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: BENTHIC GRAZING IN A EUTROPHIC RIVER: CASCADING EFFECTS OF ZOOBENTHIVOROUS FISH MASK DIRECT EFFECTS OF HERBIVOROUS FISH
Review round: 1
Reviewer: 1

Output:
Basic reporting: More description of their study system and methods is needed.  Most of these aspects should be relatively straight forward.

1.  What is the drainage area of the river Nister?  Drainage area is easily obtained from maps, and are much more quantitative than stream order.
2.  What are the potential algivores (nace and major invertebrate grazers) in the system, how do they graze (browsing tips, clipping lawns, or scrubbing down to basal cells?)  How do fish vs invertebrate grazing pressures change with substrate texture or stream velocity?  In other words, tell us more about the natural history of the system, and which biota are likely to significantly affect algae.
3.  I was confused about the scales over which densities were measured.  Invertebrate densities were not described, and fishes were unconfined, so how do stock estimates from electroshocking relate to the densities of the nase and the invertebrate feeding fish over the scales that would influence standing crops of algae on the tiles.?
4.  What taxa of algae or macrophytes were being grazed?  Are they green algae, diatoms, cyanobacteria?  Adnate or loosely attached?   Are their natural substrates stony—were concrete blocks a good facsimile?  When did the experiments occur within the seasonal algal succession and cycles of substrate colonization, vegetative growth, and sloughing that macro-algae or macrophytes show?

The English is adequate, but not always completely clear.  There may be too much background information and there is certainly too little description of the actual biota or the study site or the spatial and time scales of natural processes (like fish foraging ranges or seasonal succession in stream biota) that matter.

 Their raw data and authorizations for research all appear in order.
Experimental design: I think the design is ok if
1) the concrete tiles grow periphyton that is representative of what is on the natural river bed, but you should support this.  One problem, in addition to surface texture and chemistry differences, is that if you place the tiles after natural colonization periods by algal propagules, you'll not grow the periphyton that may represent the natural flora of the stream bed.
2) you can explain what factors keep fishes at (or close enough to) the densities that you estimate with electro-shocking long enough to reflect their actual impact on the food chains that influence algal biomass over your experimental periods
Validity of the findings: The experiment you designed tests fish effects, not nase effects, on periphyton biomass on artificial substrates.  You find that fish exclusion augments algal biomass, and infer (I suspect correctly) that invertivory may release algae from grazing invertebrates, which seem to have stronger effects than algivorous nase.  If you can give us some clearer descriptions (and even better, some quantitative data) on the densities and grazing severity of grazing invertebrates versus nase, the paper would be a clearer contribution to our general understanding of which consumers can exert strong controls over producer biomass in rivers.
Additional comments: Top-down effects of herbivorous fish (Chondrostoma 1 nasus L.) in a eutrophic river (#21164)

The authors hypothesized that a fish they identify as the only obligate herbivorous fish in Europe, the cyprinid common nase (Chondrostoma nasus), may suppress periphyton growth in eutrophic rivers, as herbivorous fish are known to do in some midwestern North American and many tropical rivers.   They tested their hypothesis with a field experiment in Rhineland-Palatinate, Germany in the river Nister, a large river enriched with human sewage and agrochemicals.  They used electric fencing to  exclude all fish from 40x40 cm2 concrete tiles placed on the river bed.   They used natural densities that varied 8x over the first year, and in the second year, artificial stocking elevated nase densities 70x (but did the fish stay where they were stocked?  See below.)  The authors, however, did not find the effect they expected from nase exclusion.  To their surprise, they found more algae where all fish were excluded, and concluded that benthic invertebrates were more important as grazers than fish.  They offer a reasonable explanation, that invertebrates were more important grazers than nase in this system, and that excluding invertebrate-feeding fish, particularly loach, released invertebrates to graze down algae within fish exclosures.  I think the large scale of the field study, the tests over a large range of free-swimming nase densities, and the lack of enclosure artifacts are all strengths of this ms, but a bit more clarification of scale and natural history is needed.


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: BENTHIC GRAZING IN A EUTROPHIC RIVER: CASCADING EFFECTS OF ZOOBENTHIVOROUS FISH MASK DIRECT EFFECTS OF HERBIVOROUS FISH
Review round: 1
Reviewer: 2

Output:
Basic reporting: The basic reporting was done well.
Experimental design: The experimental design was effective for testing effects of an electric field treatment on development of benthic river assemblages, and the methods were well described. But in some ways the design would not be effective for testing what was reported to have been tested, at least without further convincing by the authors (see below).
Validity of the findings: The findings of these experiments are valid concerning effects of excluding a subset of grazers (and predators) from early-successional benthic communities. The focus of the paper is different to what was actually tested though.

1.	I am concerned about the uncertainty of what exactly was excluded by the electric field. The authors state that all fish were excluded, so the strong focus on just one species (nase) is not warranted. Nase may be expected to be the main grazer and have the largest effect, but they were not excluded separately from other fish, so the separate effect of nase is not known.

2.	Also, the possibility of some invertebrates from being excluded was not mentioned. For example, some studies have found large impacts of electricity not only on fish but also invertebrates (Brown et al. (2000) J. N. Am. Benthol. Soc. 19:176-185). Overall, the experiment can not tell if effects on periphyton are caused by exclusion of all (or some) fish, some invertebrates, or changed predation of the fish on the invertebrates. All it can answer is – what are the effects of species sensitive to an electric field on benthic assemblages? I think it is necessary to do some additional experiments to determine if any invertebrates are or are not independently affected by electricity. Or possibly the authors can find some past studies (including similar invertebrate species) that show an electric field of the same strength used in this study does not affect their abundance or behavior.

3.	It is good that three experiments were done, but they are done at different times and the contexts of the experiments will differ in many ways besides just differences in nase abundance among those times. I think it is all right that the authors do include some speculation about how differences in nase abundance may contribute to differences in results among the experiments, but differences of nase density should not be overly emphasised (e.g. line 260, 314). The emphasis should be on differences among separate experiments that may differ in many ways including, but not limited to, nase density.

4.	The tiles were left in the river for a total of 32-33 days, so I would think these will still be early-successional communities that have developed. If so, then the results are only applicable to these kinds of assemblages, which would need to be stated. For example, late-successional assemblages may have benthic algae that are more resistant to grazing and the results would be very different. If the natural benthos is dominated by late-successional assemblages then the results may have limited relevance.

5.	The experiment did not include measurements of naturally-occurring river substrata (e.g. boulders or flat rock) so it is unknown how the colonisation of the tiles may differ to colonisation of natural substrata. For example, the surface textures may be different and affect periphyton growth. Possible differences between the natural and artificial substrata need to be discussed. If the authors have any data on what the algal and macroinvertebrate assemblages were like on surrounding natural rock surfaces they should consider including these data.

6.	The opening of the abstract and introduction is about eutrophication, but the experiments are only indirectly relatable this process. I think the beginning of the introduction and abstract should be changed to be related to effects of fish, then the possible consequences for eutrophication can be mentioned. As it is, readers interested mostly in eutrophication may be confused when they realise this study it more about fish affecting the benthos.
Additional comments: 1.	Line 40: This should be reworded because the only comparisons of periphtyon biomass showed that there was no significant different among treatments (Line 266). The difference was in chlorophyll concentrations, which may or may not be related to biomass.
2.	Line 154 – could you please include details of these preliminary experiments, perhaps as supplementary material? I would like to know details such as 1) how observations were made (were the authors certain that the nase were completely excluded during the 24hrs?), 2) were the fish starved before the trial and what kind of food were they provided near the electrified area? (if the fish were not actively foraging then they would not have any reason to go near the baited electrified area), 3) was a control area included that was not electrified in this trial? Could the authors also please include discussion about how they did not test the effectiveness of the electrified treatment on any of the many other species of fish that co-occurred with nase and which also will have affected the benthic assemblages.
3.	Line 150 – did the fence chargers create a consent electric field, or one that pulsed on and off?
4.	line 162 – I had trouble understanding exactly how many treatments were used. If this line means that there were 9 control tiles and 9 electrified tiles in each experiment, could the authors please make it a little clearer.
5.	Line 236 – I think there is a error in this sentence
6.	Line 245 – change to “weighed”
7.	Line 248-249 - Can you please explain what the multiple comparisons were that needed correcting for?
8.	Line 265-266 – any non-significant effect on AFDW should be mentioned in the abstract along with the significant effect on chlorophyll.
9.	Line 288 – change to “There was no evidence that the environmental factors water depth, light and current velocity affected the experimental results.”
10.	Line 329 - 331– the potential influence of invertebrate grazers is something that could easily have been predicted before the start of the experiment, so I think it needs to be incorporated into the hypotheses. Overall, the experiment would be made much more valuable if some more data on separate effects of invertebrates were included.
11.	Line 396 – change “special” to “spatial”
12.	Figure 2 – I think the Asterisks are not meant to be there.


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: BENTHIC GRAZING IN A EUTROPHIC RIVER: CASCADING EFFECTS OF ZOOBENTHIVOROUS FISH MASK DIRECT EFFECTS OF HERBIVOROUS FISH
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: I have provided some additional minor changes. The line numbers below correspond to the line numbers on the “tracked changes manuscript”, which had line numbers that were slightly different to the reviewing PDF for some reason.

Title: I would consider changing the title and expanding it with a bit more detail of the findings. The current one does not really reflect what was found in the study because there was no top-down effects of nase, while the important effect was likely from other fish eating the invertebrate grazers.

Line 23-24: This sentence in the abstract seems out of place and the mention of generation times being mismatched will confuse readers. Maybe change it to something like “Although benthic invertebrate grazers reduce the growth of periphyton, this is highly context dependent”.

Line 40: I may be wrong but I would guess that “benthivorous” means species that eat anything from the benthos, and this would include not only invertebrates but also algae, so maybe change to “predators of benthic invertebrates”. This may need changing throughout the MS.

Line 44-50: Starting the introduction with mention of specifically invertebrate grazing is a bit confusing, especially given invertebrates are not mentioned in the title. Perhaps you could merge the 1st and 2nd paragraphs so you mention both types of grazing (invert. and fish) together.

Line 82-83: I still find this ambiguous. It might mean there was one set of tiles per experiment, including 9 tiles some of which were electrified and some weren’t, or it could mean that each experiment had two sets, including 18 tiles altogether, some of which were electrified and some weren’t. This is an important piece of information, so try to be very clear, e.g. “Each separate experiment had a total of 18 tiles; half the tiles were electrified to exclude fish, and the other half were non-electrified to allow fish access”

Line 319: are you certain that Standard Deviation here is meant to be a percentage?

Line 335-336: Is there any reason this is in square brackets? Also, why is SD shown for the tiles but not the stone. Also, check whether you are presenting here Standard Deviation or Standard Error.

Line 409: change “we have no proof” to “there is uncertainty whether”

Line 413: Not sure what you mean by “quantitatively” here

Line 486: add “directly” before “transferred”


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: CATCHMENT LAND USE PREDICTS BENTHIC VEGETATION IN SMALL ESTUARIES
Review round: 1
Reviewer: 1

Output:
Basic reporting: The results are, in general, presented clearly; however, there is some confusion around the inclusion of chlorophyll a in their assessment. I suggest that the authors mention that (and explain why) they assessed chlorophyll a in their introduction (perhaps in final paragraph where the aim is outlined) and mention the analysis in the methods (which I’m assuming is the same as for their prediction of MA:TV).

Tables 1 and 2. Please reword your Table captions. It is insufficient just to say that it is a table of results. Ideally a table should be able to be read and understood without having to read the main body. Also expand on what you mean by pr(inc) and ß as many readers will not be readily familiar with your techniques and chosen notation. Please also indicate what the abbreviations you’re adopting (or write them in full) in your table, i.e., what does “Tf” represent? When you say “Values >0.75...” please be specific about what values you’re talking about, i.e., the Bayesian variable selection.

Table 3. Since you only measured 14 sites, it wouldn’t be too cumbersome, yet highly informative, if you could please show the export rates and land-use for all 14 sites rather than a summary.
Experimental design: The research question is generally well identified and methods are generally clear; however, as mentioned above, the authors need to also mention that they assessed chlorophyll in their introduction and methods.
Validity of the findings: No comment
Additional comments: General:

The authors present a study that proposes the ratio of macroalgae to vegetation (MA:TV) in South Australian estuaries as an indicator of ecological health and relate this to key catchment characteristics. A clear relationship between the % of fertilised land within a catchment and the MA:TV was identified. The manuscript is very well written and methods are appropriate for analysis. The potential factors influencing the MA:TV were selected apriori based on previous literature findings. Factors were examined for co-linearity, uninformative predictors removed and non-normal data transformed prior to analysis – all essential steps in having meaningful analysis. The results are, in general, presented clearly; however, there is some confusion around the inclusion of chlorophyll a in their assessment. I suggest that the authors mention that (and explain why) they assessed chlorophyll a in their introduction (perhaps in final paragraph where the aim is outlined) and mention the analysis in the methods (which I’m assuming is the same as for their prediction of MA:TV).

Specific:

 Lines 46-48. Please cite the claims made in sentence beginning “Despite this, phytoplankton dynamics...”

Lines 59-61. Sentence beginning “The ratio of macroalgae...”. Please provide a short sentence explaining why the ratio of seagrasses and macroalgae is sensitive to nutrient loading.

Lines 65-69. Please clarify what is meant by ‘continental scale, stream-and-nested-catchment framework”. Perhaps re-word to say “catchment characteristics...”

Line 71. At this point you introduce assessing chlorophyll a data yet your aims don’t mention chlorophyll a? Please expand on your aims to mention the use of chlorophyll a (i.e., that you’re using it and why) in your introduction/aims.

Line 89. Please expand on the methodology used by ‘GUMLEAF’ to calculate loads and why this method is preferred to alternative methods.

Line 112. Jags is an acronym so change to JAGS.

Line 124. Where is the the R2 and p-value from? Is this also from heirarchical partitioning? If so then please explain the use of chlorophyll a data in your methods (and aims as mentioned above).

Line 145. This could be a good point to mention how, other than increasing nutrient loading, that fertilised land can affect MA:TV. Also total area of fertilised land doesn’t take into land use type and intensity or the attenuation capacity and lag time of the vadose zone (which will differ between catchments). Figure 2 from Elwan et al (2015) shows the spatial variability in attenuation between neighbouring sub-catchments. https://www.massey.ac.nz/~flrc/workshops/15/Manuscripts/Paper_Elwan_2015.pdf

Line 153. Whilst the dilution of the estuary may differ, won’t this occur of a gradient? So the areas closest to the mouth may still have high nutrient concentrations. Do you have estuary nutrient concentration data to support this claim?

Line 155. Are they ‘measures’ or does the sentence need re-wording? This sentence is currently confusing but seems crucial to understanding the following list. I’m currently not entirely sure why there is a list of attributes, is these hypotheses on factors which may be influencing the MA:TV ratio? The paragraph also seems incomplete without a brief mention on why each of these factors may affect MA:TV and the likeliness that they are impacting your systems.

Line 163. From Figure 1 it appears that the impact of increasing fertilised land ceases to change the MA:TV after ~20-40%, why might this be? Why doesn’t MA:TV change linearly with increasing fertilised land?

Line 172. That’s an interesting finding. I’d be curious to see what kind of vegetation composed the foreign forests you compared to (no need to comment on this in manuscript).

Line 187. Ecological consequences to increasing macroalgae i take it?

Line 222. Please explain this interaction model in your methods.

Line 229. Does MA:TV differ depending on where within the estuary it is surveyed? Or do your estimates cover the entire estuary?

Tables 1 and 2. Please reword your Table captions. It is insufficient just to say that it is a table of results. Ideally a table should be able to be read and understood without having to read the main body. Also expand on what you mean by pr(inc) and ß as many readers will not be readily familiar with your techniques and chosen notation. Please also indicate what the abbreviations you’re adopting (or write them in full) in your table, i.e., what does “Tf” represent? When you say “Values >0.75...” please be specific about what values you’re talking about, i.e., the Bayesian variable selection.

Table 3. Since you only measured 14 sites, it wouldn’t be too cumbersome, yet highly informative, if you could please show the export rates and land-use for all 14 sites rather than a summary.


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: CATCHMENT LAND USE PREDICTS BENTHIC VEGETATION IN SMALL ESTUARIES
Review round: 1
Reviewer: 2

Output:
Basic reporting: 1. Hypotheses: I thought these could be better explained. Lines 65-69 has a dense and long sentence describing what the authors did, but there is no mention of what they expected to find. Also reiterating why this expectation might be useful from a management perspective would be helpful.
Experimental design: 1. Data transformation: Please explain why the proportion data was not logit-transformed for hierarchical partitioning (see Warton, D. I. and Hui, F. K. C. 2011. The arcsine is asinine: the analysis of proportions in ecology. Ecology, 92: 3–10).
2. Statistical approaches: It would be useful if the authors described why the respective statistical methods (Bayesian variable selection and hierarchical partitioning) were used. These are appropriate, but it would be helpful for the readers to know what they do and why this is important for the data analysis of this study. For example, see Hatt et al. 2004: "This method allows identification of variables whose independent correlation with the dependent variable is strong, in contrast to variables that have little independent effect but have a high correlation with the dependent variable resulting from joint correlation with other independent variables." (Hatt et al. 2004. The influence of urban density and drainage infrastructure on the concentrations and loads of pollutants in small streams. Environmental Management, 34, 112–124.)
3. Data transformation: Please state which predictors were right-skewed, and thus log-transformed (Lines 104-105). You can refer to Tables 1-2 to save space (but see comment 1 above).
4. Site selection: It would be useful to quickly describe the selection criteria outlined in Woodland et al. (2015) here. This would help assuage any concerns that the sites had been “cherry-picked” for the non-linear response shown in Figure 1.
Validity of the findings: 1. Validity of threshold response: The authors have identified a threshold of >20% of the catchment fertilized and estuarine macroalgal dominance (e.g. lines 122-123). While this seems reasonable, it would be good if this were tested objectively. Two approaches spring to mind: change-point analysis and non-linear regression ´curve´ fitting. For an example of how to use these two methods to validate an areal threshold see Burdon, F. J. et al. 2013. Habitat loss drives threshold response of benthic invertebrate communities to deposited sediment in agricultural streams. Ecological Applications, 23: 1036–1047. It should be noted that there are new ways to implement changepoint analyses in R (see Killick, R. & Eckley, I. A. 2004. Changepoint: an R package for changepoint analysis. Journal of Statistical Software 58, 1–19). Nonlinear regression fitting can make use of the "nls" and "AICc" functions in R. The latter function is in the "AICcmodavg" package. This would help describe objectively the shape of the relationship. It is important to note that the data should not be transformed for these analyses, because elucidating the actual threshold is the goal here (although OK to test a log-linear model with other candidate regression models). You can plot nonlinear regression lines a number of ways in R, one way uses "ggplot2".
2. Proximate and ultimate drivers of macroalgal cover: Although the authors discuss this issue (e.g. Lines 125-137), I wondered if a simple structural equation model (SEM) could not cast some more light on the interplay between catchment fertilization, river nitrogen loading, and estuarine macroalgae cover (keep in mind though caveats about site replication). For example, there should be indirect effects of catchment fertilization mediated through river nitrogen loading on estuarine macroalgae cover, but also a direct effect of catchment fertilization not related to river nitrogen loads (as hypothesized in Lines 156-161). SEM would be an objective way to assess causality, and its inclusion would add greater depth to the manuscript. Burdon et al. (2013) also make use of this statistical approach, but there are new R packages that can perform SEM analyses (e.g., see the "lavaan" package and the supplementary information in Grace, J. B., et al. 2014. Causal networks clarify productivity–richness interrelations, bivariate plots do not. Functional Ecology, 28: 787–798). This is important, because the “take home” message in Woodland et al. 2015 was that nitrogen load was the main driver of primary productivity in the same estuaries, but here you find that landuse (as an integrator of intensive agricultural activities) is a stronger predictor of estuarine macroalgal cover.
3. Residence times (Lines 213-214): How do the residence times of your systems compare to other estuaries around the world? It would be useful to quantify the "relatively" short duration here, and also help place your findings in the global context for the readers.
4. Mechanisms of threshold response: There is a rich literature on ecological stability and the abrupt transition from one system state to another. Although the authors do not have sufficient predictor variables or site replicates to test the underlying mechanisms of this complex system response objectively (but the simple SEM suggested above would be a move in the right direction), they could discuss their observation more with other related phenomena (e.g., state shifts to cyano-bacterial dominated algal assemblages in lakes). This would be helpful in further suggesting ways to move the science to a more predictive basis and away from description (which is useful as well - identification of thresholds have high utility for management). For a primer on this I can recommend Beisner et al. 2003. Alternative stable states in ecology. Frontiers in Ecology and the Environment 1(7): 376-382.
Additional comments: 1. Lines 56-57. Is sedimentation and eutrophication of estuaries resulting from changes in catchment landuses not related to seagrass declines? Perhaps make this point a bit clearer.
2. Lines 65-69. This a long sentence. I would consider breaking it up and make the points clearer and more concise. Also see comment above under the "Basic Reporting".
3. Line 29. Delete "great".
3. Line 29. Add "...value by supporting..."
4. Line 30. Oxford comma between "...highly productive fisheries, and recreational...". Do you have a reference for these ecosystem services?
5. Line 31. "bear the brunt" is idiomatic. Consider rewording to "...estuaries are impacted by increased..."
6. Line 100. Replace "elided " with "discarded".
7: Lines 120-121. Reword to "was positively associated...".


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: CATCHMENT LAND USE PREDICTS BENTHIC VEGETATION IN SMALL ESTUARIES
Review round: 2
Reviewer: 1

Output:
Basic reporting: 1.	Hypotheses: The Authors have greatly improved the Introduction. Their Aims are stated unequivocally, and the utility of their approach to management clearly highlighted.
Experimental design: 1. 	Data transformation: The Authors have explained that they did not logit-transform the proportion data because the “use of any transformation that achieves the unskewed-even spread empirically is sufficient”. There is a reasonable spread in the data which suggests this is probably true, but it would be more comforting if it were reported that the logit-transformation was attempted and did not qualitatively affect the results.
2. 	Statistical approaches: I have cited Ralph MacNally’s work on hierarchical partitioning, so am familiar with this contribution to the ecological literature. The example I provided previously comes from the R documentation authored by Walsh and MacNally, which I found useful when describing this method in my 2008 paper “The linkage between riparian predators and aquatic insects across a stream‐resource spectrum” (Freshwater Biology 53, 330-346). Nevertheless, it pleased me to find that the Authors have improved their descriptions of the analyses used in this manuscript. It is now clear why and how they have applied Bayesian variable selection and HP for this research.
3. 	Data transformation: OK, but see comments above re point 1.
4. 	Site selection: The Authors have provided the additional information required.
Validity of the findings: 1. Validity of threshold response: The Authors have justified not objectively testing the stated threshold because “The key point here is that once catchment fertilization exceeds 20%, > 50% of the SAV is macroalgae (i.e., macroalgal dominated)”. Whilst I agree that the change in areal coverage is probably asymptotic, I would be much less confident to state that “this is just a phenomenological observation and nothing to do with a formal phase transition to another state per se”. There seems to be an element of confirmation bias in this view. Thresholds values are highly useful for management, and objective testing is not something to be dismissed out of hand. It has much less to do with “deepening our understanding”, and more with defining explicitly a value with utility for managers. I personally would find this work more useful if the threshold value were defined using changepoint analysis, as opposed to the current interpretation which is like ‘it seems to change somewhere around here’.
2. 	Proximate and ultimate drivers of macroalgal cover: The Authors have justified not using SEM here because of the low level of site replication. This is reasonable with data for only 14 sites. However, I would encourage them to consider using this approach in the future, given the high likelihood of complex interactions/contingencies with the stated predictor and response variables.
3. 	Residence times: Good stuff - references provided and a caveat issued about residence times.
4. 	Mechanisms of threshold response: The Authors have backed off from using “transition” in their article because it implies that the threshold elucidated is suggestive of a shift to a new ‘domain of attraction’, indicated by a much greater areal coverage of macroalgae (i.e., macroalgal dominance) in the studied estuaries. Whilst the Authors seem skeptical of such phenomena, it would seem irresponsible to discount this possibility out of hand. For one example, a stream study indicated that crossing a nutrient threshold may lead to synchronous declines in sensitive alga species with simultaneous increases in tolerant species associated with increasing enrichment (Taylor, J. M., King, R. S., Pease, A. A. and Winemiller, K. O. 2014. Nonlinear response of stream ecosystem structure to low-level phosphorus enrichment. Freshwater Biology, 59: 969–984).
Additional comments: The Authors have made many changes that have improved the manuscript. However, they have been resistant to certain suggestions. The changepoint analysis might show no clear change (or a large 95% CI) because of the relatively low site replication, but that would still be a result worth reporting, because validating the threshold would enable comparison with future studies.


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: ONTOGENY OF LONG-RANGE VOCALIZATIONS IN A NEOTROPICAL FOSSORIAL RODENT: THE ANILLACO TUCO-TUCO (CTENOMYS SP.)
Review round: 1
Reviewer: 1

Output:
Basic reporting: The paper is generally well-written and organized. Multiple minor issues with word choice are listed with suggestions for improvement in General Comments. A couple of broader citations would improve scope of first paragraph of intro (see General Comments). The figures are very nice.
Experimental design: The study is of interest and, despite small sample sizes, definitely worthy of publication. The research questions are well-defined although the authors should consider whether their data can really address their second aim (vocal learning vs. vocal tract development). Additional information is needed in Methods (see General Comments).
Validity of the findings: Overall, the findings are valid because this is primarily a descriptive study. However, the statistical tests used are not appropriate to the data (see General Comments). The Discussion is quite good but I strongly encourage the authors to consider and discuss how vocal function and the context in which vocalizations are produced change over ontogeny in their own study species and others.
Additional comments: Title and throughout: The Anillaco tuco-tuco referred to as Ctenomys sp. Is this an undescribed species? If so, how is it distinguished from congeners? Some explanation that goes beyond referring readers to another publication from this research group is needed.

Abstract, L304: change undistinguishable to indistinguishable

Introduction
L46: “vocalizations experiment an ontogeny”. Experience? A better phrase might be, “vocalizations follow a developmental trajectory”
L47-51: Both citations here are for empirical papers. It would be better to have other citations to support these general opening statements.
L62: change “to” to “into”
L85: suggest removing “simply”
L88: change “can help understand how” to “can improve understanding of how”
L91: change “of” to “to”
L94: change “composed by” to “composed of”
L97: Not sure that abnormal is the right word. Abnormal has negative connotations for functionality whereas it sounds like these alternate vocal patterns are simply atypical/uncommon.

Materials and Methods
Please explain how juveniles were acoustically isolated from adults and address whether or not they were acoustically isolated from each other. Also, please provide some life history info that will place the term “juvenile” in a species-specific context: typical age at weaning (14 days seems very young), and age at sexual maturity for male and female Anillaco tuco-tucos. (Having read discussion I see that the latter is unknown; that should be stated here and at least a rough estimate could be provided based on other Ctenomys) Please provide sufficient information on the enclosure that readers can assess how the animals were maintained (e.g., group housed? Size of enclosure? Inside or outside?) and how acoustic data were collected without reading Amaya et al. 2016. This is particularly important for the “Recording of vocalizations” section. Were the animals recorded in their home enclosures or elsewhere? It sounds like they were recorded singly but this isn’t completely clear.

L162-170: Please clarify what 90% means in relation to duration and bandwidth.
L158-186: As I understand it, the way acoustic parameters were measured for triads and individual notes was very similar if not identical. Suggest combining the two sections to reduce redundancy in text.
L188-187: Some of this is redundant with lines 148-153.
L199: As above, consider changing abnormal to atypical.
L215: The Spearman correlation is not appropriate for the data because repeated measures collected from the same individuals are non-independent. It’s fine to plot the data as the authors have in Fig. 5 but to test for an effect of change in age (weight) on change in acoustic variables would need repeated measures ANOVA or a GLM with individual ID as a random variable. Same goes for the Kruskal-Wallis test.
L231-237: Ethics statement would be more appropriate at the end of Experimental animals and info on the stats package should go at the end of Statistical analyses.

Results
L243-244, 251 and elsewhere: change “were given” to “were produced” and “gave” to “produced”
L266: change “lumped” to grouped or split.
L271-272: This sentence is quite vague. Please be more specific as to how vocalizations achieved mature features at different developmental stages.
L280: change “conformed by” to “comprised of”
L282: “obviously” is subjective. A statistical test would be nice but if sample sizes make that impossible at least use numerical evidence. e.g., 7.8% is more than an order of magnitude > than 0.28% or, “abnormal” series were >25x more common in juveniles. Also, if reporting frequency of an event as a percentage should change proportion to percentage.

Discussion
L304-306: Need to acknowledge that, while this study did not find evidence for vocal learning, it also did not effectively test this hypothesis since the study animals were exposed to adult vocalizations for at least the first two weeks of life and it’s currently not clear whether juveniles were isolated from each other. This is addressed later in the Discussion, but if the authors want to include a statement about vocal learning in the first paragraph it should be modified.
L307: Again, how do the authors know that these “abnormal” vocalizations reflect poor motor control etc? How do they know that they don’t have a function in juveniles and/or adults? Without information on the context in which different types of vocalizations are produced, can’t assume that these vocal types are “mistakes”.
L332; 333-336: change “substantial genetic makeup in” to “substantial genetic contribution to”. Please clarify why the presence of series patterns in congeners supports the suggestion that there is a genetic basis to vocal patterns in the study species.
L337: tuning
L337-347: Again, I encourage the authors to consider how the function of vocalizations in their study species, and in other rodents, changes between birth and maturity.
L361: song has not been used previously to describe this species’ vocalizations, suggest changing.
L363: please clarify what “conformed only by series” means.
L369: Not all researchers agree that vocal learning is completely absent in rodents. See Jarvis 2006, Ornithological Science; Arriaga et al. 2012 PLoS ONE; Arriaga and Jarvis 2012 Brain and Language and papers citing these papers for ongoing debate.
L380: Listen is subjective. If the auditory meatus is open from birth then these animals can probably hear from birth.  Standard ways to test for a contribution of learning to the development of adult vocalizations are complete acoustic isolation (very hard to do in mammals without deafening) and cross-fostering to a closely related species with different adult vocal patterns.
L391, 393: Change presumably to presumptively; “alleged” has negative connotations re. the conclusions of Camin 2010. Consider changing.
L397, 401: Georychus capensis
L403: occurs
L409: superficial?
L411, 413: Hooper, not Hopper. Also, this citation is missing from Bibliography.


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: ONTOGENY OF LONG-RANGE VOCALIZATIONS IN A NEOTROPICAL FOSSORIAL RODENT: THE ANILLACO TUCO-TUCO (CTENOMYS SP.)
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript is of interest, at elast for scholars and students interested in acoustic communications and rodents. It is sound, scientifically valid, well structured and celarly written. In my view, it fulfills all the criteria put on papers published in Peer J. I have only minor comments, although some of them (esp. that one concerning the age of the studied animals) must be addressed:
1) The authors state (Lines 122-130) that the captured juveniles were weaned individuals between 2-4 weeks old, and had weight of 33 g. According to Camin (2010), a paper the authors are also citing, weaning (in C. mendocinus) occus at the age of 56 d.a.b. and weight of 117 g. This discrepancy should be clarified.
2) (Lines 385-390) - It is argued that slow development in Ctenomys is due to its subterranean way of life. This is only partly true. More importantly - this is a common feature of all hystricognaths rodents!
3) Bathyergus siullius and Georinchus (line 397 and further on) - correct spelling is suillus and Georychus
4) unify writting vs - either with dot vs. or without vs
5) unify writing number and percent - either with space xx % or without xx%
6) In many cases there should be "the" after all: all the experiments, all the individuals, all the parameters etc. instead of all experiments, all individuals etc.
7) Line 46: I do not understand the sentence:
Like many other aspects of biological systems, vocalizations experiment an ontogeny.
(perhaps experience instead of experiment?)
Experimental design: I have no comments
Validity of the findings: The findings are valid
Additional comments: See above


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

Input:
Title: ONTOGENY OF LONG-RANGE VOCALIZATIONS IN A NEOTROPICAL FOSSORIAL RODENT: THE ANILLACO TUCO-TUCO (CTENOMYS SP.)
Review round: 1
Reviewer: 3

Output:
Basic reporting: see below
Experimental design: see below
Validity of the findings: see below
Additional comments: In general the manuscript present nice data showing developmental changes in the structure of long range vocalization of Anillaco Tuco Tuco. The problem with manuscript is the theoretical framework in which the author put their findings. Beside this there are some serious statistical problems.
1) Vocal learning vs. vocal maturation:  The authors found no evidence for vocal learning which is not surprising because until now none of the studies describing developmental changes in rodent vocalizations found evidence of vocal learning. Their conclusion that the age related structural changes are related to maturational changes of the vocal tract is not very conclusive: First, the authors did not measure any vocal features which could describe changes related to vocal tract changes. Bandwidth and peak frequency do not describe formant structure. Insofar the authors have no measure whether changes in the vocal tract really lead to changes in the acoustic structure of these vocalizations. Further, looking at Fig. 5 makes clear that already juveniles at a weight of app. 80g have the same note structure as adults. The only difference which remains is sequence composition and number of notes. But this has nothing to do with vocal tract changes.
In addition it remains unclear to which degree adults and juveniles differ in sequence composition and number of notes. The tests (L266-270) seem to be wrong. In table S3 they make correct tests, one test per subject. But in this paragraph it seems that they combine the repeated measurements of their subjects. This cannot be tested with such tests. A chance level below 0.0001 having only three females is also a good sign that something is wrong. It is possible to use a simple pairwise test comparing old juveniles and adults.
2) Abnormal series in juveniles and adults: Independent whether it makes sense to use the term abnormal for the differences in the series, the major shortcoming is that the author forgot to take the motivation of the animals into account. The possibility that juveniles are already able to produce adult like vocalization but did not do it because they have no motivation is a general problem discussing factors underlying developmental changes. It is possible that they are already able to produce adult-like series but have no motivation.
3) Development of individual notes: The author found that only three subjects produced individual notes. None of the females produce single notes although they produce otherwise same notes as males. To me the meaning of these individual notes is totally unclear. Why are they produced only by these three males? Before making any developmental story out of it (“mixed developmental mode”), the author should try to find out whether there is any communicative relation with the production of these individual notes.
4) Life-history traits and territorial vocalizations …: This paragraph is very vague. In addition I cannot see why the development of the LRV is protracted about 110-120 days. Fig. 5 shows nicely that only very young subject differ in note structure. Juvenile seem to vocalize less but this could be simple due the fact that they have no motivation. If the authors could not come up with evidence that only the adults can produce the adult like version they should skip this part of the discussion.
5) It is unclear how the authors correct for multiple testing (e.g. Table S3).


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: ONTOGENY OF LONG-RANGE VOCALIZATIONS IN A NEOTROPICAL FOSSORIAL RODENT: THE ANILLACO TUCO-TUCO (CTENOMYS SP.)
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 done a very nice and extremely thorough job of revising this manuscript. It is significantly improved and will make a nice addition to the literature on vocal ontogeny in rodents.


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: ONTOGENY OF LONG-RANGE VOCALIZATIONS IN A NEOTROPICAL FOSSORIAL RODENT: THE ANILLACO TUCO-TUCO (CTENOMYS SP.)
Review round: 2
Reviewer: 2

Output:
Basic reporting: Most parts of the revised manuscript are clear and unambiguous.
The description of the different acoustic characterizations (L 199-239) is partly redundant, otherwise difficult to understand.
Similar table 2: Unclear why there are no p-values for “series per vocalization. What is the meaning of “A”, “B”, “C” & “D”?
Experimental design: no comment
Validity of the findings: The authors modified their statistical methods. Unfortunately not all changes led to a satisfactory result:
1)	The authors present only p-values (table2, Text L304-313, 333-336). This is not correct. At least they should give also test statistic and/ or total N.
2)	Again, it remains unclear whether the authors adjusted for multiple testing (pairwise statistic, several acoustic parameters).
3)	It is unclear how it is possible to get a p-value below 0.001 with two subjects (females) using Friedman test.
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: DIFFERENT INTENSITIES OF BASKETBALL DRILLS AFFECT JUMP SHOT ACCURACY OF EXPERT AND JUNIOR PLAYERS
Review round: 1
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: The authors have not defined ‘fatigue’ as either peripheral or central, so accordingly, cannot postulate that fatigue has actually been induced. Yes, the player’s heart rate and perceived exertion may have increased, but this is not because of heightened levels of fatigue – reinforced by the fact that the expert players jump height actually increased after the high fatigue protocol! Given this, I am almost certain neuromuscular fatigue was not induced, making the entirety of their results and discussion misguided.

The protocols used to ‘fatigue’ the players appeared nonsensical, and lacked construct validity. Why did the authors not use the protocols described by Scanlan et al. (2012 – The development of the basketball exercise simulation test)? This test was comprehensively developed, using local positioning system data extracted from game-play to inform its construct. Had the authors used this, it is likely they would have incurred ‘fatigue’.
Validity of the findings: The authors note a decline in performance of the junior group following the high fatigue protocol, citing the kinematics of the upper body being the confounding factor given the maintenance of jump height (again, showing the lack of fatigue actually induced). However, given no kinematic analysis was done, how can this be the author’s conclusion? More directly, I feel that the decline in shooting performance was more of a reflection of the attention shift participants are likely to have encountered given the perception of being ‘fatigued’ (see Maarten et al., 2005 – Effects of mental fatigue on attention: An ERP study).

Surely the expert players possessed a superior level of physiological fitness relative to the junior players? So, why did the authors not extract this data at the start and then modify the protocols to the relative physiological fitness of player groups? More directly, the ‘fatiguing’ protocol for the expert group could have simply been a warm up given the likely superior fitness they possess relative to the junior players, who are likely to have struggled more so with this protocol. Thus, are you not comparing apples with oranges?
Additional comments: The concept of fatigue and its impact upon jump shot accuracy in expert and junior basketball players is interesting. However, given the above points, I feel the study has just missed the mark here.

In addition to the more major commentary listed above, there are multiple minor points of concern throughout that the authors need to consider prior to re-submission.

Abstract
•	The first sentence is nonsensical – what is conditioning and related fatigue?
Introduction
•	The physiological parameters presented in Lines 39 and 40 hardly warrant the use of “Very severe”…. This is where I would be more inclined to focus on the movement demands of the players, as these are what would have impacted neuromuscular fatigue – making more sense for your experimental protocols.
•	No use of paragraphs throughout?

Results
•	Lines 122 – 123 – again, how can the authors state that fatigue has been induced? Jump height has maintained and actually increased slightly for the expert group! Further, the expert / junior differences are merely a reflection of training age, no?

General
•	Reference inconsistencies / Figure and Table captions on different pages.


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: DIFFERENT INTENSITIES OF BASKETBALL DRILLS AFFECT JUMP SHOT ACCURACY OF EXPERT AND JUNIOR PLAYERS
Review round: 1
Reviewer: 2

Output:
Basic reporting: There are a number of grammatical errors throughout the paper. I propose that the following changes be made for this paper to be accepted.

Abstract, Line 17- include a comma after basketball. Change to "In basketball, conditioning and related fatigue affect performance."

Abstract Line 17- include comma after moreover and remove "a". Change to "Moreover,  maximum accuracy is required while shooting."

Abstract, Line 18- include "The" and change second "study" to investigate.
Change to "The aim of the study was to investigate the effect of three different levels of fatigue on jump shot...".

Introduction, Line 38- I would suggest to change severe to specific.

Introduction, Line 41- remove "a" before maximum. Change to "Together with a high level of fitness, maximum accuracy is required..."

Introduction, Line 46- change "Similarly, it has been showed a detriment...' to "similarly, it has been found that a detriment...".

Introduction, Line 48- change "3 points-shooting" to "3 point-shooting". Keep consistent throughout the rest of the article.

Introduction, Line 52- change worsening to "reduction in accuracy".

Introduction, Line 55- change "considering" to "during".

Introduction, Line 56&57- change "indices" to "scores".

Introduction, Line 56- you have misinterpreted the results of the repeated-sprint study. There was no difference reported between total sprint time, after the warm up and after the game. Only difference reported was sprint at half-time.

Introduction, Line 59- change "showed" to "shown"

Introduction, Line 59- include training in between sport-specific and methods. Change to "...sport-specific training methods..." . Keep consistent throughout the rest of the article.

Introduction, Line 68&69- Include the jump shot in this sentence. "Our hypothesis was that fatigue could induce in both groups a decrease of the accuracy and jump height as exertion is increased during the jump shot."

Introduction, Line 70- change "with respect to" to "compared with"

Experimental Procedure, Line 86- change "minutes" to "minute" and "consisting in" to "consisting of".

Experimental Procedure, Line 87- change "free shots" to "free throw shots". Keep consistent throughout the rest of the article.

Experimental Procedure, Line 90- change "proved" to "moved".

Experimental Procedure, Line 92- change "Then he had to run..." to "The participant ran..."

Experimental Procedure, Line 94- change "he" to "they".

Experimental Procedure, Line 94- include a comma, change to "After reaching the cone, they performed a cutting manoeuver..."

Experimental Procedure, Line 102- change "always on that for all the trials" to "the same for every trial."

Experimental Procedure, Line 106- change "fly time" to "flight time".

Experimental Procedure, Line 110- change "prior the tests" to Prior to the tests."

Experimental Procedure, Line 115- include significance instead of statistically or write both e.g. "If the statistical significance..."/ "If the significance...".

Results, Line 122- change “set’ to “sets”.

Discussion, Line 155- change “contribute” to contributor”.

Discussion, Line 177- I would suggest changing “proposed” to “implemented”.

Discussion, Line 203- change “experts” to “expert”.
Experimental design: No comment. procedure is satisfactory.
Validity of the findings: No comment. Validity of findings seemed satisfactory.
Additional comments: I think the procedure used was scientifically sound. It was a good approach to investigating the effect of fatigue on shooting accuracy and a well thought out study design.

I agree with the implications for skill training in basketball provided in the 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: DIFFERENT INTENSITIES OF BASKETBALL DRILLS AFFECT JUMP SHOT ACCURACY OF EXPERT AND JUNIOR PLAYERS
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: The authors should be congratulated for addressing both reviewer comments with respect. Their rebuttal was sound and where necessary, they addressed the reviewer commentary in a sound way - well done.

I have no further commentary and wish the authors luck for their future research ambitions.


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: FACTORS ASSOCIATED WITH ELEVATED BLOOD PRESSURE OR HYPERTENSION IN AFRO-CARIBBEAN YOUTH: A CROSS-SECTIONAL STUDY
Review round: 1
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: The authors report an interesting cross-sectional study on factors associated with prehypertension in 898 young adults (mean age, 18.8 years). All subjects were born between September and October 1986, then similar in terms of age.
The study describes the burden of metabolic disorders such as obesity, high glucose and triglycerides in this large cohort of young Afro Caribbean adults. Authors show that metabolic disorders and socioeconomic status are associated with prehypertension a clear risk factor of hypertension development. Gender analysis is also interesting and discloses differences in prehypertension associated factors.
The study results may be able to support public health policy option to decrease the prevalence of metabolic disorders in young Afro Caribbean adults.

I have only minor concerns

1)	In Table 3: I think that the 3 stars associated with “Binge Drinking” should be deleted.
2)	In Table 4: The factor “Parental Occupation” may be deleted from the table since no association with prehypertension in multivariate analysis is shown.
3)	I suggest that authors could propose that the results of their study may support  a public health policy that focused on metabolic disorders decrease in childhood and in young adults.


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: FACTORS ASSOCIATED WITH ELEVATED BLOOD PRESSURE OR HYPERTENSION IN AFRO-CARIBBEAN YOUTH: A CROSS-SECTIONAL STUDY
Review round: 1
Reviewer: 2

Output:
Basic reporting: This paper is presented in a clear, unambiguous, and professional manner, it conforms to professional standards of courtesy and expression. The authors have done a reasonable job and citing the most up to date references, although they have neglected to report on the CVD outcomes from the Modeling the Epidemiologic Study, a large cohort study currently following young adults (25-45yrs) in Jamaica, and 4 other African-origin adults e.g. Cardiovascular risk status of Afro-origin populations across the spectrum of economic development: findings from the Modeling the Epidemiologic Transition Study. Dugas LR, Forrester TE, Plange-Rhule J, Bovet P, Lambert EV, Durazo-Arvizu RA, Cao G, Cooper RS, Khatib R, Tonino L, Riesen W, Korte W, Kliethermes S, Luke A. BMC Public Health. 2017 May 12;17(1):438. And Elevated hypertension risk for African-origin populations in biracial societies: modeling the Epidemiologic Transition Study. Cooper RS, Forrester TE, Plage-Rhule J, Bovet P, Lambert EV, Dugas LR, Cargill KE, Durazo-Arvizu RA, Shoham DA, Tong L, Cao G, Luke A.J Hypertens. 2015 Mar;33(3):473-80; discussion 480-1. The current study should be discussed in relation to these findings.
Furthermore, many of the methods are not referenced (e.g. Physical activity questionnaire?) and some of the sentences are incomplete: e.g. sentence 88: where do estimates range from 2-19%, and were are estimates ranging from 12-45%?
The authors also present prevalence data for Jamaica: lines 107-111, however prevalence may be changing as a result of increased screening, it would be helpful to know incidence data. Perhaps increases are simply as a result of more people undergoing screening.
The authors are inconsistent throughout the manuscript with the use of abbreviations. Sometimes they use the abbreviation before the word is defined, other times they present the whole word, and then only abbreviate later.
This reviewer also feels that there are too many tables (especially supplemental tables), representing models that do not change the outcome of the paper, or fail to reach statistical significance.
The authors have submitted a paper which was rejected by another journal, and not removed the edits or formatting requested by that journal. It is recommended that the authors submit a clean version of this manuscript, fulling PEERJ’s formatting style.
Experimental design: While the overall aims, and research question are well presented and the paper does present with some novel findings there are several issues for this reviewer.
1) It is not clearly stated that participants were overnight fasted
2) How is the WHR defined?
3) HOMA-IR used fasted insulin and glucose, which is presented in the paper, why not calculate it?
4) No reference for the physical activity questionnaire
5) No references for SES questionnaires
6) The authors imputed biochemical data, this is a serious weakness in the current data. There is no data presented to show how the associations changed with or without the imputed data? Also up to a quarter of some of the variables were missing: Family history of HTN. This would seem to be a major flaw if HTN data is missing?
7) The authors did not adjust their models for smoking/ganja, this seems as a major flaw for predicting future risk for HTN.
Validity of the findings: This paper addresses a unique population for early diagnoses of HTN among young adults. However, this reviewer has several issues with the statistical analyses (lack of adjusting for smoking), and imputation of missing variables (how do outcomes change with or without imputation?). The paper also does not include several references, see basic reporting section. Throughout the paper, it is not clearly stated who comparisons are being compared to, e.g line 326-327. This reviewer suggests cutting down on the tables, particularly those representing models that fail to reach statistical significance. The authors have complied with the data sharing policy.
Additional comments: Overall this is a well written paper presenting novel findings in an under-studied age group. This reviewer suggests that the authors be given the opportunity to address the comments, and particularly the analyses and then resubmit their 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: FACTORS ASSOCIATED WITH ELEVATED BLOOD PRESSURE OR HYPERTENSION IN AFRO-CARIBBEAN YOUTH: A CROSS-SECTIONAL STUDY
Review round: 1
Reviewer: 3

Output:
Basic reporting: No comment
Experimental design: The study is a retrospective case control study with cases defined as Afro-Caribeean youth having elevated blood pressure (either pre-hypertension or hypertension)  The reviewer congratulates the research team in recognising the important contribution that pre-hypertension plays as a cardiovascular risk factor   The study seeks to fill an important evidence gap pertaining to elevated blood pressure in youth from a specific ethnic group.
My concern with the study design is the lack of a subset analysis looking at hypertension (preferably stratified into Type I and Type II hypertension).  The reason for this is two fold.  Firstly, from a public health perspective understanding the risk factors for youth with established hypertension as opposed to just pre-hypertension is important as it assists in prioritising preventive action.  The other reason is that readers less familiar with the concept of pre-hypertension may be misled by the combination of cases being defined as elevated hypertension.  By reporting the results categorically, and combined it will better inform readers and inform practice.  I appreciate that the prevalence of hypertension is low which may preclude this sort of analysis however this should be mentioned explicitly if the authors believe this is the cas.e
The association between increased ACR and hypertension is not mentioned in the results - despite this data being available.  I would like to see this finding mentioned.  As an early marker of renal impairment it would be interesting to know if it contributes to elevated BP in this group.
The research question is well defined and appropriate methodology and statistical analysis is used.

(5)  Ethical clearance for the article was evidenced.
Validity of the findings: (1)  In the discussion I would like to see further comparison with other studies of elevated BP in youth.  Eg the gender difference that was found here has been found among Australian Indigenous youth.
(2)  The limitations of the study are appropriately delineated.
(3)  Further exploration of the public health implications of the study would be beneficial
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: FACTORS ASSOCIATED WITH ELEVATED BLOOD PRESSURE OR HYPERTENSION IN AFRO-CARIBBEAN YOUTH: A CROSS-SECTIONAL STUDY
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Author's answers are appropriate with my requests.
I have no more comments
Thank You


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: CALIBRATION ADJUSTMENTS TO ADDRESS BIAS IN MORTALITY ANALYSES DUE TO INFORMATIVE SAMPLING—A CENSUS-LINKED SURVEY ANALYSIS IN SWITZERLAND
Review round: 1
Reviewer: 1

Output:
Basic reporting: Clear and unambiguous english is used for the most part making the manuscript comprehensible. Some editorial revisions including the suggestions to the author below  would improve clarity.
Experimental design: The authors effectively demonstrate how a survey-based census system without consideration for differential non-response, such as that adopted in Switzerland, will impact the validity of survival and/or mortality analyses. They do so by comparing mortality rates and life expectancy derived from survey weights with those derived from inverse probability weights using survival data from the country’s Vital Stats Registry and taking into consideration survey non-response data. The analysis is adequate and understandable, with appropriate tables and figures, provided table 1 is modified. The findings and conclusions are accurate and of importance.
Validity of the findings: While the overall findings are valid and important and the conclusion is well stated, the general context of this research question is not discussed especially the practical implications of these findings (IMPACT). Moreover the baseline data of STATPOP could be better described. For the rest, the data seems robust , statistically sound and controlled.
Additional comments: I read the manuscript by Moser et al. with great interest. The authors effectively demonstrate how a survey-based census system without consideration for differential non-response, such as that adopted in Switzerland, will impact the validity of survival and/or mortality analyses. They do so by comparing mortality rates and life expectancy derived from survey weights with those derived from inverse probability weights using survival data from the country’s Vital Stats Registry and taking into consideration survey non-response data. The analysis is adequate and understandable, with clear, appropriate tables and figures. The findings and conclusions are accurate and of importance. Some concerns are as follows:   Major concerns:

•	While the manuscript shows that estimates based on survey weights will be underestimated (MR) and overestimated (LE), it falls short of explaining the impact or significance of this concern. For population-based studies on vital statistics, one could always fall back on the STATPOP file; thus, it is important for the authors to convey what the consequences of this difference in estimates might be in practice, ideally providing concrete examples.
•	It would be advantageous to provide the regional European context. Is this a local problem, or are other countries reverting to the same census plans?
•	Survival Concerns: Please discuss the completeness of mortality records for linkage with STATPOP. Regarding the mortality records of non-Swiss populations (roughly 20% according to Table 1), what is the “lost to follow-up” rate? How is vital status ascertained? (death certificate alone? Regular collection of “state income or pension” anywhere in the world? Etc.) What about people moving to warmer geographies or to their countries of origin and dying there (some with the authors’ exact characteristic of interest - poor health status)? How would these aspects affect the survival used for the IP weights? Furthermore, due to the overlap with poor health status, how would it affect the estimates of the current study? At minimum, these concerns could be addressed in the limitations section.
•	Non-Swiss populations have significantly lower odds of response to the survey, but the effect of that was not discussed. Please also clarify if cross-border workers to cities like Geneva and Basel are included in STATPOP –as part of the Swiss population - and/or the survey?

Minor suggestions:

•	The word “informative” may come across as positive to the less informed reader. The text should be modified so that “informative” is clearly portrayed as an unwanted characteristic.
•	Please check the order of the Figures. Currently starts at 3.
•	Lines 129-131: Is the survival time individually updated as per some sort of contact with the subject or is survival time measured throughout the full period presuming the subject is alive in the absence of a death record?
•	Line 144: Does the OR=4 come from Pizzi et al. as well? If not, please substantiate your choice.
•	Line 149: The sentence “The overall percentage of deaths was set to 10% and 25%” needs to be clarified with information regarding which group or data subset is involved.
•	Lines 262-263: This sentence is best suited for the Introduction.
•	Lines 303-305: This statement is an overreach and possibly wishful thinking. Readers will understand that resource shortages are driving countries towards novel approaches to counting their populations. Yet, as researchers, we know that there is no real substitute for a Full Enumeration Census (albeit also imperfect). To suggest that surveys and statistical estimates could ever replace an actual total count is bold at the least, and surely contentious, unless Switzerland is unique and there is a total absence of undocumented persons, the “lost-to-follow-up” rate is zero, and the borders are fully controlled. I would strongly consider modifying this segment of text.

Minor language/word choice concerns:

While the manuscript is comprehensible, some editorial revisions including the following would improve clarity.
1-The use of the word “register” is awkward
2-The use of the word “consistent” -it often seems like the authors actually mean accurate or valid
3- “Despite” is not used correctly; sentences using it should be modified.
4- The use of future tense in some sentences is odd/unusual.
5- Other awkward phrases:
	true underlying population estimates (need a better word for “true”)
	they address for the sampling
	because of privacy preservation
	a bad health status
	studies including Switzerland
	state-of-the-art nowadays
	provided almost
In addition, table 1 is confusing and should be modified, possibly with horizontal lines.


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: CALIBRATION ADJUSTMENTS TO ADDRESS BIAS IN MORTALITY ANALYSES DUE TO INFORMATIVE SAMPLING—A CENSUS-LINKED SURVEY ANALYSIS IN SWITZERLAND
Review round: 1
Reviewer: 2

Output:
Basic reporting: 1.	Throughout the article, the switch from a full census to a survey-based micro-census is provided as justification for the work. Presumably, however, full censuses also have non-response and the same conclusions could apply (i.e. inverse probability weights would still improve the longitudinal validity, despite their not being a sampling probability). Please clarify the generalizability of your findings, and if they are generalizable beyond this micro-census scenario, perhaps use a different motivation to justify your study.
2.	Abstract: Define a registry-based census. Be consistent with calling it either a registry-based or register-based census.
3.	Line 35: Describe who the 6.5 million individuals are (i.e., all persons included in the registry-based census)
4.	Line 37: Clarify “aimed to be sampled”. Presumably 3.5% were sampled, but not all responded? Perhaps remove “aimed to”
5.	Line 74: “the statistical analyses” is vague – what statistical analyses?
6.	Lines 80/81: This sentence is very general and therefore confusing. I would differentiate between what your aim was (specific, mortality rates) and its implication (potentially broader, any time to event data)
7.	Line 94: Remove “will”
8.	Lines 111, 121: English language editing needed.
9.	Line 136: Figures should be numbered in the order they appear in the text
10.	Lines 140, 242, Figure 3: Replace “a bad health” with “poor health status” throughout.
11.	Line 185, Table 1: I may be ignorant given that this is not my area of expertise, but are the mean CS and IP weights informative to the reader? I am not sure how to interpret these in Table 1 and wonder whether there is use in them being there?
12.	Figure 2: Suggest making the x-axis categorical with the different methods across the x-axis. Could also consolidate to one graph.
Experimental design: 1.	The simulation study seems like a bit of an afterthought, both in the presentation and the interpretation of the results. I suggest either fully justifying the usefulness and implications of the simulation study, or leaving it out altogether.
Validity of the findings: No comment.
Additional comments: Overall, I think this is a well-executed and thorough study that is well described and has valid findings. Some English language editing is needed and some further clarification of the generalizability and implications of the results would improve the paper, but on the whole it seems to be a quality piece of work worthy of 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: THE STATE OF OA: A LARGE-SCALE ANALYSIS OF THE PREVALENCE AND IMPACT OF OPEN ACCESS ARTICLES
Review round: 1
Reviewer: 1

Output:
Basic reporting: This article is well and clearly written, and is characterized by (to the extent possible, given the subject matter) an admirable avoidance of jargon. It is well organized, with clear and logically-arranged sections. However, the authors do need to review their references: in at least one case, they cite an article in support of a point not addressed in that article, but rather in another one by the same author that is uncited in this piece. All data sets, including the source code for the tool under examination, are made publicly available.
Experimental design: Given that PeerJ "considers articles in the Biological Sciences, Medical Sciences, and Health Sciences" and "does not publish in the Physical Sciences, the Mathematical Sciences, the Social Sciences, or the Humanities (except where articles in those areas have clear applicability to the core areas of Biological, Medical or Health sciences)," it is not clear to me that this article is strictly in-scope. This strikes me as a piece that would fall within the category of the social sciences. However, the tool under discussion certainly has application to publications in biology, medicine, and the health sciences, so PeerJ's editors will have to decide whether the subject connection is strong enough to merit inclusion.

The research methodology described in the article strikes me as perfectly sound, and the authors' interpretation of the results seem reasonable to me.
Validity of the findings: The findings strike me as sound. Not everyone will necessarily be driven to the exact same conclusions from these data as those arrived at by the authors, but since the data are provided openly, there's no reason why those who disagree can't come to their own conclusions. This article adds a valuable and (I think) important piece of the puzzle in our ongoing quest to understand the OA publishing ecosystem.

The article's most significant problem is not related to its content, but rather to the fact that its authors have (unless I missed the disclosure somewhere) failed to disclose a serious conflict of interest. Nowhere in the article, that I can determine, is it revealed that both unpaywall and oaDOI are products of Impactstory -- the company of which the paper's first two authors are founders and principals. In fact, at several points in the paper (notably the final paragraph of its Discussion and Conclusion section, which states "this paper clearly shows the potential of the oaDOI service for future research"), it begins feeling like an infomercial for Impactstory's products. A particularly attentive reader might notice that the links to source data for the study lead to Impactstory domains, but this doesn't seem sufficient: instead, the lead authors should say right at the beginning of the paper that they are principals in and cofounders of the company that produces the tool the performance and potential of which are under examination in this article.
Additional comments: No additional comments


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

Input:
Title: THE STATE OF OA: A LARGE-SCALE ANALYSIS OF THE PREVALENCE AND IMPACT OF OPEN ACCESS ARTICLES
Review round: 1
Reviewer: 2

Output:
Basic reporting: Overall the article is well written and structured.  There are some minor formatting issues with citations that should be reviewed and cleaned up (e.g. see first paragraph of lit review). I was surprised that Walt Crawford's extensive work on OA Journals wasn't referred to, but that may have been deemed out of scope.

The figures do not translate well to black and white and minor revision to make that more clear is recommended. The bar charts were incredibly difficult to understand without the color. This also made it unclear if the keys and the charts aligned.

A couple of typos scattered throughout (e.g. under definition of ASNs "we we"

Formatting of the definitions of OA vary a lot -- citations bounce all over the entries. Please update for consistency.

Raw data was available. Thank you for the very clear dictionary.
Experimental design: On Page 8 the authors mention using a broader date window than the Archambault sample -- was this only for the WOS portion? Please clarify.

On the top of page 11 where the authors describe the article assignment to discipline. It was unclear how the authors determined which journals were multidisciplinary and how articles were then further assigned. Was this by hand?
Validity of the findings: no comment
Additional comments: Overall I really enjoyed reading this paper. I made comments as I went through and found nearly all of these addressed later in the paper.


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 STATE OF OA: A LARGE-SCALE ANALYSIS OF THE PREVALENCE AND IMPACT OF OPEN ACCESS ARTICLES
Review round: 1
Reviewer: 3

Output:
Basic reporting: A comprehensive description of oaDOI would be helpful earlier in the introduction. I was expecting more information about oaDOI in line 81, consider moving some of the language in line 230 to better frame the role of oaDOI in 'the state of OA'

Regarding the raw data and analysis available at the DOI provided, you might consider including a manifest with data and article DOIs as well as a more complete codebook or at least definitions of all variables and codes in dataset (ie, 999 for missing data). This is a valuable dataset for the community and is somewhat difficult to interpret given the current documentation.

In lines 307-308 the authors assert that Scopus and WoS are known to underrepresent segments of the literature. The article would benefit from a reference for this assertion.

There is a grammatical error on line 498 'this paper aimed at answering...'

Several references are formatted inconsistently, ie line 689
Experimental design: It would be helpful for the reader to clarify which ASNs were excluded from the analysis - all ASNs or only commercial ASNs? For example, would articles shared in the Humanities Commons be excluded?
Validity of the findings: It would be useful to address the potential for self-selection among users of the Unpaywall extension and the possibility that this might impact the Unpaywall sample.

In section 1.5 of the results, the conclusions are not well-stated. Consider a comparison of disciplines based on either the percentage of open papers or the percentage of gated papers. A combination of both is confusing for the reader.

In the discussion of Bronze OA (line 527), you state that it 'seems likely' for Bronze to be disproportionately non-peer-reviewed. Why does this seem likely?
Additional comments: I appreciated the opportunity to review this paper, this is a fascinating and very important analysis of open access scholarly literature. I am looking forward to seeing what additional research emerges from this, especially in the areas of citation advantage for Gold OA and the impact of Bronze OA.


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 STATE OF OA: A LARGE-SCALE ANALYSIS OF THE PREVALENCE AND IMPACT OF OPEN ACCESS ARTICLES
Review round: 1
Reviewer: 4

Output:
Basic reporting: No comment.
Experimental design: No comment
Validity of the findings: No comment.
Additional comments: Wonderfully accessible and well framed for understanding by multiple audiences.
It would be interesting to see what could be done about parsing out the shadow of the green OA, since the availability of that content is likely more stable, and less subject to the whims of publishers than bronze (and some Gold, esp. in the hybrid case). Speaking of... the community would definitely welcome further research on the bronze OA concept, so I'm thrilled to see that you plan to develop that further.
Thank you for an open article about openness that uses open data!


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 STATE OF OA: A LARGE-SCALE ANALYSIS OF THE PREVALENCE AND IMPACT OF OPEN ACCESS ARTICLES
Review round: 2
Reviewer: 1

Output:
Basic reporting: Line 69 contains a reference to a piece by Anderson ("The Forbidden Forecast") that isn't relevant to the point under discussion (current Big Deal cancelations). The authors may have confused that piece with this one:

https://scholarlykitchen.sspnet.org/2017/05/01/wolf-finally-arrives-big-deal-cancelations-north-american-libraries/

Later in the paper the "Forbidden Forecast" piece is cited in the context of a more relevant point.
Experimental design: No change to previous comments
Validity of the findings: No change to previous comments
Additional comments: No change to previous comments


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

Input:
Title: THE STATE OF OA: A LARGE-SCALE ANALYSIS OF THE PREVALENCE AND IMPACT OF OPEN ACCESS ARTICLES
Review round: 2
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: No Comment
Validity of the findings: No Comment
Additional comments: Thank you for reviewing the edits suggested before and making updates.


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 STATE OF OA: A LARGE-SCALE ANALYSIS OF THE PREVALENCE AND IMPACT OF OPEN ACCESS ARTICLES
Review round: 2
Reviewer: 3

Output:
Basic reporting: Thank you for your revisions and response. I maintain that the underlying data provided at http://doi.org/10.5281/zenodo.837902 could benefit from more documentation, including a manifest with data and article DOIs as well as a more complete codebook or at least definitions of all variables and codes in dataset. However, I believe that this revised manuscript meets the PeerJ criteria and am recommending that it be accepted as is.
Experimental design: No comment
Validity of the findings: No comment
Additional comments: No additional comments


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

Input:
Title: FREQUENCY AND DEVELOPMENTAL TIMING OF LINEAR ENAMEL HYPOPLASIA DEFECTS IN EARLY ARCHAIC TEXAN HUNTER-GATHERERS
Review round: 1
Reviewer: 1

Output:
Basic reporting: - The paper is well written and in this context it do not need any changes.
- The literature is correctly selected, although you can delete the oldest quotes (e.g., Sarnat 1941, 1942).
- The structure of manuscript is very confused.In paragraph "Methods" the authors write about materials. It is not known why they gave an additional sub-section "Study population" (line 72). In the subsection "materials" they described using methods (line 103).
-some tables are illegible (e table 2) - a column with a number of teeth was introduced, but it is not clear why there are so many rows.
Experimental design: -The aim of the study was not clear stated.
-The teeth with strong wear were excluded (line 115).But there are not any information about the method for estimate the stages of dental wear.
-There is no information about the age of individuals. But in the discussion the age category ("juvenis") was introduced (line 170).
- The authors mention about deciduous teeth, but the Dean and Reid method applies only to permanent teeth ( line 144, 149). So it does not really make sense to write about decidous teeth in this context.
- In the paragraph "results" the authors compare the Bucheye Knoll population with the other groups (line 160). This is a mistake, because such a comparison should be transferred to the discussion.
- The authors mention about the weaning stress in the context of LEH. However, we know that the weaning stress must be assess according to isotopic studies (nitrogen), and LEH can be used only as a indirectly be used for this purpose.
- In literature (line 280) Larson - it should be Larsen.
- In literature (line 328) Wood - it is not found in the text.
Validity of the findings: No comment
Additional comments: The material used for the study is very interesting.But the results are quite poorly presented in this paper.


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: FREQUENCY AND DEVELOPMENTAL TIMING OF LINEAR ENAMEL HYPOPLASIA DEFECTS IN EARLY ARCHAIC TEXAN HUNTER-GATHERERS
Review round: 1
Reviewer: 2

Output:
Basic reporting: I suggest the authors start the Introduction with hypoplasia (lines 44-58), then give the information on the population studied (lines 32-40) and conclude with the third subsection (59-70). The aims and purpose are clearly stated in the sentence (lines 41-43)  ''Here, we infer nonspecific nutritional and developmental stresses via the developmental timing and frequency of linear enamel hypoplasia defects (LEH) in the canines using photogrammetric methods.'', and it would be better if the Introduction finished with it.
Experimental design: No comment
Validity of the findings: The conclusions are connected to the original question investigated, which should be more cleary stated in the Introduction section, as suggested above.
Additional comments: No additional comments


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

Input:
Title: THE EFFECT OF SUPRAGINGIVAL GLYCINE AIR POLISHING ON PERIODONTITIS DURING MAINTENANCE THERAPY: A RANDOMIZED CONTROLLED TRIAL
Review round: 1
Reviewer: 1

Output:
Basic reporting: No comments
Experimental design: No comments
Validity of the findings: No comments
Additional comments: There is adequate literature on use of glycine air powder for non-surgical periodontal therapy and its comparison with ultrasonic debridement. The authors have reviewed some of it in relevant sections of the manuscript. It is standard of care to disrupt subgingival biofilm during periodontal maintenance and proposing to modify that well accepted treatment methodology will require strong scientific support. Perhaps for a convincing argument to be made in favor of supragingival debridement alone, a long-term comparison of clinical and microbiological parameters with subgingival debridement will be required. Glycine air powder is restricted in its ability to disrupt calculus deposits and an ultrasonic debridement for those areas would be standard of care. It is interesting to note that patients in this particular study did not have any calculus deposits during their maintenance phase (an assumption based on lack of mention of this in the manuscript).

Authors’ idea about patient comfort and time and cost-effective nature of supragingival plaque control that may have crossover effect on subgingival biofilm is the strongest hitherto largely unexplored question in this area. However, it is possible that the time and cost effectiveness of supragingival debridement alone would be diluted if cost of purchase, maintenance and training on both air-powder and ultrasonic instruments are taken in to account. No discussion was found on this aspect in the manuscript.

Overall, the manuscript needs significant revision from a grammatical and spelling standpoint. At multiple places throughout the manuscript, it was somewhat difficult to interpret statements.

Based on the overall deficiency in use of proper language and grammar, redundancy of already available data, development of clear rationale and lack of support for it restricts the utility of the manuscript in its current format.


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

Input:
Title: THE EFFECT OF SUPRAGINGIVAL GLYCINE AIR POLISHING ON PERIODONTITIS DURING MAINTENANCE THERAPY: A RANDOMIZED CONTROLLED TRIAL
Review round: 1
Reviewer: 2

Output:
Basic reporting: I think that this manuscript would benefit from a review and thorough evaluation of English grammar and structure . There are spelling and grammar errors throughout the article, for example: Lines 72-73 (introduction) "And A.a. was less frequent than ultrasonic debridement group. Line 213 (results) "there was approximately significant difference between baseline and 12 weeks after treatment". Line 320 (discussion) I would replace "serious periodontitis" with "severe periodontitis".

Improper use of some references. For example: Loe's study (line 43) showed that dental plaque can cause gingivitis, not periodontitis.
Experimental design: Inadequate information on the randomization method. Please provide more details regarding the methods or software used to distribute the right or half of the mouth to the two study groups. Were all right quadrants assigned to the test group whereas the left ones to the control? If yes, can you please provide the rationale for this decision. As mentioned in the discussion, being left- or right-handed can have an effect on the performed oral hygiene. Were all patients right handed or left handed?

Other than that I think that is a well designed study.
Validity of the findings: I think the main limitation of the study is that it does not take into account the possible presence of calculus in the the periodontal patients and how this can affect the effectiveness of either of the two methods applied in this study. A main advantage of the ultrasonics, is the ability to remove calculus, and ability that air polishing is lacking as discussed in one of the references included (Moene et al. 2010). A 3-month period, is a long enough interval for plaque to become mineralized, opposite to what is stated in the discussion where White's paper is cited. There is a number of papers supporting that mineralization of plaque starts within a few days rather than months. The rate of calculus formation varies considerably between individuals.
Taking these factors into consideration, I think that sections of the paper should be revisited and as well as the conclusion (the recommendation for 3-month maintenance interval is based at an extend on the aforementioned parameters).
Additional comments: Overall I would say that the experimental design of the study was very good with the exception of the lack of details on the randomization methods.
Major revisions are recommended to address the issued discussed in the previous sections.
Thank you.


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

Input:
Title: THE EFFECT OF SUPRAGINGIVAL GLYCINE AIR POLISHING ON PERIODONTITIS DURING MAINTENANCE THERAPY: A RANDOMIZED CONTROLLED TRIAL
Review round: 2
Reviewer: 1

Output:
Basic reporting: Okay
Experimental design: Okay
Validity of the findings: Okay
Additional comments: There are still minor grammatical errors 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: THE EFFECT OF SUPRAGINGIVAL GLYCINE AIR POLISHING ON PERIODONTITIS DURING MAINTENANCE THERAPY: A RANDOMIZED CONTROLLED TRIAL
Review round: 2
Reviewer: 2

Output:
Basic reporting: There are minor grammar and spelling errors that could be addressed. For example:
Line 302: I would write "In the present study" instead of "In present study".
Line 341: "spilt-mouth" instead of "split-mouth".
Line 378: "remov1e" instead of "remove"
Experimental design: Well designed RCT, details provided on the randomization method, power analysis was performed.
Validity of the findings: Although clearly stated in the discussion, I would add in the conclusion section that the comparison is only valid for soft deposits and not calculus. When calculus is present, additional intervention is needed.
Additional comments: Dear authors,

Thank you for addressing the majority of the recommendations from the first review. I think at this point, there are only minor editing changes to be made. The manuscript describes a sound methodological approach and valid conclusions.

Thank you