Figs. 3 and 4 represent, making it difficult to interpret what the relative positions of different groups might mean. The authors make numerous points about separation and overlap between different clusters (131-183) without explaining what this means morphologically or why it might be unexpected.
Experimental design: It is not clear why discrete characters were used to compare disparity and diversity through time. Diversity in this case is the number of terminal taxa in each bin, and the discrete characters were chosen to distinguish these taxa in a phylogenetic analysis. Thus we should expect the discrete character combinations to approximate the number of terminals in each bin. We should also expect clustering in morphospace that mirrors the tree structures, since clades will share character states (synapomorphies) that distinguish them from other families. Both these results are reported here.

Thus the discrete results come from structural biases of cladistic data, which is constructed to test phylogenetic rather than gross morphological, evolutionary or ecological hypotheses. Thus, I am not sure the use of discrete cladistic characters is appropriate or directly relevant to the aims of this study, or if the results of these analyses have any bearing on the hypotheses here, particularly given conflicting results from continuous characters.

In fact, conflicts between taxon placement in morphospaces produced by cladistic and traditional morphometric characters for scorpions have been used to argue against the use of cladistic datasets for testing hypotheses on disparity, as phylogenetic signal rather than meaningful morphological variation drives the results (Koch et al. 2017, Journal of Evolutionary Biology)
Validity of the findings: I do not think the discrete character results are useful or valid for the reasons given above.

The continuous character dataset suggests convergence between different groups, and higher disparity early on, which is the main finding of the paper. These results should be presented up front.

The discussion of biogeography and other aspects of heterostracan evolution in the conclusion seem perfunctory, and are not directly related to the results.
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: MORPHOSPACE SATURATION IN THE STEM-GNATHOSTOMES PTERASPIDIFORMES HETEROSTRACANS: AN EARLY RADIATION OF A ‘BOTTOM’ HEAVY CLADE
Review round: 2
Reviewer: 1

Output:
Basic reporting: No Comment
Experimental design: I appreciate the authors taking the time to investigate previous literature on the nature of cladistic vs. continuous characters in order to better frame their work. However, I still have a few minor issues with the discussion, though I believe these are easy to address.

In the discussion, the authors devote a paragraph to summarizing Anderson & Friedman 2012 and conclude that it doesn't pertain to the current study because they weren't trying to ascertain functional signals. It is true that the Anderson & Friedman paper was focused on interpreting function from cladistics characters; however, the authors point out key issues with cladistic characters identified in that paper, which are not restricted to functional analyses. The lack of autapomorphies and removal of noisy, homoplastic characters in cladistics datasets will still be a concern for "total disparity" analyses. These phylogenetically problematic character types are part of the overall variation, but will be missing from cladistic datasets. In other words, variation will still be missing from the cladistics dataset.

The authors also quote Anderson & Friedman saying that cladistic characters are broadly useful. Unfortunately, the authors here have ignored the discussion that followed that quote, which points out that cladistic characters will always have a cladistic signal that needs to be acknowledged when they are used.

None of this undermines this manuscript. However, care needs to be taken to acknowledge that the cladistic data used will have a phylogenetic bias (due to lacking certain types of characters that contribute to overall variation), and the discussion of the results needs to include that.
Validity of the findings: My concerns have been addressed here.
Additional comments: Overall, the authors have addressed my concerns about the manuscript (I especially like the head-plate inclusions in the figures). My only remaining concern is the way they have interpreted some of the previous work on cladistic characters that was suggested. These are minor textual corrections that shouldn't be a problem to fix, but should be addressed.


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

Input:
Title: MORPHOSPACE SATURATION IN THE STEM-GNATHOSTOMES PTERASPIDIFORMES HETEROSTRACANS: AN EARLY RADIATION OF A ‘BOTTOM’ HEAVY CLADE
Review round: 2
Reviewer: 2

Output:
Basic reporting: The authors defends their use of cladistic characters by noting they are only attempting to capture morphological variation without reference to function. They also give more complete explanations of taxa and assumptions.
Experimental design: The methods are explained. That said, I still do not understand the point of comparing diversity of taxonomically relevant character state combinations (as cladistic characters are) to taxonomic diversity, or what this is supposed to show. If the aim is not to capture functional or ecological diversity, but just morphological variation, and this tracks taxonomic diversity as in previous efforts, it is not clear what this study is supposed to demonstrate or why it was done.

Based on one previous study from 2012, the authors suggest that in some contexts, morphological disparity from cladistic characters produces the same signal as morphometric data. Yet they do not test or explain when this occurs, when later studies have produced conflicting results, and what leads them to believe heterostracans are one of those clades in which cladistic characters fully capture variation (even just for the purposes of showing morphological diversity). The head shields of these species are certainly very diverse beyond the traits used for phylogenetic analysis, including various autopomorphic extensions. Do these not contribute to diversity?

Given that, the authors still do not explain why they did not attempt to use morphometrics to more convincingly determine whether they produced the same signal as discrete cladistic characters (given the paucity of previous tests) and to more directly address their question of whether morphological disparity in total matches taxonomic diversity. This study still seems like a minimum effort with minimum relevance.
Validity of the findings: Morphological disparity tracks taxonomic diversity, which is again expected given that taxonomic/phylogenetic differences are driving the signal here (a point which is not fully addressed).

I do not see how the authors infer a surprising 'early burst' pattern given this result - early in this case (pre-mid-Devonian) represents the core of heterostracan evolution history and the peak of their diversity. Likewise, low disparity early in the history of the clade is not unexpected given that there are only 4 taxa. It is entirely possible these four are in fact morphologically disparate in terms of function, ecology, and shape, but all these factors are excluded. likewise, late survivors could be equally disparate to the more numerous heterostracans of the early Devonian along those unsampled axes.

In sum, the limited scope of the analyses, the validity and relevance of which is untested, undermines the ability of the authors to make any conclusions that are not already apparent from raw diversity (i.e. diversity/disparity is low early one, rises in the Silurian, and falls in the mid-Devonian before extinction). There is little value added by the use of morphological data.
Additional comments: No additional comments


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

Input:
Title: CROSS-SPECIES SCREENING OF MICROSATELLITE MARKERS FOR INDIVIDUAL IDENTIFICATION OF SNOW PETREL PAGODROMA NIVEA AND WILSON'S STORM PETREL OCEANITES OCEANICUS IN ANTARCTICA
Review round: 1
Reviewer: 1

Output:
Basic reporting: Professional English is used, but additional editing would be helpful to improve grammar, mostly in the Introduction.

Otherwise, basic reporting is acceptable. I have made some comments on certain portions of the writing throughout, which are included with this review.
Experimental design: The study establishes baseline data for population genetic studies of two Antarctic seabird species. These data are necessary foundations upon which to build more in-depth studies.

Credentials and permits appear adequate.

All methods are well-described, including deviations from published Qiagen protocols, though clarification is necessary on whether siblings were sampled in the case of the snow petrels, and if so, whether this was accounted for in analysis.
Validity of the findings: All results appear sound, though attention should be given to the point I raise in the previous section.
Additional comments: I am including comments that I feel would improve the overall quality of the writing. Thank you for the opportunity to contribute to this 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: CROSS-SPECIES SCREENING OF MICROSATELLITE MARKERS FOR INDIVIDUAL IDENTIFICATION OF SNOW PETREL PAGODROMA NIVEA AND WILSON'S STORM PETREL OCEANITES OCEANICUS IN ANTARCTICA
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript entitled “Standardizing microsatellite panels for individual identification of seabirds’ Snow Petrel Pagodroma nivea and Wilson’s Storm Petrel Oceanites oceanicus in Antarctic” of Pande et al.  have relevant information to monitoring Petrels form long-term in Antarctic region. However, the text  need to be improved in many parts to became clearer and fluid. I do some suggestion, but I recommend to revised by native speaker English.
I did some suggestions about the structure of topics in the text, including delete some parts and change positions odf anothers.
Some parts the authors affirmed that are few studies with Procellariformes (lines 68-69, lines 73-80), being this study a  pioneer with Procellariformes in Antarctica, but there are many genetics studies in Southern ocean. Thus, i recommended that authors change the focus this sentence, thus cited theses studies in Antartctica and  draw attention the scarce studies with Snow Petrel and Wilson Storm Petrel.
Information about Indian Antarctic programme do not should be included in the text, can be included in the end together of permits of the study.
Experimental design: In general, the methods and results were appropriated and well conducted.  The objective of the study included  assessing population genetic structure. However, the present study aim developed a panel of microsatellites  markers, it did not population structure analysis. Thus, i recommend take out population structure of objectives.
Validity of the findings: The results are valid  and important, seem robust and conclusives
Additional comments: Major comments:
1-	Information about Indian Antarctic programme do not should be included in the text, can be included in the end together of permits of the study.
3-	Common names have start initial letter in capital letter Snow Petrel and Wilson’s Storm Petrel, thus fix the text.
Line 1- In the title delete “Standardizing “
The abstract need to be rewritten to be clearer.
Lines 30 -32  I suggest change the phrase . “Procellariiformes are one of the most abundant seabird, occurring from tropical to polar regions.”
Lines 32- 35 Change the sentence “Long-term studies with seabirds in Antarctica Continent is scarce, thus genetic tools to allow recovery population demography, evolutionary history of the species.”
Lines 35-36  I suggest deleted phrased “Under the ‘Biology and Environmental Sciences’ component of the Indian Antarctic programme, long-term monitoring of Antarctic biodiversity is being conducted.” It is irrelevant information and is contradictory with anterior phrase.
Lines 39-40 What is the percentage of amplification success?
Key-word – delete Indian Antarctic programme and Antarctic biodiversity; and include genetic diversity
Lines 58- change “makes” to “make”
Lines 87-89. This part of the text need to be altered, because it is not a reported is a manuscript. Thus, I suggested altered to “understanding distribution, abundance, population dynamics and genetics of Antarctic seabirds it is important to biodiversity conservation of the continent. “
Lines 89-94 – Delete this sentence, is not part of the present study. It is a aim of Indian Programme.
Lines 102- Change “With the broad objective of assessing population genetic structure. We describe a panel of cross-species microsatellite markers” to “The present study aim developed a panel of microsatellites  markers…..” . You did not population structure analysis.
Lines 120 and 124 – delete coordinates word.
Lines 133- 135 – deleted “ as part of the ‘Antarctic Wildlife Monitoring Programme’ under the Indian Scientific Expedition to Antarctica (Expedition nos. 33, 34 and 35).” This information yet is found in Aknowdelege
Line 139-  Change non-destructive to invase samples
Lines 167- 170 – It would be part of discussion.
Line 157_ What is the size of samples (number of individuals sampled) to each of samples and to species?  The information on line 207 to 211 could be to here.
Lines 172-179  It would be after Field Samples. I suggested to one section of Field Sampled, DNA extraction, Primer selection and standardization
Line 215_ delete “see” and “for details”
Line 220- delete  “see” and  “for detailed summary statistics”
Change the order, lines 222-224 ( Overall….. until ….. Wilson’s storm petrel respectively.) before lines 216-222(For Snow Petrel …….. until ……pair of loci)
 Lines 247-248  What the author want said with “petrel and Wilson’s storm petrel are generally lacking in comparison with charismatic species such as penguins”? It is not clearer, it is related with number of studies or diversity index?
Line 249 – 253. The future aims is not part of present study, thus I recommend change the text  “ Markers developed in this study will be extremely important to future Petrels  monitoring to understand the population structure, relatedness, behavior (monogamy, extra-pair paternity etc.) and evolution.”
Lines 108 -114- Permits and ethical clearances, transfer to the end of manuscripts, before Acknowledge


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: CROSS-SPECIES SCREENING OF MICROSATELLITE MARKERS FOR INDIVIDUAL IDENTIFICATION OF SNOW PETREL PAGODROMA NIVEA AND WILSON'S STORM PETREL OCEANITES OCEANICUS IN ANTARCTICA
Review round: 1
Reviewer: 3

Output:
Basic reporting: The writing suffers somewhat in terms of clarity and succinctness.  I’ve provided some guidance for possible editing in the manuscript.

It’s not clear to me why there is an apostrophe after the word seabirds in the title. Also, the title should perhaps be changed to something more descriptive of the work.  A suggestion is:

Cross-species screening of microsatellite markers for use in individual identification in snow petrel Pagodroma nivea and Wilson’s storm petrel Oceanites oceanicus nesting in Antarctica.

The background and introductory material are sufficient to place the study within the marker development field, and literature references are relevant although there are inconsistencies in formatting that should be corrected.
Raw data are shared (thank you very much), although metadata are lacking and some locality information for each sample would be beneficial.
The structure of the paper is appropriate for the journal although I think the formatting for the major headings may be incorrect; the authors should carefully check the instructions to authors.
The figures and tables are relevant; I have provided some notes on the manuscript requesting clarification of certain points in the table.  The figure is not aesthetically pleasing to me but I acknowledge that my art/design background gets in the way of my ability to fairly judge figure composition.

The submission is self-contained, including results relative to the focus of the paper, but there is some reference to population genetics parameters that appear to be assayable in a way that is outside the scope of the work described, which was to screen markers for individual ID in each species.  The objectives of the paper should be followed closely, with reference to future broader uses placed within the discussion.
Experimental design: The research is within the Aims and Scope of PeerJ. The research is fairly well defined and knowledge gaps identified, but the paper would benefit from a specific statement of the objectives and not stray into a broader arena (see prior section).   Original primary research within Aims and Scope of the journal.

I am unable to assess the appropriateness of the ethical treatment of the birds as I did not have access to the referenced letter (Letter no: NCAOR/ANT/ASPA/2014-15/01).  Perhaps I simply didn’t find the correct document  in the submission files.

The methods were sufficiently detailed that those in the laboratory I direct could follow them.  I have provided edits on the manscript where clarity would benefit less experienced readers.
Validity of the findings: The findings appear to be valid as presented.  However, justifying the findings with regard to marker resolution for individual ID could be strengthened by placing the results within the context of the guidelines recommended by Waits et al., or the use of PIDsib only (in the text) justified by some discussion.
I also recommend some discussion about the use of some of the markers (those > 200bp) for individual ID that may be applied to low quality sample types.  It is well known that such markers are more subject to allelic dropout (see Sefc et al. 2003).  One way to test this is to conduct sample reliability tests, such as the use of programs such as RELIOTYPE, and to screen paired high quality and low quality samples collected from the same individual.

Parameter metrics or at least P-values, even if not significant, should be reported (for example, a range of all locus by locus test values of linkage disequilibrium, or overall values or range, can be reported, along with p-values).

Regarding conclusions, the authors should carefully justify their statement that the statistical power for the markers used for the Wilson’s storm petrel is insufficient, whereas the snow petrel is.  Guidance can be found in Waits et al., referenced in the manuscript.
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: CROSS-SPECIES SCREENING OF MICROSATELLITE MARKERS FOR INDIVIDUAL IDENTIFICATION OF SNOW PETREL PAGODROMA NIVEA AND WILSON'S STORM PETREL OCEANITES OCEANICUS IN ANTARCTICA
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors have done much to improve the writing in the manuscript, in accordance with my previous comments as well as those of the other reviewers. There are however a few more points that should be addressed:

I noticed that much of the methods and results were primarily written in passive voice. The majority of journals currently request active voice, at least in the methods. While the author guidelines for this journal require ‘Established norms of academic writing within [our] field should be used’, there is not a specific mention of this particular point, so I will leave the validity of this comment up to the Editor.

Throughout the introduction, I noticed the use of the term "procellariiforms" to describe members of the order Procellariiformes, which seems appropriate when looking at other papers on this group, but here the lower-case form "procellariiformes" is also used, which seems inappropriate. Please revise to use the capitalized form when describing the order as a whole, and the first term I use in this comment when describing members of the order.

I have a few small comments on the text, which are detailed in the final section.
Experimental design: All details of experimental design seem appropriate, and are acceptable to me given the satisfaction of the other reviewers, who previously shared more detailed comments than my initial review.
Validity of the findings: As with experimental design, this section appears valid.
Additional comments: It appears that the permit information now provided by the authors consists of a denial, unless the sampling recommendation at the bottom of the document is sufficient to permit sampling without a separate approval for Broknes. Also, from what I can ascertain of Antarctica's geography, the two localities described in the permit letter are both found within the lower red box in Figure 1 - is there a separate permit for the area in the upper box? It seems like additional documentation is required.

Here are a few in-text edits to address. Line numbers refer to those in the clean revised PDF.

Line 64: Procellariiformes should be capitalized.

Lines 65-66: Change "species group" to something like "avian taxa"

Line 72: Add "the" after "Research on"

Line 74: Delete "few"

Line 210: "value was found" should be "values were found"

Line 225: For formality, "might not be robust enough" could be changed to "may not be sufficiently robust"

Lines 230-232: The sentence beginning with "Nevertheless" basically repeats lines 217-218 and can be deleted.


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: CROSS-SPECIES SCREENING OF MICROSATELLITE MARKERS FOR INDIVIDUAL IDENTIFICATION OF SNOW PETREL PAGODROMA NIVEA AND WILSON'S STORM PETREL OCEANITES OCEANICUS IN ANTARCTICA
Review round: 2
Reviewer: 2

Output:
Basic reporting: The manuscript is well written and was conducted with two important Antarctica Seabirds, the results opens up perspectives for other studies. I consider that references are adequate, it show one figure with good quality and one table that authors included all suggestion of reviewers.
Experimental design: This study is original and brings important information about two flying species, Snow Petrel and Wilson's storm petrel, that there are poor knowledge about its genetic population. The markers standardization in this research can be used in others studies around Antarctica continent. The methods were well conducted and I believe that can replicate in other laboratories
Validity of the findings: The outcome of this study can be used by others scientific groups around Antarctica continent. The analyses were robust an appropriated, and the authors included several suggestion did by reviewers, improving the new version.
Thus, i have notthing to add.
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: LIVING IN THE INTERTIDAL: DESICCATION AND SHADING REDUCE SEAGRASS GROWTH, BUT HIGH SALINITY OR POPULATION OF ORIGIN HAVE NO ADDITIONAL EFFECT
Review round: 1
Reviewer: 1

Output:
Basic reporting: The language of the manuscript requires a lot of work. I am wondering if the authors accidentally submitted a wrong version of the manuscript, as in some places it is obvious that text is missing. For example L213-215 and L247-248. Some of the abbreviations were not introduced (L194-195, Table 2), some abbreviations were not used consistently (e.g. aboveground and belowground were sometimes abbreviated as AG and BG, and other times A and B and in other places written out). Also some of the results described in the text or statistical tables do not match with the information in the figures. For example, the shoots could not have been 121% longer (L222) as based on the Fig 2F, these were ca 20-30% longer. Also if the figures really are mean ±SEM, I have hard time believing the statistical analyses. As for example the error bars for in Fig.2C overlap consistently, and the 95% CI should be much larger that SEM, I cannot understand how the authors managed to find these tiny differences statistically significant.
Experimental design: My biggest concern is the experimental design used in both experiments. In its current form, it seems that the authors only had one replicate per treatment and treatment combination. It seems that they had all the ”replicate” plants in the same unit/aquaria for the combined treatment effects. This means that they have used individual plant units (2 connected ramets) as replicate in the statistical assessment of the results. However, these units are merely pseudoreplicates, and they should have used several experimental units with plants to replicate for each treatment and treatment combination. In the second experiments, the design is described as nested split-plot design, with population as partly nested (split-plot) under emergence, which then should be nested under salinity. However, based on the description of the statistical testing, this is not how it was analyzed. Additionally, only having one tray of plants per treatment combination, testing the results is not even possible. Not even with the potential hidden replication due to use of several salinities. However, as the material and methods section was not very clearly written, I am not completely sure I understood it correctly. With this complicated design, I suggest the authors add an additional figure illustrating the desing for both experiments.
Validity of the findings: See point 2. Due to the most likely faulty statistical analyses, I cannot assess the validity of the findings.
However, if the statistical methods would be ok, the Discussion section would need clearly more work. Now the Discussion is very superficial and instead of discussing the results in a larger context, mainly turns the discussion to what was not tested in the experiments. The authors end up drawing their main conclusion about something they did not test at all in this experiment.
There are interesting findings in the paper, and I believe the ms would be much more interesting if the authors concentrated more on these. (See general comments below)
Additional comments: Reviewer comments for manuscript ”Living in the intertidal; desiccation and shading reduce seagrass growth, but high salinity or population of origin have no additional effect” (#22711) by Suykerbuyk et al.

The manuscript reports findings from two experiments testing how desiccation together with other potentially affecting factors (shading, salinity and plant population) affect the growth and morphology of the seagrass Zostera noltii. While the findings, and especially the lack of interaction of different tested factors, are interesting, I have several concerns about the manuscript, and cannot recommend it to be acceptedwithout further knowledge on the experimental design. Currently, the material and methods section is lacking some important information about the methods and design used. Even if the design turns out to be ok, the manuscript requires soem major revisions.

Firstly, my biggest concern is the experimental design used in both experiments. In its current form, it seems that the authors only had one replicate per treatment and treatment combination. It seems that they had all the ”replicate” plants in the same unit/aquaria for the combined treatment effects. This means that they have used individual plant units (2 connected ramets) as replicate in the statistical assessment of the results. However, these units are merely pseudoreplicates, and they should have used several experimental units with plants to replicate for each treatment and treatment combination. In the second experiments, the design is described as nested split-plot design, with population as partly nested (split-plot) under emergence, which then should be nested under salinity. However, based on the description of the statistical testing, this is not how it was analyzed. Additionally, only having one tray of plants per treatment combination, testing the results is not even possible. Not even with the potential hidden replication due to use of several salinities. However, as the material and methods section was not very clearly written, I am not completely sure I understood it correctly. With this complicated design, I suggest the authors add an additional figure illustrating the desing for both experiments.

Secondly, the language of the manuscript requires a lot of work. I am wondering if the authors accidentally submitted a wrong version of the manuscript, as in some places it is obvious that text is missing. For example L213-215 and L247-248. Some of the abbreviations were not introduced (L194-195, Table 2), some abbreviations were not used consistently (e.g. aboveground and belowground were sometimes abbreviated as AG and BG, and other times A and B and in other places written out). Also some of the results described in the text or statistical tables do not match with the information in the figures. For example, the shoots could not have been 121% longer (L222) as based on the Fig 2F, these were ca 20-30% longer. Also if the figures really are mean ±SEM, I have hard time believing the statistical analyses. As for example the error bars for in Fig.2C overlap consistently, and the 95% CI should be much larger that SEM, I cannot understand how the authors managed to find these tiny differences statistically significant.

The authors describe that they did model selection for the glms and lme’s and removed any non-significant main factor. In table 1 and 2 they, however, include all the factors. It is unclear if these are from the original model, or if they combined these for the different factors.
Further, the main findings according to the authors is that shading reduced plant growth, but increased aboveground biomass. It is clear from the data that this is due to increaed investment in aboveground biomass compared to belowground biomass. This reduced belowground investment and shoft to aboveground production is not considered at all, which in my opinion is one of the most interesting findings in the manuscript.

Some more minor comments:
Synergistic is not the synonym for interactive effects. Stress effects can be either interactive (e.g. synergistic or antagonistic) or additive. The terminology should be used consistently throughout the manuscript.
L28-29. PSU is no longer used for salinity.
L46-49. The authors did not test sediment properties, so haw can their main conclusions be about that?
L81. Also when desiccated or only submerged?
L106-109. How were the day length effects? These should also be reported if they are mentioned in the text
L111. Additive effects instead of ”they add-up”. Same throughout the manuscript
L115. What is referred to by ”these effects”
L118. What is referred to by ”They”?
L118-119. These information belong to M&M, not introduction
L119-123. No morphology-related hypoteses? Compare statement on L113-115.
L130. How were these stored? Transplanted in sediment, or kept freefloting in tanks? Photoperiod? And how were they transported to the location? Same question goes for the experiment 2 plants.
L135. Does using untreated sediment mean that there were infauna in the experiments?
L151. How was the photoperiod in relation to desiccation?
L160. How was the initial WW quantified? For each specific plant?
L170-171. Reference?
L186. N=12 per population or in total?
L193 & 199. An experiment is not analyzed, the results are
L199. If the authors want to test general population effects, then population should be random factor, not fixed.
L213-215. Text missing
L231-232. These results are not described for desiccation anywhere
L236. Is 22% referring to the initial plant size differences? I suggest considering using relative data for size and bm for different populations, to easier see differences in plant responses, instead of their different original and final size. Also, the initial differences should be given in material and methods section.
L244-245. These results are not shown anywhere
L271-276. Not really that relevant to this study. Teh authors should not try to simply discuss what differs between lab and field, but to try to discuss how and why they obtained results like they did and how these could reflect in more natural conditions.
L285-286. Z. Marina results here not relevant
L297-298. How is salinity of 2-25 narrower than salinity of 15-35?
L323-325. I suggest that if the authors want to bring discussion to the differences between sites (Should be introduced in M&M, instead of Discussion), they should refer to newer literature. Water clarity can certainly change a lot during 24 years.
L335. Personal observations of the last author?


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: LIVING IN THE INTERTIDAL: DESICCATION AND SHADING REDUCE SEAGRASS GROWTH, BUT HIGH SALINITY OR POPULATION OF ORIGIN HAVE NO ADDITIONAL EFFECT
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript by Suykerbuyk and co-workers aims to assess the effects of desiccation and light limitation in affecting growth and morphology of intertidal populations of the seagrass Z. noltii. Moreover, authors seek to understand the differential effects of salinity range on populations pre-adapted to different salinities.
In general, I found that the manuscript has some problems that impair at the moment the publication in a high rank journal such as PeerJ.
First, it is not clear why authors tested the possible synergic effect of low light and desiccation. When exposed, plants experience higher light that can really represent a further stressor. Low light can negatively affect plant growth, but it does not occur at the same moment when desiccation occurs.
Second, the experimental setup is not well explained and makes it difficult to evaluate results. A figure clearly detailing the experimental design should be presented for the two experiments.
Third, the interpretation of some results is not clear.
Experimental design: In order to achieve their goals, authors perform two distinct experiments in a closed aquarium system and measure growth and morphological traits after 2-3 months of treatment. The experimental design is not well explained, which also impairs a correct evaluation of the appropriateness of the statistics utilized. For example, in exp 1 it is said that 20 EPUs were utilized per treatment and each EPU was planted individually in a separate tray. Hence, they were placed in aquaria (how many EPU?). Are the aquaria representing the treatment? It is to say 20 EPUs per aquarium? Or are the aquaria representing the n=4 replicates and 5 EPUs were placed in each of four aquaria used for each treatment? Since half of each aquarium was shaded by filters, how many were shaded and how many represented the control? If the number of EPUs per aquaria is 5, the treated and the control ones cannot be of the same number.
Maybe 20 EPUs were planted in each of four aquaria utilized for each treatment. In this case, total number of EPUs per treatment should be 80 and not 20.

In exp. 2, the experimental setup is apparently clarified in the raw data provided with the submission. Nevertheless, the scheme does not correspond to the possible setup explained in the text. At line 174-175 it is stated that: “In this experiment, 2 containers per salinity treatment were used, in each container 2 aquaria were placed, and within each aquarium 3 pseudoreplicates for each population of origin.” In the raw data 6 containers are represented, with 4 aquaria for each container.
Moreover, here it should be explained how the acclimation period was performed.  Were plants acclimated to the same salinity conditions? For how long? Length of the acclimation phase is very important in common garden experiments.

The species is well known to tolerate high salinity ranges and the selected populations grow in a salinity range that is within the tolerance limits of the species (two populations naturally experience average salinity of 29.5-29.9, while one grows at a salinity of 34.7). How were the experimental salinity levels decided?

Since the nested experimental design is not clear, it is not possible to evaluate the appropriateness of the statistics (the fixed and random factors, etc…) into detail.
Validity of the findings: Results are well presented and figures are all correct and necessary. In my version, tables are not well formatted.
Main conclusion of experiment 1 is that both light reduction and desiccation impact seagrass growth, with light affecting also the BG/AG ratio and leaf length. Plants are not able to invest in the below ground tissue when light is limiting, and invest more in the photosynthetic tissue. The two stressors do not show significant interaction.
In the second experiment salinity does not have any effect on shoots growth and morphology and only desiccation produced significant results. Plants form the Northernmost population, the one with higher salinity, were bigger and this reflects all along the experiment.
Line 213; there is something wrong at the beginning of the sentence
Line 232: delete: “Z. noltii origin”

At the beginning of the section, authors discuss the effect of emergence, desiccation, in comparison with literature data. Hence they state that the effect of shading adds up to desiccation. In my opinion, the additive effect is not clear. It looks like the difference between light and shaded plants (see RGR) decreases with increasing exposure and is probably not significant at 6-8hr.
In line 267 it is said that “shading further reduced the negative effect of emergence”. Is this what authors wanted to say? If this is the case, low light counteracts the negative effects of desiccation. This is what should theoretically happen, but it contrasts with the main conclusions driven in the paper.
According to the fact the low light is not a clear stressing factor for the upper limit of plants and is not fully appropriate to be tested together with desiccation, in the conclusive paragraphs most of the speculation is about the effect of low light in determining the depth distribution of the species.  Although this is surely interesting, it is not really in line with the goal of the work.
Line 247 and 266: conforming our hypothesis…
Line 268: the additive effect is not clear. It looks like the difference between light and shaded plants decreases with increasing exposure and is probably not significant at 6-8hr.
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: TIME TO GET OUR FOUR PRIORITIES RIGHT: AN 8-YEAR PROSPECTIVE INVESTIGATION OF 1326 PLAYER-SEASONS TO IDENTIFY THE FREQUENCY, NATURE, AND BURDEN OF TIME-LOSS INJURIES IN ELITE GAELIC FOOTBALL
Review round: 1
Reviewer: 1

Output:
Basic reporting: The management of the risk of injuries is a very important question. Understanding the extent of the injury problem is the first port of call in preventing sports injuries.  The present study aimed to investigate the speed at which elite Gaelic soccer players suffer different injuries due to loss of time during the game and training activities.
The article includes sufficient introduction and background to demonstrate how the work fits into the broader field of knowledge
Experimental design: The investigation must have been conducted rigorously and to a high technical standard, in conformity with the prevailing ethical standards in the field.
Validity of the findings: The data is statistically sound and controlled.
Additional comments: After careful consideration, I have decided that the manuscript meets criteria for publication and must consider the manuscript for publication.