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: IDENTIFICATION AND FUNCTIONAL ANALYSIS OF LECRLK GENES IN TAXODIUM ‘ZHONGSHANSHAN’
Review round: 1
Reviewer: 2

Output:
Basic reporting: In this paper the authors identified the 297 putative LecRLK genes from a Taxodium 'Zhongshanshan'(?) and classified the genes to 3 types including 155 G-type, 140 L-type and 2 C-type based on the cladistics analysis of gene sequences. This kind of study is relatively rare in conifers and it worth to be published in PeerJ. But several revisions are required before acceptance of the manuscript to PeerJ.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: I point out two major issues. The first issue can be revise easily. But, the second issue requires reanalysis of data and proper graphic works for revision.

First, the plant name, Taxodium hybrid 'Zhongshanshan', is not acceptable names under either the current botanical nomenclature or the cultivar nomenclature. The name 'Zhongshanshan' looks like a cultivar name because authors used in a single quotation mark. I am not sure the origin of this cultivar. Is it a di-specific hybrid or a tri-specific hybrid? Is it a registered cultivar name? The author should clarify or explain more details about their research material with the information of the hybrid origin. The T. hybrid 'Zhongshanshan' (line 126, 143 and many other places) also not usable name, too. The genus name can’t be abbreviated without accompanying specific epithet. Please consult the right expression of cultivar name to knowledgeable botanist in nomenclatural field.

Second, the authors constructed a cladogram of 297 LecRLK gene sequences using NJ tree reconstruction methods. The cladogram (not phylogram, the term of plylogram throughout manuscript should be change to cladogram because no polarity determination in the tree). Fig. 1 simply show branching patterns of genes. This circle cladoram looks nice to see, but there is no information for the branch lengths. Therefore, the classification of group and subgroups based on the branching patterns are totally invalid. In order to use the trees to classifying the gene groups, the NJ tree with branch lengths should be presented in Fig. 1 rather than the current circular cladogram. Then, the unrooted tree should be oriented using the midpoint rooting method or the longest branch rooting method because there is no outgroup or sister gene groups. The subgroup classification of G-type and L-type in Figure 2 should be re-rooted by the sister groups such as C-type genes. In addition, Fig 3 and 4 also need to re-oriented by proper methods. I strongly recommend to authors to change the trees in Figs. 1 and 2 to the NJ distance trees rather than the branching pattern. The NJ distance tree can be presented with supporting values, 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: IDENTIFICATION AND FUNCTIONAL ANALYSIS OF LECRLK GENES IN TAXODIUM ‘ZHONGSHANSHAN’
Review round: 1
Reviewer: 3

Output:
Basic reporting: The authors report on the bioinformatic identification of putative Lectin receptor-like protein kinases (LecRLK) from the transcriptome of the hybrid species Taxodium hybrid ‘Zhongshanshan’, a water-tolerant tree that it is being used on China for aforestation. LecRLKs have been reported for other species but only for a handful of woody plants. These kinases are important on processes of tolerance to biotic and abiotic stresses as signal transductors. In addition to the identification of the putative LecRLKs, the authors also searched on the transcriptome for co-expressed transcription factors (TFs) that may be associated to the LecRLKs and test the expression patterns of 15 LecRLKs on ABA, salicylic acid, mannitol, NaCl, and low temperature.

This manuscript is well organized and details the methodological plan followed.

To the best of my knowledge, the Introduction and background cover the relevant literature.

There are some methodological problems that detract from the study on its present form:

1. Although the HMM profiles are a powerful method of identifying putative proteins, its results need to be curated before further analyzed. HMM profiles identify proteins by a probabilistic metric so sometimes proteins that do not contain full domains can be reported as valid results.
2. The subcellular localization analysis needs to be complemented with at least a second prediction tool.
3. The manuscript should be thoroughly proof-read to improve its English quality. Just to cite a couple of problems, past and present tenses are mixed as well as singular and plurals, and the order of adverbs, adjectives, and nouns.
Experimental design: As noted in the previous section, the methodology is, in general, of sufficient clarity and detail, but care needs to be taken on the reporting of the HMM and PSORT results.
On lines 189 and subsequent, authors indicate that they found (using profile PF00069) 1331 unigenes predicted to contain a protein kinase domain. These unigenes are filtered to remove those without complete ORFs, transmembrane domains, and LecRLK domains. Nevertheless, on lines 226-227 it is stated that at least five L-type ThzLecRLKs lack a kinase domain. Unless this is a missing second kinase domain these putative LecRLKs cannot be such. A diagram of the typical expected G-type, L-type, and C-type LecRLK domains should be included to aid on the understanding of the findings (in addition to figure 3). Also, the resolution of figure 3 is not enough to read the labels.

With respect to the results of the PSORT subcellular localization of the putative LecLRLKs, it has to be noted that this is a prediction tool that is not 100% accurate. I would recommend using at least a second localization tool (for example, http://www.jci-bioinfo.cn/pLoc_bal-mEuk/) and report the results that agree for both tools.

Although most of the methodology is very detailed, there are some omissions. An important one is regarding the construction of the multiple alignment and the phylogenetic tree. The authors stated that they used the MAFFT algorithm (which is a very good choice) but neglected to inform which of its modes was used. Given the nature of the different domain architectures of the L, G and C RLKs, the best choice would be to use the E-INS-I mode (suitable for multiple conserved domains and long gaps). If this mode wasn’t used the multiple alignment could contain mistakenly aligned domains that would impact on the phylogenetic tree. I would suggest the authors include, as supplementary material, the full alignment on a suitable text format (FASTA, clustal, etc.).

My last suggestion is about the presentation of results on the discussion. On lines 329-339 the authors compare the number of LecRLKs found in this study to previous ones. It would be useful if these numbers could be related to the number of proteins and/or genome sizes of the mentioned species. The authors actually mention that Taxodium has a large genome size (20Gb). Maybe presenting these numbers as a percentage of estimated protein-coding genes could aid on visualizing the expansion of these kinases (since C-type LecRLKs still remain very limited).
Validity of the findings: Most of the findings presented are supported by the methodology and results. Care needs to be taken to filter the putative LecRLKs and the corresponding subcellular localizations. If the multiple alignment is redone using the E-INS-I mode and the phylogenetic tree groupings change, these changes should be taken into consideration for the results and discussions.
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: EVALUATION OF THE SOCIALLY EVALUATED COLD-PRESSOR GROUP TEST (SECPT-G) IN THE GENERAL POPULATION
Review round: 1
Reviewer: 1

Output:
Basic reporting: The study presented here aimed to determine the effects of the socially evaluated cold-pressor test (SECPT) on acute stress responses (subjective stress perception, saliva cortisol, salivary alpha-amylase) in groups. Performing this test in small groups of the "broad population", including participants of different sex, age, with different socioeconomic background, etc., and correcting measurements of stress responses for these and other covariates, would be highly economic relevant by enabling the determination of acute stress responses in a high number of people at once.

In general, the manuscript is very well written and in very good English.
The authors cite a high number of relevant literature, provide all relevant background information in the introduction, and relate their results to previous findings without being too speculative at any stage.
The raw data is supplied as supplementary file.

There are just a few points (see general comments), which might help improving the introduction and discussion.
Experimental design: The manuscript presents primary research. The research questions are well defined, relevant and meaningful. I think the experiment was in general well designed and also shows that the SECPT can be performed in a very short time frame and in a high number of participants, which definitely proved the validity of the SECPT-G.
The study has been approved by the responsible ethics committee.

The methods are well described, there a just a few minor concerns that are adressed below  (see general comments).

However, I have some major concerns regarding the analyses (see validity of the findings below).
Validity of the findings: Although the results definitely confirm the biological/psychological validitiy of the SECPT-G, there are some major concerns regarding the analyses and the results:

One thing that confuses me overall is that the variances (standard error, standard deviation, confidence interval ?) for all parameters presented in figure 1 are seemingly not the same as presented in the text. The means presented in the text and in the figures are obviously the same, but the variances presented in the text are much higher than in the figures. Please either explain in the figure captions, which values are shown, or at least in the statistics section of the methods, which variances you provide in the figures and in the text.
Similarly, also the Eta-squares values for the cortisol and sAA analyses do not fully match when comparing the values presented in the text and in table 1; see for example eta-square for cortisol analysis in the text (= .23; line 194/195) and in table 1 (= .37). Do these values result from different analyses? If the respective values should be the same then I would recommend presenting them either in the text or the figures/table. This also applies to the further analyses, when covariates were included.

How many rmANOVAs were calculated? Based on your "Statistical analysis" section in the Methods as well as different p- and eta-square values for the main effect of time in table 1, I assume that new rmANOVAs on cortisol and sAA measurements were performed for each single covariate, so in total 11 additional rmANOVAs for cortisol and 11 additional rmANOVAs for sAA, corresponding to the 11 covariates. If I am right, this would be a very unusual way of analysis. In order to detect any relevant effects of covariates, the usual analysis would be to include all covariates in the model at once, therefore correcting for all the other covariates (when calculating type 3 sum of squares), and perhaps removing non-relevant predictors/covariates from the model (for instance based on the Akaike information criterion). Some covariates may only show significance after correcting for others, or even do not show significance anymore. Including all possible covariates/predictors at once would be highly important to extract only the relevant ones, because they all apply to the participants at the same time and might even be related to each other (e.g. physical activity and BMI). Did you control for this? Please clarify, how the data were analyzed.

Furthermore, were all covariates include as numerical/continuous variables (e.g. 0,1,2,3,...)? In case of graduation or profession, these variables definitely have to be included as categorial predictors ("groups") in the analyses, because it cannot be assumed that the measurements of stress responses change linearly with the numbering, but differences between these "groups" (e.g. student, employee, retired, other) have to be considered in any way. Please also clarify this.

Additionally, in line 139 it is said that it was "(...) the aim to introduce a competitive situation". Could it be possible that some kind of "winner-loser-effect" affected your measurements of stress responses? Perhaps, a participant who pulled his/her hand out of the water earliest in the group (the "loser") would show a different stress response (presumably a change in cortisol concentrations) compared to someone who had an immersion time of 3 minutes in the same group (the "winner"). In this case not only the own immersion time of a participant might affect his/her stress response, but also the own immersion time in relation to the immersion times of the other participants in the group. Is it possible/meaningful to include this in the analyses too?
Additional comments: Minor concerns/comments

Introduction

The provided information for effects of demographic, socioeconomic and lifestyle factors on stress responses in lines 54-70 is somehow just a "listing". I think this section should be re-written and/or shortened and the findings/information should be set in relation to each other.

Methods

In the "Participants" section of the Methods you provide relevant information, but how most of these data were recorded is stated afterwards in the "Procedure" section. Perhaps, it would be better to describe the general procedure first.
Line 173: What do you mean with "If necessary, Cohen's d was corrected (...)" ?

Disussion

In the "Participants" section of the Methods you provide relevant information, but how most of these data were recorded is stated afterwards in the "Procedure" section. Perhaps, it would be better to describe the general procedure first so that it clear from the beginning, where these data come from (e.g. measurements, questionnaires, etc.).

Line 173: What do you mean with "If necessary, Cohen's d was corrected (...)" ?


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: EVALUATION OF THE SOCIALLY EVALUATED COLD-PRESSOR GROUP TEST (SECPT-G) IN THE GENERAL POPULATION
Review round: 1
Reviewer: 2

Output:
Basic reporting: In general the structure is good. Some minor changes:
- line 20 - misses (SAA)
- line 33 please explain better why provoking stress responses in subjects is an important tool in bio-behavoral research
- line 47 - please explain what "strong" means; this is not a good word; what happen to this physiological markers during stress (e.g. HRV decreases; BP increases...) ?
- line 94 - The correct way is: the sample size is 96 (N=96); the same for line 97.

The English needs to be reviewed by a professional.

The literature references are outdated.
Experimental design: The methodology is well described

Just one question
Did you conduct a normality test before choosing the parametric test ANOVA?
Validity of the findings: Data is robust, and conclusions are well stated.
Additional comments: Very interesting paper for stress research area. The sample is robust and the results are well presented and discussed.


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: EVALUATION OF THE SOCIALLY EVALUATED COLD-PRESSOR GROUP TEST (SECPT-G) IN THE GENERAL POPULATION
Review round: 1
Reviewer: 3

Output:
Basic reporting: The manuscript is clearly written and easy to follow.

The study rationale is clearly addressed.
Experimental design: 1. The research question is well defined.

2. The experimental procedures should be clarified.
2.1. Methods described is unclear. Please describe the assessments of demographic variables and lifestyle factors in greater detail. Also, please provide validity and reliability data of the TICS-SSCS and IPAQ-short form. In a related note, how you 1) defined smokers and non-smokers? 2) how BMI was assessed? by self-reported or following standard laboratory procedure?
2.2. The reporting of activity levels is problematic. When using the IPAQ as measure of activity levels, we usually report the results using metabolic equivalents (METs) per week, not metabolic minutes per week. Please clarify this.

3. The current study did not include a control group. As noted by the authors themselves, there were other factors that could have also introduced stress response, the authors are encouraged to have reflection on this issue.
Validity of the findings: The reviewer has several concerns about the validity of findings.

1. Did the authors perform a priori power calculation to determine the sample size?

2. Do BMI norms change by age? If so, how the authors deal with this matter?

3. Participants were asked to refrain from alcohol for only 2 hours before experiment or to consume no more than two drinks (which is pretty vague). As the half-life of alcohol could be longer than 2 hours, depends on the amount of consumption, the 2-hour restriction is not rigorous enough. In a related note, participants were not refrained from caffeine before experiment, this is also problematic as caffeine is a SNS stimulant.

4. The authors reported ethnic data but did not make use of them. It might be interesting to look at whether ethnic affects the results.

5. Participants were asked to fill out several questionnaires between t1 and t2 measure points. Is it possible that filling out these inventories affects following sAA/cortisol measures in t2?
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: EVALUATION OF THE SOCIALLY EVALUATED COLD-PRESSOR GROUP TEST (SECPT-G) IN THE GENERAL POPULATION
Review round: 2
Reviewer: 1

Output:
Basic reporting: The manuscript is very well written and the English was further improved.
Additional literature was included to provide even more background.
All tables and figures are clear, raw data is provided.
The conducted changes definitely improved the manuscript's quality.
Experimental design: The manuscript presents primary research, the research questions are well defined, relevant and meaningful.
The experiment was well designed, the conducted changes to the methods section further improved the clarity on how specific procedures, measurements, and analyses were performed.
The study has been approved by the responsible ethics committee. All relevant information with regard to ethical issues are provided.
Validity of the findings: The authors performed a variety of additional analyses (additional RM-ANOVAs, Power analyses, etc.) in order to confirm that the SECPT-G can be performed in a general population based on significant HPA-axis/cortisol responses.
The findings and conclusions are definitely valid and are linked to original research questions.

The authors responded to all raised concerns adequately and answered all my questions.
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: EVALUATION OF THE SOCIALLY EVALUATED COLD-PRESSOR GROUP TEST (SECPT-G) IN THE GENERAL POPULATION
Review round: 2
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The authors have addressed all my concerns. I am now satisfied with 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: NO EVIDENCE FOR NEGATIVE IMPACTS OF ACUTE SULFOXAFLOR EXPOSURE ON BEE OLFACTORY CONDITIONING OR WORKING MEMORY
Review round: 1
Reviewer: 1

Output:
Basic reporting: The work presented by Siviter et al. titled " No evidence for negative impacts of acute sulfoxaﬂor exposure on bee olfactory conditioning or working memory" is of great interest and fits well the scope of the journal. In my regard, the manuscript is well structured. Since English is my second langue, I don’t have any comment on writing of this manuscript.
Experimental design: The methods are adequate and the results clearly presented.
Validity of the findings: Author found that not all neonicotinoids have the same effects on bee cognition. The result showed that other mechanisms might underlie the impact of sulfoxaflor on bumblebee colony fitness. It also reminded us more indexes should be accounted in evaluating impact of sulfoxaflor or next generation neonicotinoids on non-target organism.
Additional comments: No 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: NO EVIDENCE FOR NEGATIVE IMPACTS OF ACUTE SULFOXAFLOR EXPOSURE ON BEE OLFACTORY CONDITIONING OR WORKING MEMORY
Review round: 1
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: I think these two experiments are well thought-out, thorough and highly appropriate for publication in PeerJ. My two main queries would be whether the authors measured other behavioural measures in experiment 2 that might be affected by the pesticide aside from learning, for example time spent foraging or movement patterns? It seems like a rich data set and so it would be interesting to know if any behaviour at all seems to be affected by the treatment. If other measures have been addressed, it might be worth including this, even just in the supplementary material. My second main query is about whether another statistical test could have been used in the first experiment (details below). Other smaller comments are listed below.

Line 94: Remove comma after “acute”
Line 98-99: isn’t the RAM not only a measure of working memory, but specifically spatial working memory? I’d be specific here, since it seems that STM could also be captured in the PER assay.
Line 107: “hypothesised” should be “predicted”
Line 107-109: it would be good to hear more about the specific mode of action here and why this is thought to affect learning performance
Line 115: 50% sucrose by weight or by volume? – I think Brix is usually reported as degrees Brix rather than a percentage?
Line 156: was the sucrose reward offered to the bees via a pipette?
Line 169: were all three size measures used or was an average taken? Also I think it would be good to mention why you’re measuring bee size and how you expect that it might affect results.
Lines 145-146: did the number of bees that did not consume the solution vary by treatment?
Lines 171-172: did the number of bees that did not respond here vary by treatment?
Lines 188-190: Wondering why you don’t look at binary response (0/1) (for a given bee) over the 15 trials, including ‘trial’ as a fixed factor (and bee as a random factor) using a GLMM with a binomial distribution? It seems like you might get more information out of your data this way, rather than reducing it to the variables listed?
Line 191: shouldn’t bee size be a covariate here rather than a fixed factor?
Line 204: do you mean mg of pollen?
Line 233 section: I think it would be good to report how long each trial lasted and the inter-trial interval in this section if this isn’t reported elsewhere?


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: NO EVIDENCE FOR NEGATIVE IMPACTS OF ACUTE SULFOXAFLOR EXPOSURE ON BEE OLFACTORY CONDITIONING OR WORKING MEMORY
Review round: 1
Reviewer: 3

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: It was delightful to read such interesting and well conceived manuscript. It is very well written and brings valuable information about potential impacts of a new insecticide on bees, the most important pollinators worldwide.


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: NO EVIDENCE FOR NEGATIVE IMPACTS OF ACUTE SULFOXAFLOR EXPOSURE ON BEE OLFACTORY CONDITIONING OR WORKING MEMORY
Review round: 1
Reviewer: 4

Output:
Basic reporting: The manuscript, "No evidence for negative impacts of acute sulfoxaflor exposure on bee olfactory conditioning or working memory" by Siviter et al. addresses a very important issue regarding the sublethal effects of insecticides on olfactory conditioning performance and working memory performance of honeybees and bumblebees. The research was thorough and the findings were convincing. The paper wrote well and clearly. I think the manuscript can be published after minor revision.
Experimental design: More details regarding bumblebee colonies should be provided. These colonies are provided by a company, but what were the rearing conditions? These colonies are from the UK? Which localities?
Validity of the findings: The figures text could be in larger font size.
Additional comments: The title could express a curiosity regarding this investigation, and not include an affirmative sentence about the main evidence found.

For instance: There are negative impacts of acute sulfoxaflor exposure on bee olfactory conditioning or working memory?

Or

Negative impacts of acute sulfoxaflor exposure on bee olfactory conditioning or working memory


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: POLLEN REPORT: QUANTITATIVE REVIEW OF POLLEN CRUDE PROTEIN CONCENTRATIONS OFFERED BY BEE POLLINATED FLOWERS IN AGRICULTURAL AND NON-AGRICULTURAL LANDSCAPES
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript is clearly written and structured and it is easy to follow the authors’ rationale and findings. I have suggested some additional references which might be included in my general comments below. I had some trouble with the formatting of the raw data file, so it wasn't possible to examine this in much detail.
Experimental design: The database is a useful resource and though, as you acknowledge, there are shortcomings in using only crude protein content as a measure of nutritional quality, the data will be of assistance in planning nutritional studies, agri-env schemes etc. and hopefully can be built up on in future if data for other macronutrients becomes more widely available.

In the analysis did you use raw data from the cited papers, or the averaged values for each species?

The rationale for comparing wild versus cultivated plants is fairly obvious, but the comparison of wild flowers versus ‘weeds’ needs more justification, since in reality there is overlap in these categories.
Validity of the findings: I question why you have chosen to publish the nectar and pollen results separately. Both resources are important for bee nutrition, and for those plant species where you have data on both matrices it would be interesting to compare and calculate the overall nutritional quality of a species. In terms of provisioning bees in agricultural landscapes, while some plants may provide a poor pollen source, this can be compensated by a good nectar supply or visa versa, so when making recommendations as you do in your discussion, it would be best to consider both floral rewards where possible, and I feel this would make your conclusions stronger and more informative.
Additional comments: Introduction:
Line 41: primarily
Line 58: Not all bee species will visit a particular crop, so weeds/wild flowers are (in theory) also providing alternative, more appropriate/attractive foraging sources during crop flowering, as well as extending the flowering period.
Line 60: Consider also citing Wood et al. (2017) J. Applied Ecology
Line 63: You should probably explicitly mention that pollen protein content is highly variable between species e.g. Roulston & Cane (2000) Eco Monographs
Line 82: See also following papers, among others, on solitary bee nutrition; Vanderplanck et al. (2014) PLoS ONE; Haider et al. (2013) Fun. Ecology; Eckhardt et al. (2014) J. Animal Ecology
Line 84: Lipids seem to be important, as well as the ratio of protein to lipids e.g. Vaudo et al. (2016) PNAS, JEB
Methods:
Line 115- do you mean strictly if pollination has been observed or if pollination and/or visitation was observed?
You could also include data from Fowler et al. (2016) Insect Conservation & Diversity
Results:
Figure 1- clarify in the legend what N refers to- presumably species, but would be good to include the number of genera too in each category as there is likely some co-variation in protein content
Figure 2: Why are some genera listed in red?
Discussion:
Interesting that Senna and Solanum have highest pollen protein concentration- both have poricidal anthers to restrict collection/wastage of pollen by bees, which might be worth mentioning.
Line 261- True that they can discriminate, but seemingly only when differences in quality are sufficiently large (>30% difference in pollen content). However your results suggest that differences in crude protein content within and between most genera were not very large.
Line 263- This is a bit vague/over-simplified- increased how?


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: POLLEN REPORT: QUANTITATIVE REVIEW OF POLLEN CRUDE PROTEIN CONCENTRATIONS OFFERED BY BEE POLLINATED FLOWERS IN AGRICULTURAL AND NON-AGRICULTURAL LANDSCAPES
Review round: 1
Reviewer: 2

Output:
Basic reporting: This manuscript is well written, and the introduction frames the experiment well.  I have suggested the addition of raw data to all of the plots and have provided an example of such a plot.  I have detailed more explicit comments regarding the plots in my general comments section. All of the data are provided but need minor revision to make them more easily accessible to a broad audience (detailed in general comments).
Experimental design: At its core this is a valid compilation and re-analysis of an interesting global dataset of pollen protein contents. Provided that the authors can address the statistical issues outlined in the general comments section, any findings supported by those corrected analyses will be sound.
Validity of the findings: Despite the strengths detailed above, I believe that in their current state the statistical analyses need revision and are not sufficient to support the authors’ conclusions. I have detailed the issues in the general comments section of my review.
Additional comments: This manuscript provides a valuable analysis of pollen protein content in agricultural and wild landscapes.  The authors gathered data from eight previous publications on the protein contents of crop, weed, and wild plants and use these data to conclude that wild plants produce higher protein pollen than crop or weed plants on a global scale.  This pattern is largely driven by plants in the new world, but there is a non-significant trend towards a similar pattern in Europe.

Though these findings are potentially very interesting, there are some serious issues with the statistical analyses that need to be fixed before the authors conclusions are fully supported. I have organized my comments into Major Issues that I feel need to be addressed in order for the data, analyses, and conclusions to be sound and Minor Comments that deal primarily with the presentation and communication of the findings.  Further I have directly addressed the PeerJ editorial criteria at the end of this review.

Major Issues

•	I am very concerned about the authors’ analytical methods regarding whether or not crops, weeds, or wild plants have higher pollen protein content.  Based on the sample sizes presented in figure 1, it appears that they are treating each observation in their data as independent despite ~85 of their observations being within species replicates.  It is not clear in the description of their statistical models (lines 183-189) whether or not the authors accounted for this in their models, but figure 1 suggests they did not.  If the authors did not account for this repeated measurement, they need to.  Otherwise if they did somehow account for the non-independence of repeated measures on a single species they need to describe how they did this.

•	Similarly there are two issues with the authors analysis of genus level variation.  First, at line 173, the authors say they only included genera that had more than three species level records in this analysis, but they did not do this.  They have included some genera that have three or more repeated measure of a single species but not three different species in the genus (e.g. Lupinus, Zea, Hypochoeris). Secondly, these data seem to call for a phylogenetically corrected model, and the authors should attempt to apply some sort of phylogenetic correction or explain why it would be inappropriate to do so.

•	The authors use two schema for categorizing plants in their dataset: 1) domestication and weediness status, and 2) genus.  At various points in the manuscript they refer to genera of plants as either crop, wild, or weed (e.g. line 207), but not all members of every genus in the dataset are entirely agricultural or wild.  This is especially true for members of Solanum which the authors refer to as a “crop genus” despite only 4 of the 18 species in the authors’ database being crop plants. The authors should be careful regarding this point throughout the manuscript.

Minor Comments

•	L64-67: The authors should move the citations after the final word of this sentence to increase readability.

•	L76 and elsewhere: Throughout the work there is an issue with the Roulston, Cane, and Buchmann 2000 citation.  First, T.Roulston’s name is spelled incorrectly in the supplemental data file (currently written as Roulstone in the, but the correct surname is Roulston).   Secondly in all of the in-text citations the authors have used T.Roulston’s first name instead of his surname (e.g. line 76 should read “Roulston, Cane et al. 2000”).

•	L84: The authors should consider including lipid content here (as they do at line 158 and 253).

•	L279-280: There is a missing line here, and I believe the authors may have inadvertently deleted some text.

•	Works Cited: as written the works cited section is extremely difficult to read, and its formatting should be revised for clarity.

•	Figures 1 and 2: The authors should add raw data as points overlaid over these box plots (to provide readers with a better sense of the distribution of the data) as long as it does not make the plots overly complicated.  As an example, I have produced the an example figure (an attached version of figure 2 that both corrects for the issues mentioned above regarding the inclusion of genera that do not have 3 species, and which also includes raw data). I will include the code to generate this plot with my review.

•	Figure 2: It appears that the authors have color coded the genera, but the logic behind this color coding is not clear in the figure description.  Perhaps red genera are crops, and black genera are wild plants.  If this is the case the authors should consider how they might color code genera that contain crops, weeds, and wild plants (e.g. Solanum).

•	Supplementary data file: The data are uploaded as a comma separated values file (.csv), but are semi-colon delimited. This may cause issues for some readers who open the file in common spreadsheet software (e.g. Microsoft Excel).  The authors should either change the file type to .txt or change the delimiter to a coma.


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: POLLEN REPORT: QUANTITATIVE REVIEW OF POLLEN CRUDE PROTEIN CONCENTRATIONS OFFERED BY BEE POLLINATED FLOWERS IN AGRICULTURAL AND NON-AGRICULTURAL LANDSCAPES
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: The authors have either addressed or provided satisfactory justification for all of the comments and queries I raised in response to the original version of the manuscript. The paper will be a very informative and useful addition to the field of pollination ecology.


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: POLLEN REPORT: QUANTITATIVE REVIEW OF POLLEN CRUDE PROTEIN CONCENTRATIONS OFFERED BY BEE POLLINATED FLOWERS IN AGRICULTURAL AND NON-AGRICULTURAL LANDSCAPES
Review round: 2
Reviewer: 2

Output:
Basic reporting: Overall the reporting is clear and professional.  I only have suggestions on two minor corrections, and the inclusion of one extremely pertinent citation.

Comments:

L63-65: This sentence as written is not 100% clear.  Consider revising, “However, in all cases INCREASING the quantity of flowering plants, and LENGTHENING the timing of flower alone are likely…”

L93: It would be worth citing the recent large study of pollen secondary metabolites – Palmer-Young et al. (2018) Chemistry of floral rewards: intra: and interspecific variability of nectar and pollen secondary metabolites across taxa. Ecological Monographs 89(1). E01335.

L232: “a” should be “and”
Experimental design: Though the authors have decided to only report summary statistics, I still feel that treating each observation as independent is fundamentally flawed. I have detailed my reasoning, suggested a solution, and have detailed specific lines in the manuscript where there are issues.  Further, the authors need to report the number of species represent in  each genus (and report the methods they actually used for generating figure 2 - see comment below).

Comments:

L178-180: Though the authors have chosen to not use any statistical hypothesis testing, there is still an issue with treating multiple observations of the same plant species as independent.  Is there evidence that within species variation (due to the factors described in the text) is higher than among species variation?  There is no issue reporting multiple values for a single plant, but there is an issue treating each observation as independent as it clearly is not.

Instead of treating each measurement from a species as an independent observation when calculating summary statistics, the authors should consider calculating the mean of each species first, then calculate the genus means based on each species level mean. This is a major issue if any given species differs from the true genus level mean and is overrepresented in the sample. In this case the genus level measurement will always be biased in the direction of the more sampled group. I have done some simple simulations (PDF of some code and figures attached) that demonstrate the issue here.

L187-188: The authors say here that they only used genera that had observations for at least 3 species, but this is pretty clearly still not the case in figure 2. For example, they have 5 observations for Echium, but these are only from two species and 3 observations for Lupinus but from only one species.   If the authors are going to include the genera with less than three species represented they should not only report the number of observations for each genus, but also the number of species represented in each genus (at line 201, Table 1, and/or Figure 2).
Validity of the findings: I still feel these are extremely useful data, and the authors should be lauded for compiling this data base.  That said there are still a few issues with their interpretation of these results (see my comments above re: species level replication).
Additional comments: Overall the manuscript has improved after revision, and needs only very minor revision before it is acceptable for publication in PeerJ.


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

Input:
Title: PHOSPHORYLATION/DEPHOSPHORYLATION RESPONSE TO LIGHT STIMULI OF SYMBIODINIUM PROTEINS: SPECIFIC LIGHT-INDUCED DEPHOSPHORYLATION OF AN HSP-LIKE 75 KDA PROTEIN FROM S. MICROADRIATICUM
Review round: 1
Reviewer: 1

Output:
Basic reporting: I feel the manuscript lacks a bit of general introduction or discussion about the current knowledge on the roles and evolution of kinases in the plant kingdom. In particular, the evolutionary conservation of protein kinases in eukaryotes is not mentioned at all. For example, a quick search in PFAM database retrieved more than 600 Symbiodinium protein sequences with a potential kinase activity. Also, protein kinases are well described in multicellular plants (for example Arabidopsis thaliana has >1000 genes encoding kinases, see Wang et al., “The Protein Phosphatases and Protein Kinases of Arabidopsis thaliana”, Arabidopsis book, 2007).

I also found some typos in the manuscript:
- line 60 “… genus Symbiodinium, are photosynthetic…" I would remove the coma;
- idem line 62 “In both, their…”; line 234: “(gives)”;
- lines 302-303, I did not understand the following sentence “Unfortunately, because anti-pTyr antibody-cross reactive proteins were inconsistently observed and due to the lack of reproducibility, were not considered."
Experimental design: Major technical concern: No loading controls are provided in the figures. I strongly encourage the authors to provide images of nitrocellulose membranes stained with a general protein staining such as coomassie blue to show that equal amounts of proteins are present in the lanes analyzed by western blot. This is of particular importance for the experiments where modulation of the phosphorylations is induced experimentally. The presence of such loading controls would greatly improve the reader’s level of confidence in the experiments.

Minor technical concern: the authors are using a NBT/BCIP revelation technique for the revelation step of the western blots. This technique is based on the activity of an alkaline phosphatase and I am questioning the effect of this phosphatase on nitrocellulose immobilized phosphorylated proteins.
Validity of the findings: In this study, Castillo-Medina and colleagues have used an interesting approach to reveal the presence of serine-, threonine- and proline-phosphorylated proteins in extracts from different Symbiodinium species subjected to various experimental conditions. A strong limitation of the technique lies in the fact that there is no possibility to directly identify the phosphorylated proteins or the kinases responsible of the phosphorylation. Nevertheless, this work allowed the authors to reveal the presence of Ser, Tyr and Thr phosphorylation in their Symbiodinium samples. They also revealed phosphorylation/dephosphorylation events in response to light stimuli. Despite the aforementioned limitations, this piece of work is interesting per se, especilly if we consider the very little amount of data already published in the field.
Additional comments: To my sense, this work meets Peer J standards and should be published after completion of the minor revisions listed herein.


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: PHOSPHORYLATION/DEPHOSPHORYLATION RESPONSE TO LIGHT STIMULI OF SYMBIODINIUM PROTEINS: SPECIFIC LIGHT-INDUCED DEPHOSPHORYLATION OF AN HSP-LIKE 75 KDA PROTEIN FROM S. MICROADRIATICUM
Review round: 1
Reviewer: 2

Output:
Basic reporting: The authors Castilla-Medina et al. have presented a profile of phosphorylated proteins from three species of the Symbiodinium family and specifically the light induced phosphorylation and rephosphorylation switch of a 75 kDa proteins from S. microadriaticum. The study is essential as it aimed at filling the knowledge gap about the key signal transduction proteins that undergo the phosphorylation and dephosphorylation switch in response to environmental stimuli like light conditions, nutrient content and availability, etc. The manuscript is easy to understand with clear English language and proper use of grammar and is structured as per PeerJ standards. The authors have reviewed relevant and adequate background information to set a context to the research question being addressed. The reviewer thanks the authors for providing the necessary raw data corroborating their results.
Experimental design: Though the authors have well-defined the research question and provided relevant data to corroborate their findings, the results are preliminary and require further corroboration with orthologous methods. The reviewer has following concerns about the data reported and suggestions to further improve the manuscript –
1.	The authors have stated the detailed protocol for cell lysate preparation and isolation of supernatant for protein analysis, however, protease and phosphatase inhibitors were not used during lysate preparation. It is critical to use a concoction of these inhibitors, especially, phosphatase inhibitors as Espina, V. et al (Molecular & cellular proteomics, 7(10), 1998-2018) reported an augmentation of phosphorylation after phosphatase inhibitor use.
2.	The study uses polyclonal anti-pThr and anti-pSer antibodies whereas monoclonal anti-pTyr. The authors should provide an explanation for the same.
3.	The western blot procedure uses PBST, however, phosphates in the PBST buffer can potentially interfere and therefore it is recommended to use TBST instead of PBST
4.	The authors should consider presenting the total protein content of the lysate as control.
5.	The intensity of the bands indicated for phosphorylated proteins in figure 1 are very weak and barely visible. Perhaps, the authors can try lower dilutions of the primary and/or secondary antibodies, longer incubations times or temperature etc. to increase the intensity of the bands. However, if the authors have already tried different ways to improve the band intensity, they should mention in the results section.
6.	To further support their western blot findings about the effect of light on dephosphorylation & rephosphorylation of pp75 protein in S. KB8, the authors should consider estimating the band intensities in figures 2 and 3 using densitometry analysis on three separate assays to estimate the statistical significance of this phenomenon.
7.	Though the western blot is partially convincing, the authors should definitely consider using orthologous methods like mass spectrometry to corroborate their findings. Mass spectrometry is highly sensitive and is considered a gold standard method for studying phosphorylated proteins and other post-translational modifications (Mann, M. et al. (2002) Trends Biotechnol. 20:261).
Validity of the findings: The above-mentioned suggestions will strengthen the manuscript and will serve to fill a critical knowledge gap as mentioned by the authors. Though the findings are interesting, the work is still preliminary and needs further improvement before it can be accepted for publication. The reviewer strongly advocates use of orthologous method to corroborate the findings as, in general, there are some concerns with the specificity and cross-reactivity of phospho-antibodies.
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: PHOSPHORYLATION/DEPHOSPHORYLATION RESPONSE TO LIGHT STIMULI OF SYMBIODINIUM PROTEINS: SPECIFIC LIGHT-INDUCED DEPHOSPHORYLATION OF AN HSP-LIKE 75 KDA PROTEIN FROM S. MICROADRIATICUM
Review round: 1
Reviewer: 3

Output:
Basic reporting: The results presented were very limited and immature for publishing.

Please also see my comments below.
Experimental design: This manuscript falls within the scope of PeerJ, but the research question was vaguely defined. The hypothesis, approaches, and results were not justified.

The authors identified the gap as ‘…very little information from the genus Symbiodinium regarding proteins that participate in key phosphorylation processes for signal-transduction events that arise from environmental stimuli’. They sought to identify phosphorylated proteins, but showed only western blots, without actually identifying anything.

Why didn’t the author use the mass spec to identify the proteins? The author should at least report which genes/proteins are the phosphorylated proteins. Otherwise, this piece of research will not benefit anyone in the field or those who are interested in Symbiodinium biology.

The genome of Symbiodinium kawagutii was assembled and annotated in 2015 (Lin S. et al, Science). The authors should try to identify the protein of interest using this data. Are there homologous proteins to other known light-induced signaling proteins?
Validity of the findings: It is unclear how many times these western blots have been performed.

 ‘The intensity of band’ was not properly quantified and no meaningful replications was reported. Looking at fig2,3, S1, and S2, I can’t reach the same conclusion as the authors.

The reported changes in fig2 & fig3 are not validated. This change in phosphorylated protein level could result from a change in total protein level. If that is the case, then this process is not related to phosphorylation at all.

None of the results were validated by other methods. I am not convinced. The authors can’t even claim that they have been observing the same protein. Assume there are two proteins, both run at 75kD in a gel, one is upregulated and one is down-regulated, the method here won’t be able to distinguish them.

The conclusions are not well supported by 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: PHOSPHORYLATION/DEPHOSPHORYLATION RESPONSE TO LIGHT STIMULI OF SYMBIODINIUM PROTEINS: SPECIFIC LIGHT-INDUCED DEPHOSPHORYLATION OF AN HSP-LIKE 75 KDA PROTEIN FROM S. MICROADRIATICUM
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors Castilla-Medina et al. have presented response to my previous reviews for their manuscript where they have investigated the phosphorylation/dephosphorylation response of Symbiodinium proteins to light stimuli. The revised manuscript is easy to understand with clear English language and proper use of grammar and is structured as per PeerJ standards. The authors have reviewed relevant and adequate background information to set a context to the research question being addressed. The reviewer thanks the authors for providing the necessary raw data for densitometric analysis.
Experimental design: The following is my response to their rebuttal –
1.	We carried out all the experiments again now using protease and phosphatase inhibitors and all the results reported in this revised version are from experiments carried out again, now in the presence of protease and phosphatase inhibitors.
As suggested in my previous review, the authors performed all their experiments in presence of protease and phosphatase inhibitors. They detail the use of this inhibitor complex in the methods section. This reviewer thanks them for carrying out all the experiments again in the presence of protease and phosphatase inhibitors.
2.	The use of the anti-phospho amino acid antibodies polyclonal or monoclonal depended exclusively on the commercial availability and advertised specificity. In this revised version, we provided the catalog numbers for each antibody we used.
I am contented with this explanation and thank the authors for providing the catalog numbers.

3.	We found no difference in the immunodetection of the phosphoproteins between either buffer; the results were identical, and we provide the evidence as a new Figure S2.
The reviewer thanks the authors for providing this evidence that shows that there in no difference in using either of the buffers.

4.	We used now as an internal loading control, the presence of actin; in this revised version we show the band intensities as well as the densitometric analysis normalized to this internal control (Fig. 3).
The use of actin as the internal loading control and the densitometric analysis have bolstered the authors claims.

5.	The new experiments yielded much clearer bands and they are shown in the corresponding figures; additionally, labels were placed to identify all the detected bands (Figure S1).
This reviewer thanks for providing this new image with clearer bands, however, the authors should detail what was done differently to get clearer bands?

6.	The re-phosphorylation effect was not observed in the new experiments with more rigorously temperature and light control, so all mention to this was deleted. On the other hand, the dephosphorylation effect was reproduced and densitometric analyses were carried out on triplicate samples from each species and the corresponding graphs are now shown as Figures 3 A-B. At least one of the time points in the three species analyzed showed a statistically significant decrease in phosphorylation after the light stimulus.
Thank you for providing the densitometric analyses and carrying out the experiments with more rigorous controls.

7.	We carried out IEF-SDS-PAGE 2D analysis to isolate the corresponding spots (Figure 4 A-B and S5) and the partial peptide sequence, as well as the unequivocal identity of the protein is now reported (Figure 4C) This made also necessary a change in the title.
Thank you for including this new analysis which has significantly improved the quality of the manuscript.
Validity of the findings: The response and the experiments carried out by the authors adequately answer all the questions that were raised in the previous review. Expect for minor question I have in point 5, the manuscript has been significantly improved and meets the standards for publication in PeerJ. I recommend that this manuscript be accepted for publication after answering the minor question in point 5.
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: AN ENIGMATIC DECOUPLING BETWEEN HEAT STRESS AND CORAL BLEACHING ON THE GREAT BARRIER REEF
Review round: 1
Reviewer: 1

Output:
Basic reporting: Well written paper.
Experimental design: High standard.
Validity of the findings: The conclusions are given tentatively. I don't agree entirely with their conclusions, but I think the key point is the results (or more correctly analysis of the results) are soundly undertaken.
Additional comments: This paper poses an excellent question (why didn’t 2004 bleach on GBR), and uses a broad range of available data to answer it. The paper is very well written. The tentative conclusion of the paper is that current driven upwelling, a function of the alongshore velocity of the East Australian Current, is the explanation. While they are looking at important processes, I am not convinced the EAC is the dominant reason (I suspected it is solar radiation, as per point 3). They could also have made a better critique of their conclusion by considering spatially-resolved differences in the bleaching, or lack thereof, in 2004. Nonetheless, they do not over state their findings, and give detailed considerations to an important question. So I conclude this is a paper that should be published, and will provide new estimates on one component of an important, complex problem. But the below comments should be addressed.
Major comments.
1.	I found the figures of the whole GBR with the corals as black dots to be frustrating. What we really want to see is the temperature over the reefs, but instead this is blacked out, and we a drawn to regional scale processes such as offshelf Coral Sea water. I think these figures should be redrafted as scatter plots, with reef points only given and coloured by temperature.
2.	For the discussion. There are papers on the decadal oscillations of the EAC that would put your arguments in perspective (search Hill, Ridgway Cetina-Heredia). As I understand it, but the authors should check, the EAC (at least south of 30 S) was at a maximum strength in around 2005, and a minimum around 2009. I suggest that you look into this using the model you have (SODA), and for your relevant latitude. If the oscillations show a decadal signal, then you can make estimates of when the EAC influence on bleaching will be greatest. What does the next decade hold for EAC-influences on bleaching?
3.	When I look at figure 6, OLR, I would argue the main reason that corals didn’t bleach is that the length of time with anomalously high OLR was shorter for 2004 than the other years. Could you add a third row to this figure of temperature? Corals bleach because of light absorbed at elevated temperatures. How well do the excess light and elevated temperatures line up in each year?
4.	Upwelling nutrients, if limiting, will (1) increase zooxanthellae (thus increasing oxidative stress per coral host), (2) reduce nutrient limitation, thus potentially shifting to light limitation, and encouraging more pigment synthesis that could drive more oxidative stress per symbiont) OR (3) increase the activity of Rubisco enzyme, therefore decreasing oxidative stress.
5.	Upwelled nutrients will not spread evenly over the reef. The argument for the role of the EAC would be much strengthened if it is possible to show that the EAC has a greater impact on preventing bleaching where it has the greatest influence.
6.	North of the separation point, the alongshore flow is northward, which is downwelling favourable. So a weaker SEC would shift the corals north of the separation point to more impacted by upwelled nutrients, and therefore more likely to bleach. The counter argument would be that north of the separation point upwelling is driven mostly by tides, with current-driven bottom boundary layer dynamics less important. The differing effect of the SEC intensity north and south of the separation point should be considered.
Minor comments.
1.	What does MODIS do with PAR data during cloudy periods? I suspect a satellite weather products might do better than MODIS PAR – but this will no substantially change the story.
2.	L210 ‘South Equatorial Current (SEC) colliding with the Australian continental shelf at around 15 S’
3.	L214 ’x’ and ‘y’
4.	Fig. 4 – choose a different colour for Hotspot days (loggers only).


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: AN ENIGMATIC DECOUPLING BETWEEN HEAT STRESS AND CORAL BLEACHING ON THE GREAT BARRIER REEF
Review round: 1
Reviewer: 2

Output:
Basic reporting: The article is well written, unambiguous, and technically clear. Authors provide sufficient background and extensive rationale for research. They highlight the importance of understanding the variety of environmental drivers (besides temperature) the can contribute to coral bleaching. The structure of the manuscript is well organized and easy to follow. I appreciated the sufficient description of their methods and rationale for use of SST derived products.
Experimental design: Methods are describe with sufficient detail. Authors provide detailed information for replicating work. Authors provide thorough evidence of error and standardization of each method.

Line 124: Can authors provide evidence of accuracy for direct comparison of overlaying SST estimations? Is there previous evidence of linear interpolation method to create a pixel-by-pixel comparison of the SST products?
Validity of the findings: Authors highlight importance of key differences in satellite SST products and the need for validation with in situ loggers. I would like to see a text including their recommendation on which SST products to use in future coral bleaching work.

Clarification is needed regarding the reported 64% bleaching that occurred in the Coral Sea Marine Park. Please make a clear distinction between your claims of <3% bleaching and the bleaching that was recorded in the Coral Sea Marine Park. Currently, the manuscript is overlooking the extent of bleaching that did occur in the Coral Sea Marine Park. How did SST products relate to the observe bleaching there?
Additional comments: Very well written manuscript that highlights the importance of monitoring a suite of environmental variables in coral reef ecosystems to better quantify bleaching thresholds. This information is crucial in understanding how to move coral bleaching research forward.


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: AN ENIGMATIC DECOUPLING BETWEEN HEAT STRESS AND CORAL BLEACHING ON THE GREAT BARRIER REEF
Review round: 2
Reviewer: 1

Output:
Basic reporting: No further comment.
Experimental design: No further comment.
Validity of the findings: No further comment.
Additional comments: I am happy with the authors' modifications on what was already a nice piece of work.


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: EFFICIENT VIRUS-INDUCED GENE SILENCING IN HIBISCUS HAMABO SIEB. ET ZUCC. USING TOBACCO RATTLE VIRUS
Review round: 1
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: Figure 3B and 3C: The numbers of the mock and the control plants should be more than three. Here, one seedling was only got for each treatment.

Figure 4 and Table S1 show us four individual repetitions of the qPCR results using infected leaves. And the Figure 3A displays only three infected plants. The authors should name each infected plants.

I suggest the authors compare the transcription abundances of HhCLA1 with the chlorophyll contents in each gene silencing plants.
Validity of the findings: This manuscript tried to set up a virus-induced gene silencing system in H. Hamabo. And the transcription abundance of the marker gene (CLA1) in infected leaves was down-regulated. It was a praisable exploration in such an important plant like Hibiscus Hamabo.
Additional comments: On the whole, the research details and writing of the manuscript is some stuffless.

There are several print mistakes 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: EFFICIENT VIRUS-INDUCED GENE SILENCING IN HIBISCUS HAMABO SIEB. ET ZUCC. USING TOBACCO RATTLE VIRUS
Review round: 1
Reviewer: 2

Output:
Basic reporting: This manuscript is well writen and the data presented is clear.
The refences about study on Malvaceae in TRV-VIGS technique should be added in Introduction.
Experimental design: experimental design is OK.
Validity of the findings: The findings is important to promote molecular breeding and gene function identification in H. hamabo.
Additional comments: This manuscript reports development of TRV-VIGS technique used a new plant species, Hibiscus hamabo through silencing a marker gene HhCLA1. Authors analyzed HhCLA1 similarities of H. hamabo to different plant species, and succeed in development of HhCLA1-silenced plants through presence of white steak on leaves and increase of HhCLA1 expression level.
This manuscript is well written and the data is clearly presented. The provided information is important to carry out the molecular breeding and gene function identification in H. hamabo.
Some points for authors’ consideration:
1.Line 143-145, the rest of 7 treated plants likely showed subtle white-streak leaf symptoms 2 weeks later, so these treated plants should be monitored about their expression level of CLA1. The experiment can improve the manuscript in quality.
2.The leaf phenotypes shown in Figure 4D are shortage of statement in Results. please check.
3.Line 166, add space to separate "fromother" into "from other"
4.Line 167, studies on VIGS in Malvaceae plants, major different cotton species, should be in more detail discussed for explaining highlight of this research.
5.ref Fowler (2017) is incomplete, please check it.
6.In Figure 4 legends, 1, 2, 3 and 4 individual plants are representatives from 52 treated plants? However, supplemental Table 2 only showed 4 individual silenced plants. Please check. Correct “tandard errors” into “standard errors”


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: EFFICIENT VIRUS-INDUCED GENE SILENCING IN HIBISCUS HAMABO SIEB. ET ZUCC. USING TOBACCO RATTLE VIRUS
Review round: 1
Reviewer: 3

Output:
Basic reporting: The manuscript entitled “Efficient virus-induced gene silencing in Hibiscus hamabo Sieb. et Zucc. using Tobacco rattle virus” by Zhiquan Wang et al. describes the TRV-mediated gene silencing of Hibiscus plant.
The author demonstrated that the TRV-mediated transient gene silencing is possible in Hibiscus plant and the optimized methodology would be critical for the functional genomics studies of this sequenced plant genome.
Basic reporting is clear and literatures were cited properly.
Experimental design: Experiments design were acceptable except few points need to be addressed as mentioned below.
Validity of the findings: Results are acceptable but need more control to validate the findings, which is mentioned below.
Additional comments: I have many concerns, especially with the figures. Figures arrangement and description require attention. Also controls are missing which I had listed below,

1.	In Introduction, author need to elucidate the CLA1 gene in Hibiscus, a comparison of CLA1 gene of Hibiscus with Gossypium spp., Arabidopsis and Vernicia fordii is highly recommended.

2.	Although authors had mentioned in materials and method section, I would suggest providing the vector map of the plasmid constructed in figure 3.

3.	After infiltration, author observed the appearance of white streak on plant leaves, but no molecular evidence has been provided that this phenotype is a result of the dsRNA which is cleaved into short interfering (si) RNAs of 21 to 25 nucleotides. Any RNA blot or fluorescent/non-radioactive probe to detect these 21-25 nucleotide guide sequences could have been utilized to confirm this working of TRV system and phenotype.

4.	Figure 1: The figure is not clear and hard to read, conserved amino acids, motif and domain analysis are also not clear. Define the color code used in figure legend. Mark clearly the conserved residues. I would suggest, for the domain analysis and homology study author should keep only closely related and well characterized 3-5 sequence of CLA1 from different organism. And include Gossypium spp., Arabidopsis and Vernicia fordii as TRV mediated gene silencing has already been performed in this organism.

5.	In figure 2 also, include Arabidopsis and Vernicia fordii sequences as well.

6.	Result subheadings are poorly written, it should be more conclusive. What do you mean by qPCR??? Are you going to explain qPCR technique??

7.	In result section “Characterization of the HhCLA1 gene.” Elaborate in detail about your result of homology and phylogenetic analysis as mentioned above for figure 1.

8.	Figure legend is poorly written. Please explain the figures. Remove sequence identity from figure legend 1 and put it in table form.

Overall the manuscript is satisfactory. The findings are worth to report and will be useful in functional genomics of Hibiscus hamabo. Literature is well referenced & relevant to the concept.


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: EFFICIENT VIRUS-INDUCED GENE SILENCING IN HIBISCUS HAMABO SIEB. ET ZUCC. USING TOBACCO RATTLE VIRUS
Review round: 2
Reviewer: 1

Output:
Basic reporting: In the new version, the manuscript has been made some improvement.
Experimental design: I think the authors answer my questions below clear.
1.	Figure 3B and 3C: The numbers of the mock and the control plants should be more than three. Here, one seedling was only got for each treatment.
2.	Figure 4 and Table S1 show us four individual repetitions of the qPCR results using infected leaves. And the Figure 3A displays only three infected plants. The authors should name each infected plants.
3.	I suggest the authors compare the transcription abundances of HhCLA1 with the chlorophyll contents in each gene silencing plants.
Validity of the findings: It is a worthy effort for establish of a gene silencing system in Hibiscus Hamabo.
Additional comments: The manuscript needs much more attentions on English writing.


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: EFFICIENT VIRUS-INDUCED GENE SILENCING IN HIBISCUS HAMABO SIEB. ET ZUCC. USING TOBACCO RATTLE VIRUS
Review round: 2
Reviewer: 2

Output:
Basic reporting: as shown in general comments to authors
Experimental design: as shown in general comments to authors
Validity of the findings: as shown in general comments to authors
Additional comments: The revised manuscript has been obviously improved in quality. The most questions have been explained. I have not other comments for this revised manuscript excluding some minor suggestions.
1.	“Gossypium” throughout the manuscript should be omitted to “G.” excluding the first presence.
2.	Line 205, “functional genomics” is unfit for VIGS tool because it is used in transcriptional level.
3.	In figue 4, “Aa” and “Bb” are unclear. Please check it.


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

Input:
Title: EFFICIENT VIRUS-INDUCED GENE SILENCING IN HIBISCUS HAMABO SIEB. ET ZUCC. USING TOBACCO RATTLE VIRUS
Review round: 2
Reviewer: 3

Output:
Basic reporting: The manuscript entitled “Efficient virus-induced gene silencing in Hibiscus hamabo Sieb. et Zucc. using Tobacco rattle virus” by Zhiquan Wang et al. describes the TRV-mediated gene silencing of Hibiscus plant.
Manuscript has improved after revision and is acceptable for publication.
Experimental design: Satisfactory
Validity of the findings: Satisfactory
Additional comments: I agree with the authors about their response for my comment especially number 3. Answer to this question may qualify for the next publication.


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

Input:
Title: TRANSPLANTATION OF ADIPOSE-DERIVED STEM CELLS OVEREXPRESSING INDUCIBLE NITRIC OXIDE SYNTHASE AMELIORATES DIABETES MELLITUS-INDUCED ERECTILE DYSFUNCTION IN RATS
Review round: 1
Reviewer: 1

Output:
Basic reporting: There are a few minor typographical errors:
Line 57 should read "secrete" rather than "secret"
Line 58 should read "ADSC" rather than "ADSCs"
Line 62 should read "in the penis" rather than "in penis"
Line 110 should read "fourth" rather than "forth"
Line 312 should read "penile" rather than "penil"
Experimental design: There are a few elements of the methods and materials that are missing such that the experiments would be impossible to replicate as it stands: These are detailed below:

The number of passages through which the ADSCs have been cultured should be given for all experiments, at the moment it is only stated for some experiments.

The catalogue numbers of all of the antibodies used in the FACs, immunofluorescence microscopy and immunoblotting experiments should be provided.

It is not clear if the adenovirus expressing iNOS-EGFP expresses a fusion protein or iNOS and EGFP from separate promoters, as through most of the results it is annotated as ADSCs-iNOS and statistical comparisons should only really be made with statistical tests between ADSCs expressing EGFP and not ADSCs alone.

There is no mention of how the immunofluorescence microscopy experiments were performed.

It is not clear how the immunoblotting was performed - what secondary antibodies were used and how were they detected? From the blots provided in the raw data it would appear to be enhanced chemiluminescence with HRP-labelled secondary antibodies, but this is not stated.

It should also be noted that the CCK-8 assay essentially measures levels of reduced NADH and NADPH, so it is a measure of metabolic activity and viability, not a measure of proliferation as the authors state.
Validity of the findings: In Figure 2A, the authors provide images of EGFP-adenovirus-infected cells, but not iNOS-EGFP-adenovirus-infected cells, which is equally important to assess infection efficiency.

As mentioned above, the appropriate statistical comparison is between ADSCs expressing EGFP and those expressing iNOS in Figures 2B, 2D, 3B, 3D-G, 4B-D. These data should not be compared with ADSCs alone, as any difference could be ascribed to viral infection and/or expression of iNOS.

The number of independent replicates undertaken for all of the data needs to be clear in the figure legends of each data figure.

The raw data for Figure 3A does not appear to have been provided.

The raw data tiff files provided for the immunoblots for Figure 2-2 are over-exposed and new data should be provided.

The immunoblots for p-Smad2/3 and Smad2/3 exhibit multiple bands, indicating a great deal of non-specific binding of the antibody. Do the authors have evidence that the bands they have quantified are actually Smad2/3?  As a consequence the immunoblots are not of a quality suitable for quantification and more clear immunoblots should be provided.  With any improved immunoblots, quantification should examine Smad2 and Smad3 individually, otherwise any data will underestimate potential differences.

How were the immunoblotting experiments performed to give the cell culture protein expression? The ratio will vary with the exposure of each immunoblot and unless all replicates were immunoblotted at exactly the same time, probed with secondary antibodies at the same time and imaged at the same time. Therefore it seems unlikely the data can be presented without being normalised to one condition for each experiment (as it is in Figure 1C, for example).
Additional comments: The manuscript is clearly written and convincing yet there are issues I have highlighted with respect to the detail of the methods and materials used and the quality of the immunoblots. Furthermore, without better labelling it is difficult to tell whether the supplemental files of the raw immunoblot data are all of the replicates or just some of them. I would also point out that lines 289-293 in the conclusions indicate one particular mechanism by which the ADSCs may signal to the CCSMCs in co-culture, but there are many alternatives to miRNAs in exosomes and this should be discussed in further detail.


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: TRANSPLANTATION OF ADIPOSE-DERIVED STEM CELLS OVEREXPRESSING INDUCIBLE NITRIC OXIDE SYNTHASE AMELIORATES DIABETES MELLITUS-INDUCED ERECTILE DYSFUNCTION IN RATS
Review round: 1
Reviewer: 2

Output:
Basic reporting: This a clearly written, logically structured manuscript that succinctly described the results of experiments designed to test the potential therapeutic utility of adipose derived stem cells over expressing iNOS in experimental diabetic erectile dysfunction. The background literature is well summarised and supports the authors novel and testable hypothesis.

The data figures are well constructed and presented.
Experimental design: The experiments described in this manuscript are logically designed to advance previous studies in this field; specifically the therapeutic utility of ADSC's and iNOS-mediated NO generation in DMED.

The methods employed are appropriate and span biochemical, cell biological and in vivo techniques. Taken together these experiments represent a comprehensive test of the hypothesis.

Whilst the findings from the in vivo model are entirely consistent with iNOS-mediated NO produced by transplanted ADSC's  exerting beneficial effects this has not been directly verified (by the co-administration of an iNOS selective inhibitor) and therefore the authors should be cautious when discussing this point.

The authors have not quantified the number of ADSC-iNOS cells that remain the erectile tissue after transplantation. It is clear that NO and cGMP levels are elevated following transplantation but it is not clear where the transplanted cells end up.
Validity of the findings: No comment
Additional comments: This is a well written and logical manuscript that describes the results of a series of experiments testing the therapeutic utility of ADSC-iNOS in a preclinical model of DMED. The data presented broadly support the conclusions and provide novel findings that advance our understanding of the role and therapeutic utility of iNOS in ED.


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

Input:
Title: THE EFFECTS OF HIGH VERSUS LOW TALKER VARIABILITY AND INDIVIDUAL APTITUDE ON PHONETIC TRAINING OF MANDARIN LEXICAL TONES
Review round: 1
Reviewer: 1

Output:
Basic reporting: This manuscript investigates the question of how high-variability training and individual aptitude interact in learning of Mandarin tonal contrasts using real Mandarin words. Training manipulations included low variability (one talker), high variability (four talkers, interleaved presentation), and high variability blocked (four talkers, blocked presentation). Aptitude was assessed with a pitch contour perception task and a categorization task of a synthesized tonal continuum. Tone learning was assessed with discrimination, word identification, and production (word repetition and picture naming) tasks. Although all groups improved on the training and testing tasks from pre-post, no advantage was found for the high-variability groups for trained or untrained stimuli, and no interaction was found with aptitude.

The high quality of statistical methods and data analysis was the main strength of the paper: I thank the authors for their careful description of the methods, providing raw data and R scripts, and for using rigorous statistical methods (e.g., mixed effects logistic regression) to analyze their data. However, several major issues with the framing of the study attenuated my enthusiasm for the manuscript, and these are detailed below.

A primary concern of this study is that it lacks a strong theoretical motivation, and I was unconvinced that it was necessary to replicate the Perrachione et al. (2011) findings using real Mandarin words. There may be good reasons to investigate whether high-variability training is beneficial for learning in a more ecologically valid situation, but this needs to be discussed and motivated more strongly. The manuscript could be strengthened by discussing a theory or model that would predict different outcomes of the high-variability training paradigm when using real Mandarin words as opposed to pseudowords. Perhaps there is reason to believe that learning Mandarin segmental phonology and tonal contrasts simultaneously would yield different results than previous studies (e.g., Perrachione et al., 2011). Otherwise, it does not seem that this study adds to the field’s understanding of high-variability training in phonetic learning.

The literature review was thorough; however, the introduction could be substantially shortened and streamlined. Instead of giving such detailed descriptions of previous studies, I would recommend discussing the previous literature in the context of a theoretical model of (phonetic) learning and making the core questions of the study more prominent.

Line 92: Please cite Bradlow et al. (1999) for long-term retention of production improvements.
Experimental design: As discussed above, it is not clear that there is a gap in the literature that necessitates this study, and reframing the introduction could help clarify the motivation for using real Mandarin words in training and why this might impact our understanding of high-variability training or phonetic learning more generally.

Statistical analyses are appropriate for the data collected, and the methods and analyses are explained in enough detail to enable replication. Plots are easy to read and effectively display the data.

In Figure 11 (training data), in the high aptitude group, the HVB and the LV groups look almost indistinguishable from each other, especially for the first few days. However, in the low aptitude group, the LV group looks like they are performing better than the HVB group. Although I agree that using a continuous measure for aptitude gives you more power in the analysis, it might be worth looking at the aptitude variable categorically after all, especially to compare the HVB-trained participants in high- and low-aptitude groups in the training task.
Validity of the findings: The discussion section should address in greater detail why the current study did not replicate previous high-variability training studies. I agree that some of the earlier studies were likely underpowered; however, this effect has been replicated several times since then with larger sample sizes (e.g., Lively et al., 1994; Perrachione et al., 2011) and for different speech tasks such as accent adaptation (Bradlow & Bent, 2008) and tone learning (Perrachione et al., 2011). The greatest benefits observed in previous studies of high-variability training have typically been for generalization. Perhaps there was no benefit for generalization in the current study due to the pre-training differences in the trained and untrained talkers. Please address.

A discussion on why variability may not be universally beneficial could improve the discussion section, as well, seeing as the LV condition outperformed the HV and HVB conditions on some tasks.

Although some of the original predictions were not borne out, I think there are still some valuable findings in this dataset. For example, the fact that participants improved from pre- to post-test on the pitch contour perception task may have methodological relevance, as this task is often used as an aptitude measure (i.e., Is it really measuring aptitude or is it measuring some type of experience?). A more general discussion of this transfer of learning (from training task to PCPT) would also strengthen the discussion.

The discussion could be further improved by suggesting specific studies that would need to be done to disentangle some of the inconclusive results of the study.
Additional comments: In general, this manuscript needs to be thoroughly proofread. I have noted several typos below, but this list is not exhaustive. There were also inconsistencies in British and American English spellings (e.g., generalization vs. generalization).

Typo line 38
Line 161: productions with an s
Line 225: should be en-dash, not hyphen
Line 275: “Those used in…”
Typo line 285: tones
Typo line 293: that the last two tasks?
Typo line 294: into
Line 378: on-screen, not on- screen
Line 433: main stimulus set?
Line 454: pictures
Typo line 464: space
Typo line 465: conditions
Typo line 469: conditions, but should this actually say, “for this condition”? It seems the low variability group wouldn’t need speakers to be randomized because they only have one.
Line 503: colon not appropriate there. Only use after a complete sentence.
Line 507: no comma after analyses
Line 523: ensured?
Line 551: (2013) in parentheses
Line 806: typo—measures
Line 812: English speakers’
Line 963: en dash, not hyphen
Descriptions for Figures 11 and 12 seem to have gotten cut off (at least in my copy of the manuscript).


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

Input:
Title: THE EFFECTS OF HIGH VERSUS LOW TALKER VARIABILITY AND INDIVIDUAL APTITUDE ON PHONETIC TRAINING OF MANDARIN LEXICAL TONES
Review round: 1
Reviewer: 2

Output:
Basic reporting: Overall, the manuscript was fairly clear. There were some ambiguities (some of which were listed below) to be clarified.
Figures and Tables were appropriate and useful.  For ease of processing, it would be great if the tests were itemized in the same order in Session 1 and 8, and that the authors could indicate that Picture Identification and Picture Naming were additional tests.
Table 2 was useful to provide the readers with an overview of the talker manipulation. Given the number of tests administered in the current study, it was difficult for the readers to keep track the purpose of various tests and its relevance to the research questions and predictions, especially when some of them were administered both pre and post-tests; whereas others were only administered post-test.  Perhaps the authors would consider including such information in Table 2.
The current ms organized the results (also the procedures) around each administered test.  This made it difficult to relate the results to the research questions and predictions.  It would be great if the authors could re-organize the stimuli, procedures and results according to the purpose of these tests. For instance, measures of aptitude assessment (PCPT, CSTC); measures of learning (word repetition, 3-level-oddity, picture naming, picture identification). Within the measure of learning, the 4 tests can be further sud-divided.
Experimental design: Line 249-263: the current study tested the benefit of learning from multiple voices, using new paradigm and real Chinese words. It was a partial replication of previous studies on the beneficial effect of learning from multiple voices, as well as the interaction between individual aptitude and learning from multiple voices. Apart from replication, the question was not very well-defined.
The ms discussed the 2 studies (Perrachione et al., 2011; Sadakata & McQueen, 2014) and used their findings to motivate the research questions in the current study.  Yet the current study did not point out that Perrachione et al. only manipulated familiar vs novel speakers. That is, the same 18 test items were used in pre-test, training and post-test. Training effect (single talker vs multiple talkers) was generalized to test items from novel speakers. On the other hand, Sakadata & McQueen (2014) manipulated the critical (test) tones along a few dimensions so that the bi-syllabic tone sequences in training was different from those at test.  These dimensions included a new position of the critical tone in the bi-syllabic sequence, a new contextual tone in combination with a critical tone to form a bi-syllabic tone sequence, a new vowel bearing the critical tone, the critical bi-syllabic tone sequence from a novel speaker and the critical tone sequence in a sentence context. These differences raised questions as to what kind of information is being learned during variability training and how these information can be generalized across different types (i.e. speaker-variability, item-variability).  It would have been useful if the experimental design was clearly tabulated: what was varied, what was kept constant during pre-training, training and post-training, for example:
Aptitude Assessment
PCPT (pre & post-test)
CSTC (pre & post-test)
Assessment
(in the following 2 tests there was a factor of ‘item-novelty’)
Word Repetition (pre & post-test)
Three-interval-oddity  (pre & post-test)
Picture identification (post-test) – in familiar voice vs. novel voice
Picture naming (post-test)

When I grouped the stimuli in Appendix A as below,
Training Items
Onset consonants
T1-T2: Ch, m, q, T1-T3: j, sh, x, T1-T4: b, h, zh, T2-T3: b, w, n, T2-T4: d, x, y, T3-T4: d, m, y
Vowels
T1-T2: Ua, ao, ia, T1-T3: iao, u, ue, T1-T4: a, ua, u, T2-T3: i, a, iu, T2-T4: i, ie, u, T3-T4: a, i, a

Non-training items
Onset consonants
T1-T2: sh, t, t, T1-T3: m, g, zh, T1-T4: d, k, x, T2-T3: ch, h, y, T2-T4: m, sh, w, T3-T4: b, d, j
Vowels
T1-T2: i, uo, i, T1-T3: a, ui, e, T1-T4: en, u, ian, T2-T3: i, u, u, T2-T4: o, e, a, T3-T4: ao, ao, ian
It is clear that there was segmental variability for each tone pair contrast and that there was segmental variability between training and non-training items.  So, what was it that one expected learners to generalize to? And what was it that high variability training would benefit learners in this regard?
Validity of the findings: The overall result of the current study was that high variability training did not benefit learning Chinese tones and the variability training did not interact with aptitude assessment.  Given my concerns about what kind of generalization and benefit that high variability training would bring to various tasks/tests, I was not convinced about the interpretation of the findings in view of the previous literature (e.g. Lively et al., 1993; Logan et al., 1991 etc).
Additional comments: Line 38. Please change ‘This task is particularly difficulty…’
Line 59. Please change ‘… a phonemic contrasts…’
Line 117. ‘… however for the identification task the improvement was greater following high variability training’ was a dangling phrase.  Please change.
Line 152 – 153, … 60 NEW words produced by … training speakers, and another with additional 60 new words by new speaker’ Confusing with the word ‘new’. Confusing. There were 2 generalization tasks: one to novel stimuli from familiar speaker, the other to novel stimuli from novel speaker.
Line 143. ‘they do not use pitch information lexically…’ please note that pitch can be used to mark stress at the lexical level too (e.g. ‘import vs. im’port).
Line 163-164. Please note that this was not what Wang et al. 2003 reported (see p. 1037 to 1039: All four tones improved in production post-test, and p.1040 the para starting ‘in terms of individual tones…’ it only referred to T1).
Line 191. Please specify in what way the participants with different aptitude benefited from the different training conditions. High aptitude participants benefited in terms of generalization. Low aptitude ones benefited in terms of performance during training.
Line 201, shouldn’t the correct reponse be ‘1’ instead of ‘2’?
Line 205. Please make it clear that Sadakata et al did the following: Variability was increased in terms of the number of different speakers and the number of different vowels used in bisyllabic sequence.
Line 221-3. This was confusing. Please specify the tasks the benefits were found.
Line 234. Please specify the task the benefits were observed.
Line 236 – 240. Please clarify about the blocked presentation in Sadakata et al. Speaker variability was blocked by session, but not segmental variability. In Perrachione et al, the phonetic variability (i.e. segments) were kept constant and talker variability was varied. Note that Sakadata et al. additionally manipulated item-variability; whereas Perrachione et al. did not. So it is unclear whether trial-by-trial inconsistency is less in the former than the latter.
Line 252. Please note that Wang et al (1999) also used real words in their investigation of variability on learning L2 contrasts.
Line 294. ‘… tapping into mechanisms…’
Line 351. ‘… talker set 2..’
Line 333-338. This was very difficult to process.
Line 412. The choice of ‘different’ stimulus was ambiguous.  The test item was different in terms of speakers too.  I presume what the authors meant was ‘the odd one out’.
Line 454. ‘… the two pictures always…’
Line 464. ‘… resulting in 288..’
Line 507. ‘ These analyses explore… ‘
Line 523. ‘… which ensured…’
Lines from 526. The description of easy, neutral and hard trial types was not easy to follow.  Did the difficulty lie in different voices/talker or different critical/test words?
Line 539. ‘ and in order..’ grammatical issue.
Section 3.2.1 please stick to the PCPT –CSTC order as before.
Line 600. Please change to ‘… in pinyin..’
Line 606. 3 measures were taken.  But it stated that the inter-rater reliability was examined for ‘both’ measures. Which ones?  Why 2, not 3? This was ambiguous, especially when later on the authors did talk about 3 measures. Please clarify.
Line 630-632. How good were they at pre-test?
Line 649-652. Please clarify ‘ … variability condition (test session by LV…’ The statistical result did not correspond to the statement.
Line 754. ‘participants in the LV groups performed showed no significant difference..’ Please rephrase.
Line 757, Please state that there was no significant difference in pinyin accuracy between variability conditions.
Line 765-766. Why would one expect improved performance, if the task required them to recognize a picture, when the focus of training was on speaker variability? The segmental and f0 information would allow the L2 learners to do the job. From the figures, it looks like the accuracy rate was fairly high overall.
Line 838. ‘… input is in line with…’
Line 851-854. Statements did not correspond to the reported results.
Line 868.’ Since all of the speakers in these test items were new, improvement in this test indicates generalization over speakers.’ I did not follow.  The 3-interval-oddity task was administered pre- and post- training.
Line 875. ‘… best performance…’
Line 882. ‘… but not for those…’
Line 898-900. But line 647 reported no improvement after training in the word repetition task. Please clarify.
Line 904. ‘… in the different types of variability conditions..’
Line 909. ‘ 47% ; ‘
Line 919. ‘… is in line with the lack of a main effect in previous tone-training studies..’ Which one?  Please specify.
Line 931. ‘… there is a need…’