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: INSIGHT INTO THE KINEMATICS OF BLUE WHALE SURFACE FORAGING THROUGH DRONE OBSERVATIONS AND PREY DATA
Review round: 1
Reviewer: 1

Output:
Basic reporting: Generally, this manuscript does a good job of describing results and placing them in the literature. It includes a rarely captured overhead view of a blue whale surface feeding event and interestingly documents some measure of prey response.  I think the authors actually undersell the importance of the prey escape response they recorded and could even provide additional details on these findings (at the authors’ discretion of course but could strengthen the manuscript, see final comment).  This could be an important contribution to the literature.  The manuscript also provides an interesting characterization of the prey field in this environment (though see comments below) that suggests that in this environment blue whales may depend more on shallow prey aggregations, increasing their overall efficiency.

I do think, however, that some of the language in other places regarding the results being “unique” (e.g. line 361, 416 etc.) and “novel” (e.g. line 400) is perhaps a little overzealous given the number of UAV studies of cetaceans (e.g. Johnston 2019, full cite below) and the number of on-animal video observations reported of blue whale lunge feeding that have provided similar insights.  Not suggesting you need to cite these (especially given that I am pointing towards several of my own papers here), just providing for your reference and suggesting to remove “unique”:
Segre, P. S., D. E. Cade, J. Calambokidis, F. E. Fish, A. S. Friedlaender, J. Potvin and J. A. Goldbogen. 2018. Body flexibility enhances maneuverability in the world’s largest predator. Integrative and comparative biology.
Cade, D. E., A. S. Friedlaender, J. Calambokidis and J. A. Goldbogen. 2016. Kinematic Diversity in Rorqual Whale Feeding Mechanisms. Current Biology 26:2617-2624.
Segre, P. S., S. M. Seakamela, M. A. Meÿer, K. P. Findlay and J. A. Goldbogen. 2017. A hydrodynamically active flipper-stroke in humpback whales. Current Biology 27:R636-R637.
Gough, W. T., P. S. Segre, K. Bierlich, D. E. Cade, J. Potvin, F. E. Fish, J. Dale, J. Di Clemente, A. S. Friedlaender and D. W. Johnston. 2019. Scaling of swimming performance in baleen whales. Journal of Experimental Biology:jeb. 204172.
Werth, A. J., M. M. Kosma, E. M. Chenoweth and J. M. Straley. 2019. New views of humpback whale flow dynamics and oral morphology during prey engulfment. Marine Mammal Science.
Johnston, D. W. 2019. Unoccupied aircraft systems in marine science and conservation. Annual review of marine science.

Additionally, while the authors have clearly made effort to compare their result to previous literature, I think, given an n of 1, some of this discussion is not really warranted (e.g. line 408-412).  Speeds in the other papers that you are comparing to are all averages of many lunge feeding events.  Your observation is not really abnormal given the normal variation in blue whale lunge feeding (see, for a clear example, the means and st. dev. listed in Table 1 of Cade et al. 2016 cited above), so without further information it’s hard (and not really necessary) to speculate as to whether the lunge you measured is actually that different from other reported values and what the reasons could be (since it’s not statistically different).  Better are times where you remark that the observations of speed and engulfment in your video fits into reported values.

Finally, I would recommend scaling down the mentions regarding the lack of surface feeding in the literature.  It’s not that studies haven’t considered it (you cite Goldbogen 2011, for instance), but surface feeding is often excluded from other studies because of a) limited hydroacoustic prey data for appropriate comparisons and b) biomechanical processes and forces change when half the whale is out of the water.  This should be added to discussion in line 102 etc.  Some of examples of papers that directly tackle surface feeding include:

Allen, A. N., J. A. Goldbogen, A. S. Friedlaender and J. Calambokidis. 2016. Development of an automated method of detecting stereotyped feeding events in multisensor data from tagged rorqual whales. Ecology and Evolution 6:7522-7535.
Doniol-Valcroze, T., V. Lesage, J. Giard and R. Michaud. 2011. Optimal foraging theory predicts diving and feeding strategies of the largest marine predator. Behavioral Ecology 22:880-888.
Iwata, T., T. Akamatsu, S. Thongsukdee, P. Cherdsukjai, K. Adulyanukosol and K. Sato. 2017. Tread-water feeding of Bryde’s whales. Current Biology 27:R1154-R1155.
Kot, B. W., R. Sears, D. Zbinden, E. Borda and M. S. Gordon. 2014. Rorqual whale (Balaenopteridae) surface lunge‐feeding behaviors: Standardized classification, repertoire diversity, and evolutionary analyses. Marine Mammal Science 30:1335-1357.
Owen, K., R. A. Dunlop, J. P. Monty, D. Chung, M. J. Noad, D. Donnelly, A. W. Goldizen and T. Mackenzie. 2016. Detecting surface‐feeding behavior by rorqual whales in accelerometer data. Marine Mammal Science 32:327-348.
Experimental design: No comments, though see notes on acoustic analysis below.
Validity of the findings: Most of the manuscript seems to have a solid foundation. I wish the error in speed and distance measured from the UAV were better quantified given the motion of the UAV, but I do not believe those overly distract from the results.

The krill density analysis, however, is not sufficiently described such that a reader can follow the procedures, and there seems to be at least one potentially major mischaracterization of the data.

*keeping this paragraph here, but see note in next paragraph* On line 210 the authors describe their method for isolating krill, but the numbers and procedures are not well described.  Line 210 is very confusing and seems to suggest the authors excluded all data above -90dB?  In almost any ecosystem and acoustic set up this would essentially be all of the data (assuming it is a calibrated system, though the calibration procedure was not described but should be).  -90 dB is like a single krill / m3 (or 10 krill if the krill are very small), this is basically background noise and suggests your analysis is inappropriately excluding most patches that have any kind of density.  With only a single frequency transducer, there’s no real way to exclude fish species (and the cited source from Bernard and Steinberg is from a different ecosystem on a much larger species of krill, and their method is not especially robust and should be used with caution given their single frequency).  The described method would need a lot more justification and additional details, including an understanding of the target strengths of other types of organisms that may be returning echos, currently it sounds like lots of data may have been inappropriately excluded.  Especially in known foraging areas, it may be more prudent to actually leave in all data and assume it is krill (except for noise of course), given that you can’t know for sure.  Or do one pass trying to differentiate (though I’m not convinced that’s possible) and one pass where nothing is excluded.  Presenting both analyses would at least let the reader draw better inferences.

*I keep re-reading this description- I’m actually thinking now that you probably excluded data below -90 dB (the opposite of what you said on line 211).  At least this would make sense and would exclude background noise and help identify the boundaries of schools.  This method would definitely not differentiate krill from other ensonified species (like the fish example given, which have high TS), however, so some discussion should be devoted to if there was any ability to exclude fish schools (e.g. based on school shape), or at the very least what the general prevalence of such non-krill species is in this ecosystem.  If this opposite reading is what was actually done, some additionally validation of the -90 dB threshold should be given (i.e. based on the target strength of the krill in your ecosystem)

A second issue in the acoustic analysis regards the depth of the patches (around line 216), it is not clear exactly what “mean depth” represents.  That is, is it the mean depth of the densest part of the patch?  Or just the depth of the aggregation?  To give a sense of what is meant by “mean depth”, a sense of the size of the krill school is also necessary.  For instance, if an aggregation is 100 m thick, centered at 50 m depth, that’s very different, in terms of availability to blue whales, than if an aggregation is 1 m thick centered around 50 m.  Reporting mean thickness may help, especially since you are using NASC, which is an aggregation of the whole water column.  As you point out, density is critical, so it matters a lot when reporting NASC of a patch what the thickness of the patch is.  May be better to report and analyze mean volume backscattering (Sv) of the patch instead.
Additional comments: See minor comments on the following lines

Line 32- Awkward sentence, seems to imply that blue whales were encountered when surface lunge feeding was observed, which is a weird statement

Line 41-43 prefer to lay out what the observations were, rather than just saying unique observations were made

Line 68- because gray whales appear to be more firmly placed within Balaenopteridae, “rorqual family” isn’t quite correct anymore.  Better to say “blue whales are rorqual whales”

Line 70, perhaps these three citations could be condensed just to the Goldbogen et al 2017 paper you cite later on.

Line 75- re: “so that calories gained outweigh foraging costs”.  This is true, of course, but even low density patches < ~100 g/m^3 likely outweigh costs. Perhaps better just to say to “maximize energy gain” or something along those lines.

Line 78- remove “notoriously”

Line 94-95- the parenthetical here is not really necessary as the sentiment that krill species can affect prey quality is also encapsulated in the previous statement about more general density

Line 96-98, thoughout be a bit careful with vocabulary.  It’s not actually instantaneous efficiency (defined as energy in compared to energy out) that matters for a foraging animal over time, but net energy gained over time.  The calculations in Goldbogen 2011 can be used to support this (i.e. the net energy gain over 12.5 minutes of a dive is still less than assuming continuous surface lunging every ~1.5 minutes at the surface if krill density was the same).  Recommend rephrasing the comparison calculations throughout

The implication that blue whales mostly surface feed in New Zealand (line 101) should be walked back a bit unless more general information can be presented.  Better to say that the observed blue whales were mostly surface feeding.

Line 104- true that automatic detection methods can be confounded, but that does not mean lunges are undetectable or excluded for that reason. Human analysts can fairly accurately differentiate lunge feeding signals from surface noise.

Line 188 consider reporting the size and sex of the observed whale here.

Line 187-198, seems like a lot of unnecessary detail.  Can just say one flight over a surface feeding whale was completed

Line 222- more explanation- could not be determined why?

Line 223- Are these estimates from the cited paper?  If this is not directly measured data, some caveat should be stated (e.g.: “surface swarms can range between xx and yy”).  Also more helpful than numbers of krill (or in addition to) should be biomass as that is the unit described elsewhere in the paper.

Line 226- 100 g/m^3.  Your krill are much smaller than 1 g/ individual and likely 100 krill are not sufficient.

Line 228- this assumption seems unwarranted, but also not necessary to your other observations.  Better just to say the density of the swarm was unknown.

Is there any estimate of the importance of surface feeding?

Line 242- What about pitch (as in Fig 3?)

Line 242-257 Given the uncertainties, recommend calling the quantities “relative speed” and “relative acceleration” throughout the manuscript

Line 260- was “max gape” later reported?

Line 266-270, how does the “interval of interest” here relate to the information in lines 248-252?  Is it the same?  Can one of these sections be streamlined?

Line 297-300- not clear how roll was calculated?  Was it an estimate or was there some derivation of the values? (okay I see in line 310 that these are estimates, please list earlier)

Line 304-309- are you using “head inclination” and “pitch” interchangeably?  Since pitch conventionally refers to body pitch, recommend changing to “head inclination” throughout the manuscript which is an interesting metric and worth differentiating

Line 325- Some of the language is a little strong.  My understanding is that foraging behavior was presumed from surface observations of dive behavior.  This can an unreliable indicator foraging, so best to say a less strong word than “confirmed” when using surface observations and presumptions of ARS.

Line 374- a “likely” is warranted here, as there are several hypotheses for why whales lunge quickly, including biomechanical based hypotheses:
Orton, L. S. and P. F. Brodie. 1987. Engulfing mechanics of fin whales. Canadian Journal of Zoology 65:2898-2907.
Potvin, J., J. Goldbogen and R. Shadwick. 2009. Passive versus active engulfment: verdict from trajectory simulations of lunge-feeding fin whales Balaenoptera physalus. Journal of the Royal Society Interface 6:1005-1025.

Line 391- It seems fairly clear from your general depiction of the preyscape that blue whales here are foraging in shallow water because the krill is in shallow water.  Unless there is evidence that there is deeper krill that the whales are choosing not to forage on, it seems unlikely that they are making an active energetic choice, but instead are just foraging where the krill is.

Line 394-395- not sure this statement is necessary, or even justified here.  You show that blue whales sometimes feed at the surface, but there is not much discussion about the proportion of their time spent surface feeding.  A better statement might be more locally based, e.g. “blue whales in our study area appear to get a substantial portion of their diet from near-surface foraging at least during daylight hours, so new methods of analysis are available.”  Or something to that effect

Line 397-399, recommend making some of the comparison explicit.  Agree that your measurements are comparable to others, but worth making that explicit comparison for readers that are not steeped in the literature.  An additional comparison that may further justify your findings is that the timings of engulfment, with mouth opening at peak speed and maximum gape coinciding with peak deceleration, also match findings from camera tags (Cade et al. 2016).  Do not have to cite this paper, but may further strengthen your results.

Line 407- Unclear how speed “allows” lower mass-specific engulfment capacity?  I think you are looking for a different word there.

Line 415- “except that the whale did not fluke through the lunge”.  My understanding is that a basic assumption of most of the models in the papers cited assume that fluking stops at mouth opening, so in that sense your results match.

Line 418- agree.  These results could be further highlighted.  The reaction distance of the krill is a great metric to report.  To make the results even more meaningful, the authors could consider including (not necessary, just a suggestion) a brief calculation about the % of the krill patch that could escape given the observations of when they start to react and the observed escape speeds around the edges.  Even if all krill escape outwards away from the whale, given the speed differential between the krill and the whale, the response time (~0.8 s from your findings) and the scale of the whale’s mouth, this escape proportion is assumed to be small, but would be very useful for future models of efficiency to state explicitly the number that you would find.


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: INSIGHT INTO THE KINEMATICS OF BLUE WHALE SURFACE FORAGING THROUGH DRONE OBSERVATIONS AND PREY DATA
Review round: 1
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: I still need to be convinced that kinematic measurements can be conducted from a moving drone, otherwise the specific kinematic results should be omitted.
Additional comments: This study describes and analyzes the surface lunge feeding behavior in a population of Pygmy Blue Whales (Balaenoptera musculus brevicauda) and contends that this behavior is key to understanding the ecology and energetics of this species. I commend the authors for their efforts, which will aid in our understanding of this iconic species and SLF behavior. Furthermore, having high-resolution video evidence of predator-prey patch behavior is uncommon and should be published as it lends to testable predictions on predator prey dynamics, schooling/swarming behavior, and sensory ecology of both predator and prey. However, I have several major issues that need to either be addressed or re-worded before I can endorse this study for publication. All the changes I recommend are doable however, and along with them I suggest a title change to: “Insight into blue whale surface foraging through drone observations and prey data”.

Major points:
I do not understand how it is possible to obtain specific kinematics on a moving animal subject – that is otherwise uninstrumented – from a moving drone. Typically, when kinematics are determined from video imagery the camera is still, or each still frame is calibrated to correct for the movement of the image capturing device, a drone in this case. While the kinematic details are interesting and in line with what we know from tagging studies of this species in the Eastern North Pacific, I do not see how they can be considered robust with the methods as described. For example, animal speed is notoriously tricky to measure accurately even when a tag is affixed to the animal; to get measurements as precise as a tenth of a m/s seems impossible from a drone. The same can be said for the roll, and other kinematic measures, all reported with one-degree precision. I am willing to be convinced by expanding the methods to fully explain how this is possible, but as the paper currently reads results this specific should not be reported. This does not have to be a fatal flaw of this study however; I think describing the SLF events using relative kinematics would be perfectly fine. For example, “Just prior to prey capture the animal rolled on its right side, accelerated, and lunged laterally into the patch,” and similar, would be acceptable.

This flows into my other major concern, which is the extendibility of these findings to the ecology and energetics of the blue whale as a species. The kinematics, and associated conclusions, were drawn from one observed feeding event. This is a very exciting natural history observation worthy of reporting and describing, but to claim that this is how all, or even most, SLF is in this population or this species as a whole is over-reaching what the authors’ data is able to support.

The energetic argument is flawed in that the energetic cost of transport to and from “deep” krill patches (typically 100-300m deep) is predicted to be extremely low. Further, even a patch that is 250m deep is only ~10 body lengths for a blue whale. Therefore, act of diving itself, in both time and energetic expenditure, is extremely low for a blue whale. A more parsimonious energetic explanation is that blue whales simply feed on krill wherever it happens to be densest in that time and place. Also, a better test on energetic efficiency would be to compare the feeding rates at the surface and at depth, which I understand is beyond the scope of this study, but to say that SLF is a critical component of blue whale ecology it is critical to look at the whole picture. I am confident that the authors’ have conducted enough observations to state that SLF is an important aspect of the feeding ecology of this population, but to say that it is important to the overall foraging ecology of this cosmopolitan species is over-reaching. There are very few behaviorally well-studied populations of blue whales, perhaps the only other one is the Eastern North Pacific population, where, as you reference, SLF appears to be a relatively uncommon (but not unheard of or unseen) behavior. It is fair to say that for this population of pygmy blue whales SLF is an important (and perhaps previously unconsidered?) component of their foraging ecology. At present, there is not enough rich behavioral data available for the other blue whale populations to speak to the importance of SLF overall.

Minor points:
•	Line 226: Your talking about prey density but then you provide a volume of water. Perhaps you meant the spatial extent of a prey patch and not it’s density?
•	Line 255: Add space before citation.
•	Line 415-416: Rorquals typically do not fluke through the lunge, doing so would crater their energetic efficiency.
•	Line 461: Add space after semicolon
•	Lines 470-474: There is not enough data to conclude the specific value of this particular whale’s energetic efficiency; see major comments 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: INSIGHT INTO THE KINEMATICS OF BLUE WHALE SURFACE FORAGING THROUGH DRONE OBSERVATIONS AND PREY DATA
Review round: 1
Reviewer: 3

Output:
Basic reporting: It is always fantastic to have new data for animals in their natural environment. The authors provide new prey data in blue whale habitat in New Zealand. Although blue whales are relatively well studied in other areas, little is known about blue whales in NZ. Specifically, new information on the distribution of krill in relation to blue whale sightings at the sea surface is the primary strength of the manuscript. However, there are many weaknesses of the manuscript. In particular, one aspect of the study (kinematics) is technically flawed and should be removed.

As the title indicates, the manuscript aims to provide insight into two aspects of blue whale foraging: 1) significance and 2) kinematics. I will focus my review on each.
Experimental design: See other fields for comment.
Validity of the findings: 1. Significance. The authors are making the claim that surface lunge feeding is important and that prior studies disregarded this part of their foraging ecology.  This latter is is patently false for many reasons (see a, below). For the former, surface lunge feeding may very well be important, but the data in the paper cannot speak to whether it is or not. For example, the authors were not able to measure any potential feeding at depth, so any feeding rates of surface versus depth cannot be assessed with this data.

a) Many studies have looked at surface lunge feeding in rorquals, and also blue whales more specifically (Doniol-Valcroze
 et al., Kot et al.). In particular, Jill Schoenherr’s study (1991, Can J Zool) on deep and surface krill patches in blue whale forging habitat is the most comprehensive study to date that compares deep and shallow. This is a major omission and needs to be addressed. Therefore, it is not clear how the research fills an identified knowledge gap.

b) The authors fail to define what significance is, as well as how it would be measured and statistically compared. A dichotomy between surface and deep feeding is present in the narrative of the paper, but it is unclear what would constitute significance in this context. A certain proportion of lunges at the surface versus shallow? This needs to be defined. If a lunge occurs at 5 or 10 meters in depth is it still a surface lunge? Is there a arbitrary or justified threshold that distinguishes the two categories or is it a continuum? At what depth will UAS not be able to view the whale? In summary, the research question is not well defined in the manuscript, and it is not clear how the data are relevant & meaningful in the context of blue whale foraging ecology.

2. Kinematics. The kinematic analysis is technically flawed and should be removed. The authors should report the amazing behavior observed by the UAS, but attempts to quantify kinematics are problematic because the UAS was moving, currents were not accounted for, and krill may undertake primary escape responses in well lit environments (O’Brien, 1987). All these factors complicate any kinematic analyses with respect to speed and acceleration. Also, it is not possible to measure roll as a function of time from one overhead camera. When I looked for methods on roll estimation, it is not described in sufficient detail for replication in the manuscript.
Additional comments: No additional comments


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

Input:
Title: INSIGHT INTO THE KINEMATICS OF BLUE WHALE SURFACE FORAGING THROUGH DRONE OBSERVATIONS AND PREY DATA
Review round: 2
Reviewer: 1

Output:
Basic reporting: Overall, I thought the authors did a good job addressing reviewers’ concerns and I found the manuscript much more of a compelling read. I appreciated the authors attention to language and to the reviewers’ comments.  There is a major issue with the prey analysis (discussed in detail in the “Validity of the findings” section below) that needs to be addressed before the manuscript can be accepted, and generally the description of the prey analysis could be much tighter and clearer, but other comments are small.

General comments:
I appreciated the increased focus on error with regards to kinematics.  Unless I missed it, I didn’t not see a similar error reported for whale speed/distance.  Some discussion of the potential error in speed estimation (in numerical form, even if an additional estimation) given the different moving pieces seems warranted (in addition to the helpful caveats given describing why the error exists).

Thank you for including the raw video that allows the reader to examine the escape responses laid out in lines 397-407.  After viewing the video, it is perhaps worth an extra sentence at the end of this paragraph noting that the krill appears to move around in response to the whale, but do not appear to move in an outward direction away from the whale, so capture percentage is likely high.  Indeed, the general shape of the patch (including the off-shoot arm on the right side of the frame) appears to be maintained throughout the lunge.

Line 499-500.  It is worth a little bit more explanation of why surface feeding energetics are presumed to be lower than deep feeding.  Wave drag is higher at the surface, so it’s my understanding that  the actual cost of lunging is not smaller at the surface, but the overall reduction in cost is more likely related to the shorter recovery times (from the shorter dives you describe) as well as shorter transit times.

Prey comments-

Generally, it was a little difficult to know exactly what steps were taken in the analysis, but I do thank the authors for including well-commented, easy-to-follow code that allowed me to make the following observations that should improve the descriptions in the methods, but also allowed the identification of a major issue that, when fixed, should give more convincing results.

Minor prey comments:
NASC as a metric of density.  As I mentioned in the first review, NASC is typically used in two dimensions as it integrates the vertical dimension to measure abundance over an area (as opposed to density in a patch).  These authors use NASC to measure changes in the vertical domain, in which case care should be taken to justify why this is appropriate.  The explanation should highlight that because 1 m vertical bins were used, NASC and sv essentially only differ by a multiplicative factor (i.e. NASC/(4pi*1852^2), see Maclennan reference below).  I would still suggest using sv (or better, Sv, see below) as that additionally standardizes for bins of unequal size (i.e. some bins in the dataset are ~ 1.1 m and some are 0.9, meaning that a 1.1 m bin would have 20% more backscatter than a 0.9 m bin even if density was the same when using NASC; this problem is ameliorated by using sv), but those differences should not substantially affect results.  If NASC is used, places to further explain how it was used would be in lines 227-228, for example, where the authors could emphasize that the NASC of the 1m thick bins were averaged within krill swarms (i.e. it is not clear right now from that description if the NASC of the whole swarm itself was calculated, which would give the areal vs density problem, or if the 1 m x 5 ping bins were averaged).

Sv vs sv.  Throughout the manuscript, these appear to be used interchangeably (see, e.g., Fig S1).  In conventional usage, Sv is the logged form of sv, that is Sv = 10 log10 (sv).  See the guide to definitions and symbols here:
MacLennan, D.N., Fernandes, P.G. & Dalen, J. (2002) A consistent approach to definitions and symbols in fisheries acoustics. ICES Journal of Marine Science, 59, 365-369.
This will be critical later, as improper averaging of Sv in the logarithmic domain is one of the problems identified in the code.

The term “patch width” is used throughout the manuscript, but I think from the usage in the code the authors are referring to patch size in the z-direction, so “patch thickness” may be a clearer term to use as width is often a dimension along the x and y axes.

Supplemental figure S1 is hard to interpret.  Would it be possible to place the correlations on the plot that they go with?  Looking in two disparate places makes it challenging to draw connections.  A legend/caption would help as well, though I do not see one in the files available to reviewers.  I’m not familiar enough with these types of plots to know what, for instance, a plot of mean depth vs mean depth with different scales means.

Line 228-229.  The description of how depth was calculated was a little hard to follow.  Perhaps say more explicitly that mean depth was calculated as the mean depth of the patch midpoints.  Another suggestion would be to calculate the depth of the densest bin in each vertical column, but regardless a clearer explanation would be useful.
Experimental design: It should say explicitly in the text what surface values were excluded.  Your spreadsheets have very high values in the first m, which is in the near field of the transducer so need to be excluded or they will bias your results.   Code suggests first two m were excluded (line 142), so just state that this was the method applied to all data

What software was used for the original export of acoustic data to csv file?

When/how was the echosounder calibrated?  If uncalibrated, important to state.
Validity of the findings: There is a major issue in the prey analysis that will lead to large underestimation of patch density in some cases that needs to be corrected.

This issue in analysis appears in line 296 “nasc = mean(mean((NASC_Agg(minr:maxr,minc:maxc))))”
as well as line 300 of the matlab code.  Earlier in the code, empty water was replaced in the aggregation matrices “Krill” and “NASC_Agg” with zeros.  But then in line 296 those zeros are averaged into overall density estimation (since the code as written takes the mean of the columns, and the means of those values) which will bias your values low (if using NASC, high if using Sv), particularly for patches with both thin and thick sections.  See figure below (included in the pdf attachment to this review) which is the 3rd aggregation in the first csv file.  In this example, averaging as is done in the code results in a value that is half what the actual value should be.

Instead, you need to find the mean of just the patch.  So code for you would look instead like this:
NASC_Agg(find(Aggs==i))
Which gives you a column vector of just the bins within the patch (without the zeros).  Taking the mean of this will give you the mean NASC of the aggregation.  There is a second reason why this is better as well.  Even if you removed the zeros, the way the code is now, “mean(mean(…” takes the mean of the columns and then averages those.  This will create a bias towards the thin parts of the patch. Taking the mean of all the data combined (i.e. “mean(NASC_Agg(find(Aggs==i)))” gives you the overall mean of the patch.

Additionally, line 300 of the code involves the “Krill” table, which are Sv values.  The same problems from above apply, but additionally, if you are trying to calculate a mean patch density, you need to average values in the linear domain (i.e. sv).  NASC is already in linear domain (which is why you log it for comparisons and figures), but Sv, which is in decibels, needs to be converted back to sv before averaging (see equation above and Maclennan et al. cited above), and then converted back to Sv after averaging.
Additional comments: no comment


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: INSIGHT INTO THE KINEMATICS OF BLUE WHALE SURFACE FORAGING THROUGH DRONE OBSERVATIONS AND PREY DATA
Review round: 2
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: I am happy with the changes made by the authors. The revised manuscript has the results limitations clearly stated and better contextualizing the nature of their observations. In the long run this will help science build off of and improve on this work. I have only one minor comment for the authors this round.

My main comment for this version is I am not sure about the use of the word "relative" to describe the kinematic measurements. It leaves me thinking "relative to what?" Perhaps a better way phrase this would be "estimated", "approximated" or similar. I don't feel very strongly about this, rather that the use of the world relative here seems odd.


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 USE OF PSEUDO-MULTIVARIATE STANDARD ERROR TO IMPROVE THE SAMPLING DESIGN OF CORAL MONITORING PROGRAMS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The explanation of the experiment is clear and the vocabulary seems appropriate.
In the introduction, lines 40 to 45, more description of the methods would be appreciated to explain the differences between each and how this topic of "how many transects are enough" is so important. In method it is said that a variation of the GCRMN method is being used, describe its main characteristics and add citation. More background could be added.
Overall more references would be appreciated in particular in the method section as the whole design seems to be based on the study of Anderson and Santana only.
Figure 2 seems low definition and present a typo at playa tiburon.
Results are very interesting and should be detailed more. Figures are very briefly explained.
Discussion should include more references. Line 131 to 135 are very important points and very interesting for other monitoring teams, more discussion would be relevant. More link to the habitat type or site size should be made.
Experimental design: This research is meaningful and keep adding to the discussion. The experimental design is well described and made available.
Validity of the findings: Results are quickly described and more conclusions could be drawn or described more in depth but they are very interesting and relevant for the line of research.
More interpretation regarding the different monitoring methods stated previously would be appreciated.
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 USE OF PSEUDO-MULTIVARIATE STANDARD ERROR TO IMPROVE THE SAMPLING DESIGN OF CORAL MONITORING PROGRAMS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript provides important data regarding the use of different sampling strategies (transects, quadrats and points) to survey coral assemblages. The authors use the multivariate standard error to determine the best sampling protocol in order to get the best estimation of the coral assemblages. An important finding is that increasing the number of transects provided a more precise estimation, while increasing the number of quadrats and points didn’t.

I find the paper to be well written and structured, with only a few minor details included below.  The introduction is appropriate and reflects a thorough review of the literature on the topic. The data are clearly presented and interpreted. The discussion is appropriate and supported by adequate references. The conclusions are sound.

In my opinion the study represents a useful contribution to science.
Experimental design: The work is original and the research question is clearly defined, relevant & meaningful.
Validity of the findings: The study is important as it will help to improve the way sampling of coral reefs is done and to have better estimations of the coral assemblages that will allow us to evaluate changes more accurately and to make comparisons between sites and localities.

The authors provide all R codes well structured and described so they can be used to replicate the analysis or to use them for other studies.
Additional comments: ABSTRACT
Ln. 21. It is not clear what authors mean when they say the “re-annotated” a subset of sites. Do they mean “re-sampled”?

METHOD
In the methods section authors only mention that the data came from 36 surveyed sites of Venezuela, however, in the Results Section they also talk about Localities, and this is confusing. I suggest mentioning in this section the number of localities.
Pg. 2. Ln 88. Change “variables” with “variable”

DISCUSSION
Pg. 4 Ln122.  Change “spend” to “spent”
Pg. 4 Ln 132. Change “separated at hundred…” to “separated by hundreds”…
Pg. 6 Ln 130 - This sentence is very long, I recommend dividing it in two.

Figure 2. The quality needs to be improved. In Y-axis - Change Playa Tibur?n to Playa Tiburon

Literature
Change: R Core team (2019). R: A language environment for statistical computing. To:
R Core team (2019). R: A language environment for statistical computing. R Foundation for Statistical Computing, Vienna, Austria. https://www.R-project.org/


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 USE OF PSEUDO-MULTIVARIATE STANDARD ERROR TO IMPROVE THE SAMPLING DESIGN OF CORAL MONITORING PROGRAMS
Review round: 1
Reviewer: 3

Output:
Basic reporting: The article is well written, with appropriate literature for the research topic. Information is available to readers. The figures should improve the resolution of the image, especially Figure 2. The authors should include in the introduction, explicit  questions and hypotheses that are evaluated.
Experimental design: The article presents a sampling design and an adequate resampling techniques proposal. However, it must include information on multivariate dataset (nxp) and measures of dissimilarity used.

The authors are interested in assessing the consequences of using different combinations of sample points, quadrants and transects in the multivariate standard error. To evaluate the multivariate standard error, the authors rely on the methodology proposed by Anderson and Santana-Garcon 2015 (included in the literature). However, the statistical proposal of Anderson and Santana-Garcon (2015) refers to the dissimilarity pseudo multivariate-
based standard error (MultSE), measure of precision, not multivariate standard error. An important point is that authors should clarify because in this article they refer to the multivariate standard error and do not use (MultSE). The multivarite standard error and (MultSE), statistically have different implications.This point is key and influences the results obtained, depending on the methodological implications of Anderson and Santana-Garcon (2015)
Validity of the findings: The authors suggest "We suggest that using at least ten transects provides a more precise estimation of the coral assemblages from Venezuela." For this suggestion there are two aspects to consider: 1-How much accuracy in the estimation do the authors refer? and 2-Anderson and Santana-Garcon (2015) suggest that "the value of MultSE in equation (3) (original paper) is dependent on the scale of the dissimilarity measure chosen and (potentially) also on the number of variables, so no such generalization for its value across multiple studies is apparent "; so it influences in the results suggested sample size (least ten transect). Authors should consider reviewing Legendre and De Cáceres Ecology Letters, (2013) 16: 951–963, to select the appropriate dissimilarity measure for dataset (nXp).

The authors suggest "We recommend the evaluation of multivariate standard error in coral reef monitoring programs, especially in pilot surveys to optimize the estimation of the coral assemblage."Two important aspects to consider: 1-What set of variables do the authors refer to when they say "the coral assemblage"? 2- How the authors suggest "estimation of the coral assemblage". These two aspects need to be clarified in the proposed methodology.
Additional comments: This article presents an important topic to consider in environmental and biological monitoring programs. However, there are several aspects (mentioned above) that should be considered by the authors to clarify the methodological approach followed by the authors.


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 USE OF PSEUDO-MULTIVARIATE STANDARD ERROR TO IMPROVE THE SAMPLING DESIGN OF CORAL MONITORING PROGRAMS
Review round: 2
Reviewer: 1

Output:
Basic reporting: Previous comments were appropriately attended, no further comments
Experimental design: Previous comments were appropriately attended, no further comments
Validity of the findings: Previous comments were appropriately attended, no further comments
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 USE OF PSEUDO-MULTIVARIATE STANDARD ERROR TO IMPROVE THE SAMPLING DESIGN OF CORAL MONITORING PROGRAMS
Review round: 2
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: I have only a few minor suggestions;

Abstract

Pg 5, ln15

I recommend changing:

“In this work, we aimed to assess the pseudo multivariate dissimilarity-based standard error (MultSE) of a series of reefs in Venezuela, sampled between 2017 and 2018, and also, to evaluate the consequences of using different combinations of points, quadrats, and transects over this error.”

To:

“In this work, we use the pseudo multivariate dissimilarity-based standard error (MultSE) approach to assess the precision of sampling scleractinian coral assemblages in reefs of Venezuela between 2017 and 2018 when using different combinations of number of transects, quadrats  and points.”

Pg 5, Ln 24:

I recommend changing:

“For this case study, when comparing between sampling with 10 transects, 10 quadrats per transect and 25 points per quadrat; and the original data for Venezuela, we find that the error is reduced by half”

To:
“For this case study, the error was reduced by half when using 10 transects, 10 quadrats per transect and 25 points per quadrat.” (you don’t have to repeat that data for Venezuela are being used).

Introduction

Pg 6, Ln 58
Improve the redaction of last sentence of the introduction:

I recommend changing:

“In this study we wanted to answer what values of multSE were achieved in a series of scleractinian coral assemblage surveys conducted in 36 sites of Venezuela?; and after knowing the reference values,  what would be the effect of using different combinations of sampling strategies, including number of points, quadrats, and transects over the multSE? This with the aim of comparing the best sampling protocol and potentially improve precision for future samplings of these communities.”

To:

“In this study we pretend to answer two questions: 1) what values of multSE are achieved in surveys of scleractinian coral assemblage conducted in 36 sites of Venezuela?, and, after determining the reference values, 2) what would be the effect over the multSE of using different combinations of sampling strategies, including variable number of points, quadrats, and transects? This information will help to determine the best sampling protocol and potentially improve the precision in future samplings of these communities

Methods

Pg 6, Ln 64

Change: “We estimated the multivariate standard error”

To: “We estimated the pseudo multivariate dissimilarity-based standard error (MultSE)”

Pg 6, Ln 66

Write what GCRMN means

Change:

“following a variation of the GCRMN monitoring protocol: instead of using five transects per site, we used four 30m transects (to increase the number of sampling sites), 15
photo-quadrats per transect placed one another meter, and 25 random points per quadrat (GCRMN, 2016).

To:

In order to increase the number of sampling sites, we used a variation of the GCRMN monitoring protocol (2016) and used four instead of five 30 m transects, 15 photo-quadrats per transect, placed one another meter, and 25 random points per quadrat.

Pg 10
Fig. 4 needs a title on axis Y2 (number of quadrats)


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 USE OF PSEUDO-MULTIVARIATE STANDARD ERROR TO IMPROVE THE SAMPLING DESIGN OF CORAL MONITORING PROGRAMS
Review round: 2
Reviewer: 3

Output:
Basic reporting: This section it´s ok.
Experimental design: This section it´s ok.
Validity of the findings: This section it´s ok.
Additional comments: I include two changes that must be added:

Line 64. Change: “We estimated the multivariate standard error (Anderson and Santana-Garcon, 2015)” for “We estimated the MultSE (Anderson and Santana-Garcon, 2015)”.

Line 72. Change to "Matrix of dissimilarity of the Bray-Curtis index". Please, the authors must specify, for the readers, which version of the B-C index they used: quantitative or presence-absence or binary?


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 COREPRESSOR NCOR1 AND OCT4 FACILITATE EARLY REPROGRAMMING BY SUPPRESSING FIBROBLAST GENE EXPRESSION
Review round: 1
Reviewer: 1

Output:
Basic reporting: General: This manuscript reports that siRNA-mediated knockdown of the transcriptional corepressor NCOR1 or of the pluripotency transcription factor OCT4 results in similar changes in colony phenotypes in mouse embryo fibroblasts (MEFs) and partially overlapping changes in the transcriptome.  The authors also report that NCOR1 and OCT4 co-occupy a shared subset of promoter sites and that in early MEF reprogramming down-regulation of one group of somatic genes requires both NCOR1 and OCT4 whereas another group requires NCOR1 but not OCT4.  Later in MEF reprograming a separate cluster of genes are also upregulated by siNcor1 but are downregulated by siOct4, suggesting the expression of the latter genes is normally facilitated by OCT4.  The authors conclude that “NCOR1, assisted by OCT4 and C-MYC, facilitates transcriptional inactivation of genes with high expression in MEFs, which need to be suppressed to bypass an early reprogramming block.”

Overall this is a fairly straightforward, concise manuscript that reports several interesting observations relevant to how pluripotency in MEFs is regulated.  The analysis is carefully performed, the results are generally convincing, and most of the conclusions are well supported by the experiments provided.  However a few suggestions are proposed to improve the presentation and to test one of the authors' hypotheses (please see specific comments).

The manuscript is clearly written and the introduction, background, and citations are appropriate and well-constructed.  The figures are relevant and are sufficient quality, adequately labeled and described (with just a few exceptions; please see specific comments).
Experimental design: The research question, the role of NCOR1 vs OCT4 in control of pluripotency, is well defined and is appropriate for PeerJ; its relevance to previously unanswered questions is clearly explained.  The technical and ethical standards appear high and the methods are sufficiently detailed.  The submission website provides the various usual assurances but I was unable to find a statement in the text stating these. Will this be reconciled on publication?

Checks: The submission website indicates that files were deposited to NCBI-GEO (which I confirmed) but I was unable to find a statement in the text stating this. Will this be reconciled on publication?  MEFs, not a cell line, were employed.  The use of English is very good.  My inspection of the data reveals no obvious manipulation but my ability to test this is very limited.
Validity of the findings: The experiments are generally well designed scientifically, adequately controlled, and the results are fairly straightforward.  The authors’ conclusions are clearly stated and generally well founded on their experimental results, although one of the authors' hypotheses would be strengthened by one or two additional modest experiments; several other conclusions would benefit from being discussed at greater length (please see specific comments).

Specific Comments: 1. The authors provide several lines of evidence that NCOR1 and OCT4 coregulate an shared subpanel of genes, including an apparent overlap between NCOR1 and OCT4 promotor binding sites by ChIP analysis.  The results presented are generally supportive of this argument but there are some incompletely resolved questions in this regard:

a. Figure 4D presents ChIP occupancy data for different proteins/chromatin modifications at different times post-induction; unfortunately the time point presented for the NCOR1 ChIP does not match those of the other ChIPs.  The power of these comparisons would be significantly strengthened if the authors had access to, or could newly generate, data from a matched time course NCOR1 CHIP.   Alternatively (recognizing that the NCOR1 ChIP is not their own data and that de novo ChIP experiments would require significant effort and time) a discussion of the limitations of the current data may be adequate instead.  The authors should also discuss why, if only a minority of NCoR-occupied sites exhibit up or down regulation in response to siOct4 (Figure 4C) all of the NCoR1 occupied/regulated sites presented in Figure 4D also exhibit co-occupancy by OCT4: are the genes presented in this panel already filtered to present only those upregulated by both siNcor1 AND siOct4?
b. The authors state that “NCOR1 directly binds to a significant fraction of deregulated genes in Ncor1 and Oct 4 knockouts” (lines 328-329).  The most likely mechanism for this observation and for the reported overlap between NCOR1 and OCT4 occupancy sites in Figure 4D, would be if the repressor NCOR1 “is recruited to such promoters by OCT4/c-MYC" (lines 364-365). Have the authors tested this hypothesis in more detail such as by (i) a “reChip” analysis using anti-OCT4 antibodies followed by anti-NCOR1 antibodies, and/or by (ii) a coimmunoprecipitation of OCT4 and NCOR1 from MEFs after DNase I treatment or an in vitro GST-pulldown protocol using the two proteins?  These would also help confirm/define the term “direct” in line 328.
2. It is curious that only ~4% of the sites of Ncor1 binding identified by ChIP in Figure 4C are up regulated by siNcor1, and more than 2/3's of the genes upregulated by NCor1 siRNA are not associated with an Ncor1 binding site in the ChIP.  These observations do not invalidate the authors’ conclusions but the authors definitely should discuss possible mechanisms that might explain these results and their implications.

3. What was the efficiency of the siNcor1 knockdowns in the experiments presented in this manuscript?

4.  The following are related to presentation rather than the validity of the science itself.

a. The image in Figure 1D is too dark and too small to easily evaluate by the reader.  Can better panels be provided?

b. The labelling of the heat maps in Figures 2 and 3 confused me.  Each descriptor at top (e.g. "siNcor1" or "siOct4" in Figure 2) spans two lanes of heat map but the difference between those two lanes is not labeled or explained in the captions.  Does each lane represent a separate set of genes within the same overall category (e.g. cluster 2A, Day 6, siNcor1)?  Or do the two adjacent lanes represent the same genes under different conditions not specified by labeling?

c. I could not find legends for the Supplemental figures.

d. A few statements in the text should be reworded to be more precise:
(i) Line 271-272, “approximately half of the genes deregulated in siNcor1 cells were also deregulated in siOct4 cells…”  The actual percent is 43%; why not just use that value rather than round up to "approximately half"?  It should also be explicitly stated here (and in lines 400-404 of the Conclusions) that, reciprocally, less than 1/20 of the genes responding to Oct4 siRNA also respond to siNcor1.  The asymmetry in these NCOR1 vs OCT4 overlaps is important in considering the mechanisms that may be operative and the conclusions that can be made; it should be noted prominently in the Results and specifically addressed in the Discussion.
The following are relatively minor points:
(ii) Line 78, “NCOR1/NCOR2 are essential enzymatic co-factors of histone deacetylases.”  The construction of this statement is slightly ambiguous and may lead some readers to incorrectly assume that NCOR1/NCOR2 are themselves enzymes, rather than non-enzymatic cofactors for the enzyme HDAC3.
(iii) Line 328-329, “NCOR1 directly binds to a significant fraction of deregulated genes in Ncor1 and Oct 4 knockouts…”   Technically the siRNAs generate "knockdowns" not "knockouts."  Use of the term “directly” is discussed in specific comment 1b, 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 COREPRESSOR NCOR1 AND OCT4 FACILITATE EARLY REPROGRAMMING BY SUPPRESSING FIBROBLAST GENE EXPRESSION
Review round: 1
Reviewer: 2

Output:
Basic reporting: Well written and presented, adequate references in general, clear hypothesis and well-supported data.
Experimental design: Good in general.
Validity of the findings: Appropriate and timely.
Additional comments: In the manuscript by Penalosa-Ruiz et al., the authors continue their previous work based on a high content siRNA screen on the reprogramming of somatic cells to induced pluripotent stem cells. In this screen, they discovered a link between NCOR1 and OCT4, which they now study in detail and go on to validate using a range of genomic tools. The author’s screen was set up in such a way that it is more likely to get hits during the early phase of reprogramming, which is a particularly interesting phase as the mechanism behind the suppression of somatic genes still remains somewhat fuzzy and there is much disagreement. Hence, the observation that OCT4 can recruit NCOR1 to suppress somatic and fibroblastic genes adds a useful dimension to the action of the reprogramming factors in reprogramming, and contributes to the wider discussion on the role of epigenetic control in reprogramming and cell fate conversions. The results are consistent with a previous manuscript by Zhuang et al. in Nature Cell Biology (2018) showing that NCOR/SMRT contribute to suppress the somatic cell program during reprogramming, but the present work extends those observations significantly and provides new data too.

Overall, on a technical level I found the study to be well performed, and technically sound. Statistical analysis is appropriate. I have a few relatively minor points the authors should address.

1. Figure 4D. As NCOR1 modulates H3K27ac, it would be useful to add the H3K27ac data from Chronis et al. here to see if these loci are indeed marked as active in MEFs.
2. The authors don’t seem to show the level of knockdown of NCOR1 by RT-qPCR and in the RNA-sequencing data. In a related point, does the knockdown of OCT4 affect NCOR1? Also, what are the expression levels of NCOR2 in the various knockdowns?
3. Since NCOR1 plays a dual role in reprogramming (inhibits both the somatic cell program and pluripotency genes) it would be useful if the authors could explain that siRNA and shRNA knockdowns may turn the balance towards increased or decreased reprogramming efficiency (full reactivation of the pluripotency network at late time points, which is not measured here) differently depending on the strength of the knockdown.

Minor stylistic points:

1. Line 52-54. Whilst a very attractive model, it is by no means proved that chromatin state is the dominant controller for cell type stability. Should be rewritten in a more speculative tone.
2. Line 67. It is not clear that OCT4 binds to open chromatin first. It could bind both closed and open simultaneously or the timing for one process or the other be a matter of the time points assessed or be due to differences in chromatin state in mouse and human reprogramming, and/or be caused by the type of medium used for the reprogramming.
3. Please correct issues with terminology. For example, NCOR2 is written as NCOR2, SMRT, and SMART depending on the paragraph. Check figures as well. Also, there is iPSC and iPS. Moreover, check gene versus protein terminology.


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: POPULATION STRUCTURE AND MICROBIAL COMMUNITY DIVERSITY OF TWO COMMON TETILLID SPONGES IN A TROPICAL REEF LAGOON
Review round: 1
Reviewer: 1

Output:
Basic reporting: In this study Baquiran and colleagues examine the population dynamics and microbial community composition of moon sponges on coral bommies in the Philippines. They found the population structure to be stable over the course of the 4-yr study, with the two species of moon sponge harbouring distinct microbiomes. However, there was an overlap in their functional profiles as determined by PICRUSt2. On initial passthrough of the abstract there was some expectation that there would be metagenomic data to support the convergence of functions identified between the two species. While the authors do a good job of identifying the limitations in the methods section, it should be made clear from the start that conclusions are drawn from PICRUSt2. In addition, the first line of the abstract states that, “Sponges are predicted to dominate future reef ecosystems influenced by anthropogenic stressors and global climate change” however, the introduction is lacking any information to directly support this statement. There is a growing body of literature that can be used see Bell et al. 2018 DOI: 10.1093/biosci/biy142 as a starting place. Other suggestions pertaining to the introduction can be found in the general comments.

Figures and tables
•	Suggest Fig 1 becomes Supplementary and Figure 4 be split. Perhaps (D) on its own then the fonts can be enlarged for all graphics, which are currently hard to read as is.
•	Supp Fig 2 – very hard to read tree, increase font size. In addition, suggest red font is replaced with another color.
•	Supp Table 5 and 7-11 are not mentioned within text. In addition, all tables and figures need to be in cited in sequential order. For example, Supp table 6 is cited before Supp table 1, please correct throughout.

Raw data
•	Raw sequencing data should be submitted to the NCBI SRA or equivalent prior to acceptance.
Experimental design: The research question was well defined and the methods logical, though I have a few comments/suggestions:
•	What was the justification for where the sponge samples for micro were collected (i.e. why bommie 22 & 15)? Also, it is not clear from the NMDS which samples came from 22 vs 15.
•	You have used DADA2, but are reporting OTUs classified at 97% similarity and not ASVs, is there a reason why?
•	While there was no significant difference in environmental variables between the sampling times, the dataset collected provides the unique opportunity to examine if any of the environmental variables measured are correlated with microbiome structure in these sponges. This can be done using the envit test in vegan or you could use DISTLM/dbRDA and would provide an extra element to the study.
Validity of the findings: This manuscript contributes to the growing body of literature on the microbiomes associated with sponges, as well as information on sponge population dynamics over multiple years, which is a strength of the study. Authors have applied statically sound methods; the data is robust and the paper itself well written.
Additional comments: Line 58: Instead of just citing a review, this statement should also include a reference that examines the microbiomes of sponges. Work from the global sponge microbiome project would be a good option, Thomas et al. 2016.
Line 67: specifically, what environmental conditions? Suggest expanding on this topic.
Line 262: ‘individuals’ is not needed
Line 306: insert ‘,’ after (16.09%)
Line 337: it might be worth clarifying what the NSTI score relates to and why the chosen cut-off is acceptable.
Line 386: while the statement is factually correct, the connection between it and your study is lacking given no seawater or sediment was examined.
Line 392: given the substantial number of sponge-microbiome studies available, there should be more than one that backs up your findings of these dominant taxa.
Line 412: what is the relevance to this study? Have SRCR been identified in moon sponges? If no direct link can be formed, this paragraph should be removed.
Line 456: remove ‘,’ after ‘addition’


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: POPULATION STRUCTURE AND MICROBIAL COMMUNITY DIVERSITY OF TWO COMMON TETILLID SPONGES IN A TROPICAL REEF LAGOON
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript by Baquiran et al is a nice piece of work on the population structure and of two related sponge species and their associated prokaryotes. It is based on a very complete dataset (although you might advocate that seawater samples should also have been included as a reference for the prokaryotic communities) and analyses are well done. The story is well written, was easy to follow and well... it is just a nice piece of work.
Detailed comments are listed per line number in the last box “general comments for the authors”
Experimental design: Experimental design is well done except perhaps the missing seawater samples and some explanation is needed what is the exact target of the 16S rRNA gene primers used and why not both COI and 28S are sequenced from both sponges.
Validity of the findings: The findings are valid. Speculation is well indicated and underpinned. I do find the section on the predicted gene functions rather long as it remains a prediction and the predictions described do not add very much to our insights. Now they overtake a little bit your own data.
Additional comments: l33+34: not clear how to interpret the numbers or what they exactly refer to
l35: what is the "moon sponge"? It is for the reader at this point not clear that they refer to both species. Or even more?

l78: it should be made clear that "moon sponges" is the colloquial name??? Now it is mixed with classical taxonomic terms. It is ok to use the colloquial terms, but it needs to be specified which taxonomic groups are covered by the colloquial name

l90: From the aim of the study it is not clear how this discriminates the study from the studies of Cuveliers and Chambers.

l160: was template DNA diluted to a certain concentration or was the DNA extraction solution used undiluted?

l184: No water samples were included as reference for the bacterial communities. It would have been better if they had, but I think it is not strictly necessary as it has been proven by many scientists that sponge-associated prokaryotic communities are different from the seawater and that seawater communities do not really interfere with the conclusions taken.

l188: The 16S rRNA gene primer names suggest that only bacterial genes are amplified. Yet throughout the manuscript "microbes" "microorganisms" etc. are used. Microbes comprise the 3 domains of life, so better to change throughout the manuscript to "bacteria".
In the results I see that also Thaumarchaeota were recovered. If the primers target both bacteria and archaea, better use the term "prokaryotes" to refer to both.

l244: Would it be possible to indicate the moon sponge species for Fig 2A-F?
Actually.... although Fig.2 is prettier than suppl. fig 1, I think suppl. fig. 1 is a better figure for the paper than Fig.2

Why are the Cinachyrella and Paratetilla specimens not in both trees in suppl. Fig. 2? Now we can see how they relate to other sponges, but not how they are related to each other rather than only on the morphological characteristics described.

l289: what do the dashed ovals in Fig. 4b signify?

l366: "a change in size frequency..." better include the direction of change. Now it remains a bit mysterious

l434 and on: I don't have fundamental objections against these functional predictions, but think we don't learn so much from this section (85 lines), while the rest of the manuscript is really well covered by solid data.
Also 50% of the conclusion is based on these functional predictions. To my opinion your other results are more interesting


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: POPULATION STRUCTURE AND MICROBIAL COMMUNITY DIVERSITY OF TWO COMMON TETILLID SPONGES IN A TROPICAL REEF LAGOON
Review round: 1
Reviewer: 3

Output:
Basic reporting: Please introduce the common name “moon sponges” both in the abstract (line 35) and the introduction (line 84). Presumably the name refers to both (all?) tetillid species, but this is not explicitly stated.

In fact, there is some general confusion about two species that only becomes clear (to me at least) later on in the manuscript. Namely, that the two species were not distinguished in most of the field monitoring due to there similar superficial morphology. It would be worth to clarify this earlier in the text.

Can sponge species name be added to Fig. 2 – or is not confirmed for these photos?

Line 408: Typo – change “Lopex” to “Lopez”

Lines 410-418: Interest work is summarized here, but a lack of sponge genome data in the present make this paragraph seem a bit tangential (i.e. the data herein do not inform this hypothesis).
Experimental design: Clear research questions and solid study design: multiple years of monitoring, replication in microbiome characterization, and careful taxonomic and phylogenetic analysis of hosts.
Validity of the findings: The data is robust and statistically sound.
Additional comments: The authors present a solid, well-written manuscript that adds to fields of sponge microbiology and coral reef biology. All aspects are well done: from field surveys, to microbiome characterization and comparison, to host taxonomic and phylogenetic analyses. Accordingly, the manuscript yield important and well-supporting new findings. Aside from a few small comments above, the manuscript is in great shape and worthy of publication. I congratulate the authors on a thorough study.


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

Input:
Title: PRODUCTION OF CUPCAKE-LIKE DESSERT CONTAINING MICROBIAL BIOSURFACTANT AS AN EMULSIFIER
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript is in general well written. The authors use numerous references from their group (around 20%) to discuss the results. In order to put their data into context, a more diverse literature should be used. Tables and figures are appropriate.
Experimental design: The subject of the work is within the scope of the journal and is relevant. The methodologies used are well described.
Validity of the findings: The alternative formulation suggested by the authors does not provide clear advantages when compared with the original formulation, and it is more expensive.
Additional comments: The manuscript “Production of cupcake-like dessert containing microbial biosurfactants as an emulsifier” studies the application of the biosurfactant produced by Candida bombicola URM3718 in the elaboration of cupcakes. The biosurfactant was produced using a residue-based culture medium, which resulted in the production of 25 g of biosurfactant per liter. The interfacial activity of the biosurfactant was studied through surface/interfacial tension measurements and through microscopy. The thermal stability of the biosurfactant was also studied through differential scanning calorimetry and thermogravimetric analysis. The biosurfactant was used to replace vegetable fat in cupcakes’ formulation. According to the authors, “cupcakes with biosurfactant incorporated in their dough did not show significant differences in physical and physical-chemical properties after baking when compared to the standard formulation”. Biosurfactants are outstanding molecules with remarkable properties. Their application in the food industry to replace vegetable fat in dough formulation, as suggested in this work, is out of consideration. The amount of biosurfactant used in this work (between 80 and 160 g per Kg of dough) is very high. It is expected the use of biosurfactants, in low amounts, for instance to replace conventional synthetic emulsifiers, and it is expected that their incorporation in dough formulation will improve the properties of the final product. Otherwise, the application of biosurfactants in the food industry will not be economically viable, even if they are produced using low-cost culture media.
Lines 257-261. “The results obtained for surface and interfacial tension for the biosurfactant produced by C. bombicola were 30.790 ± 0.04 mN/m and 0.730 ± 0.05 mN/m, respectively. According to Akbari et al. (2018), biosurfactants with the ability to reduce the surface tension of water from 72 to 35 mN/m and the interfacial tension from 40 to 1 mN/m are effective, being considered good surfactants” However, other biosurfactants such as rhamnolipids and surfactin (and other lipopeptides) reduce the surface tension up to 25-26 mN/m, and the interfacial tension to values as low as 0.001 mN/m. Furthermore, they exhibit critical micelle concentrations considerably lower (10 mg/L) when compared with the biosurfactant produced by C. bombicola URM3718. The authors should compare the biosurfactant herein studied not only with biosurfactants previously reported that exhibit a similar or worst performance, but also with biosurfactants that exhibit better properties. In that sense, more appropriate references should be used. In summary, this biosurfactant exhibits a weak activity when compared with others previously reported.
Lines 264-268. An advantageous method was used to recover the biosurfactant, avoiding centrifugation and filtration (i.e. without removing the cells). How does this affect to the purity of the biosurfactant recovered? Which was the purity of the biosurfactant used in this work?
Lines 273-276. “CMC is related to the efficiency of surfactants and ranges from 0.001 to 2 g/L for biosurfactants. Biosurfactants are more efficient as they have reduced CMC (Santos, Luna, Rufino, Santos & Sarubbo, 2016). Thus, the C. bombicola biosurfactant proved to be efficient, since it had a CMC of 0.5 g/L”. Once again, the biosurfactant herein studied is considerably less efficient when compared with those that exhibit considerably lower CMCs. That point should be discussed in the manuscript. By the way, in the Abstract it is referred that the CMC is 0.6 g/L.
Regarding the emulsifying activity, the authors state that “the increase in the concentration of biosurfactant did not exert a significant increase over the emulsification percentages”, although biosurfactant concentrations below and above the CMC were studied. Biosurfactants usually exhibit higher emulsifying activities at concentrations above the CMC, how can the authors explain this behavior for this biosurfactant?
The results obtained in the study of the antioxidant activity of this biosurfactant should be compared with those obtained for other biosurfactants (or similar compounds) in order to assess the potential of this biosurfacant.
Regarding the characterization of the cupcakes elaborated with the different formulations, “The results demonstrate that there were no major discrepancies between the different formulations in relation to the evaluated parameters… the partial or total replacement of vegetable fat by the biosurfactant did not cause significant changes in the physical properties of the cupcakes”. Which is the advantage of replacing vegetable fat by a more expensive ingredient (biosurfactant)?
Lines 382-384: “As a consequence, cupcakes containing vegetable fat in their composition had a higher moisture content compared to cupcakes that contained biosurfactant in the formulation”. This seems to be a disadvantage.
Lines 386-387: “Considering that the C. bombicola biosurfactant has a glycolipidic nature (Luna et al., 2016)”. Lines 389-391: “about 75% of the fatty acids of C. bombicola glycolipid are unsaturated (C18: 1, C18: 2 and C18: 3), while the other 25% are saturated fatty acids (mainly C16: 0)” This characterization corresponds to the same biosurfactant herein studied? Which is the exact chemical composition of this biosurfactant, including the carbohydrate fraction?
Lines 403-405: “Since the biosurfactant is a glycolipid formed by carbohydrate units called glycans, it may have contributed to the increase in the carbohydrate content of the formulated product.” This is a general assessment. Which is the structure of the glycidic fraction of the biosurfactant herein studied?
Lines 412-415: “Regarding the pH of the cupcakes, there was a decrease when the biosurfactant was added to the formulation in increasing concentrations. This occurred due to the pH value of the biosurfactant production medium, which at the end of the fermentation reaches values around 6.2” The biosurfactant was not purified from the culture medium before its addition to the dough? Is it not possible to adjust the pH of the biosurfactant solution to avoid these variations? I cannot understand which is the effect of the pH of the culture medium in the pH of the final formulation.
Lines 418-432: The authors compare the surface activity and the amount of biosurfactant produced by the yeast strain herein studied with the data obtained by other researchers. However, most of these works come from the same group! The authors should take a look to other works from other researchers reporting biosurfactants produced by different yeasts with better surface-active properties. The same can be said regarding the emulsifying activity (lines 433-441).
A.E. Elshafie, S.J. Joshi, Y.M. Al-Wahaibi, A.S. Al-Bemani, S.N. Al-Bahry, D.Al-Maqbali, I.M. Banat, Sophorolipids production by Candida bombicola ATCC22214 and its potential application in microbial enhanced oil recovery, Front. Microbiol. 6 (2015) 1324
G.L. Maddikeri, P.R. Gogate, A.B. Pandit, Improved synthesis of sophorolipidsfrom waste cooking oil using fed batch approach in the presence ofultrasound, Chem. Eng. J. 263 (2015) 479–487.
Kaur G et al. 2019. Efficient sophorolipids production using food waste. Journal of Cleaner Production 232:1-11.
Alimadadi N et al. 2018. Efficient production of tri-acetylated nono-acylated mannosylerythritol lipids by Sporisorium sp. Aff. Sorghi SAM20. J. Appl. Microbiol. 124(2):457-468.
Lines 430-432: “Pinto et al. (2018) obtained a yield of 61 g/L using C. bombicola in a bioreactor, with the same extraction methodology used in this work, indicating the feasibility of this method to increase the yield of production in biosurfactant” I do not believe that the extraction method used has influence in the amount of biosurfactant produced.


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: PRODUCTION OF CUPCAKE-LIKE DESSERT CONTAINING MICROBIAL BIOSURFACTANT AS AN EMULSIFIER
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript number 46042 described biosurfactant production by Candida bombicola URM 3718 and its possible application in food industry.

The work is clear presented and included relevant results
Experimental design: no comment
Validity of the findings: no comment
Additional comments: 1.	The authors do not describe about the purification rate of the biosurfactant, could the authors specify if the crude or the purified biosurfactant was used in this study.
2.	Nature of the biosurfactant was not established in this study, could the authors explain why they refer to a previous study of biosurfactant production by the same strain even the extraction method was different and maybe some characteristic of the biosurfactant too?
3.	The authors used the fact that the biosurfactant was a glycolipid in nature to explain the decrease of protein and the increase of the carbohydrate in the cupcakes when the concentration of the biosurfactant was increased, while the composition of the biosurfacant given in the reference was “The preliminary analysis demonstrated that the biosurfactant isolated from C. bombicola consisting of 70% lipids, 10% carbohydrates and 20% proteins”. (Luna et al, 2016). Could the authors explain this?
4.	Could the authors discuss if the decrease of pH from 8.19 to 6.3-6.6 can affect the quality of the cupcakes?
5.	In the conclusion, line 478: cookies or cupcakes?


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: PRODUCTION OF CUPCAKE-LIKE DESSERT CONTAINING MICROBIAL BIOSURFACTANT AS AN EMULSIFIER
Review round: 1
Reviewer: 3

Output:
Basic reporting: Paper is very much clear. Professional English is used
Recent references are also cited well
Experimental design: Experimental design is also fine
Validity of the findings: Need to improve information in the table and figure with respective to concentrations. Figures are not labelled properly
Additional comments: Isolation of biosurfactant
99 A method developed in the laboratory was used, which initially consisted of extraction with ethyl100 acetate, twice, in the proportion 1:4 (v/v) of the non-centrifuged broth. Then, the organic phase 101 was centrifuged (2600xg for 20 minutes) and filtered. The filtrate was transferred back to the 102 separating funnel and a saturated NaCl solution was added to separate the remaining aqueous 103 phase. The organic phase was transferred to an Erlenmeyer flask and anhydrous MgSO4 was 104 added until granules were formed, which were filtered and dried at 50 ° C.

What about other debris and metabolites? It is not mentioned anywhere  how purified biosurfactant was purified?

Table 5(on next page)
Percentage of viability of the C. bombicola URM 3718 biosurfactant against the L929 and the Vero strains.
What is the concentration? It is not mentioned in the table.

Physical properties of cupcakes after baking for the standard formulation (100% vegetable fat), formulation A (50% vegetable fat + 50% biosurfactant), formulation B (25% vegetable fat + 75% biosurfactant) and formulation C (100% biosurfactant). Data expre…….
Typo errors
At many places such type errors are seen.
For example
Physical-chemical composition and energy value of cupcakes for the standard formulation (100% vegetable fat), formulation A (50% vegetable fat + 50% biosurfactant), formulation B (25% vegetable fat + 75% biosurfactant) and formulation C (100 % biosurfacta

Physical properties of cupcakes after baking for the standard formulation (100%
vegetable fat), formulation A (50% vegetable fat + 50% biosurfactant), formulation B
(25% vegetable fat + 75% biosurfactant) and formulation C (100% biosurfactant). Data
expre

Table 4(on next page)
. Percentage of sequestration of the radical 2,2’-azino-bis (3-ethylbenzothiazoline-6-
sulfonate) (ABTS•+) by the biosurfactant. Data expressed as mean ± S.D. of triplicate
determinations.

Table 5(on next page)
Percentage of viability of the C. bombicola URM 3718 biosurfactant against the L929 and the Vero strains.
What is the concentration? It is not mentioned in the table.

Figure 1
Critical Micelle Concentration (CMC) of the biosurfactant isolated from Candida bombicola URM 3718
Indicate CMC value in the figure
Information can be represented with CMC concentration and suface tension value


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: PRODUCTION OF CUPCAKE-LIKE DESSERT CONTAINING MICROBIAL BIOSURFACTANT AS AN EMULSIFIER
Review round: 2
Reviewer: 1

Output:
Basic reporting: The manuscript is in general well written. Tables and figures are appropriate.
Experimental design: The subject of the work is within the scope of the journal and is relevant. The methodologies used are well described.
Validity of the findings: The alternative formulation suggested by the authors does not provide clear advantages when compared with the original formulation, and it is more expensive.
Additional comments: The answers given by the authors to my questions are not convincing to change my evaluation. Some questions were not properly answered, as for example those related with the purity and the chemical structure of the biosurfactant herein used. The main concern is that the alternative dough formulation suggested by the authors did not provide clear advantages when compared with the original formulation, and it is considerably more expensive.
According to the answers given by the authors, “this study presents an initial study aiming to evaluate if the biosurfactant (at high concentrations) can exert the same effect as the vegetable fat in physical, physicochemical parameters and texture profile of cupcakes”. The final result is a more expensive formulation (the cost of the biosurfactant is considerably higher when compared to the vegetable fat) which does not improve the properties of the final product.
Also, according to the authors, “the results obtained serve to support future studies that seek to decrease these (biosurfactant) concentrations and increase industrial viability. Studies with lower (biosurfactant) concentrations, based on the positive results obtained in this study, together with the sensory evaluation, are going on” Maybe the authors should focus in those studies, using lower biosurfactant concentrations, in order to obtain more promising results.
Although I agree with the statement of the authors: “there is an increase interest of the market for products of better quality”, it is also true that consumers also look at the price. Which was the real improvement of the properties of cupcakes containing biosurfactant when compared with those containing vegetable fat? And which would be the increase of production costs?


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: PRODUCTION OF CUPCAKE-LIKE DESSERT CONTAINING MICROBIAL BIOSURFACTANT AS AN EMULSIFIER
Review round: 2
Reviewer: 2

Output:
Basic reporting: The manuscript number 46042:1 described biosurfactant production by Candida bombicola URM 3718 and its possible application in food industry.

New references are added to the revised version of this paper
Experimental design: The experimental design is well done
Validity of the findings: The work is clear presented and included relevant results.
Additional comments: No additional comments


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

Input:
Title: PRODUCTION OF CUPCAKE-LIKE DESSERT CONTAINING MICROBIAL BIOSURFACTANT AS AN EMULSIFIER
Review round: 2
Reviewer: 3

Output:
Basic reporting: Authors have addressed all the queries
Experimental design: Revised manuscript is satisfactory
Validity of the findings: They are well supported
Additional comments: Authors have addressed all the queries satisfactorily


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: WITHIN-HOST COMPETITION DRIVES ENERGY ALLOCATION TRADE-OFFS IN AN INSECT PARASITOID
Review round: 1
Reviewer: 1

Output:
Basic reporting: This manuscript is clearly written for the most part. A few passages are a bit awkward, and some statements, especially in the Introduction seem vague or imprecise and could be improved with careful proofreading. For example:
Abstract Lines 53-56 this is a bit vague. Also, the first “rules” could be omitted.
Introduction
L. 82-consequences for?
L. 85 “evolutionary target” – evolution has no target. I’m not sure what is meant here.
L. 86-87 to what end?
L. 87-88 In what way?
L. 94 – what is meant here by “outline”?
L. 96. Insects are not really modular, like a coral for example. They are metameric, with segments specialized as groups into tagmata. The use of terms like body parts and segments in the manuscript is confusing, as a segment has a specific definition in insects. Perhaps they should use terms such as tagmata and appendages
L. 100 constraints on selection
L. 101 fitness related traits?
L. 104,106 work on
L. 109 tradeoffs between what? Be more precise.
Some citations include first and middle initials, some don’t, some have full first names written out, some are italicized…
L. 111-112 doesn’t allometry always involve size? And generally not tissues but structures or organs?
L. 126 Always spell out generic names at the beginning of a sentence.
L. 136 – the authors can’t mention their field site without saying something about it (e.g., where it is)
L. 171 these are usually referred to as sexual patches (Cerretti et al, 2014 First report of exocrine epithelial glands in oestroid flies: the tachinid sexual patches (Diptera: Oestroidea: Tachinidae). Nuptial pad is a new and unnecessary term.
L. 206 Tracheae
L. 229 It is probably best to avoid contraction like didn’t
There are also punctuation errors, e.g., extra ) or . that need to be fixed

The authors provide a brief overview of life history theory and allometry that is sufficient, though see comments above on precision. On line 146 they state that theirs is the first study to examine cohort resource competition in Tachinidae, but this is false. In fact, many studies have examined numbers and size and survival of tachinids in hosts observationally and experimentally. This study fails consider this previous literature and place its results in this context, and this is a major fault. However, this is likely the first study to assess energetic allocation among tagamata relative to size.
Structure - fine
Figures – The figures are generally well-constructed and illustrate the man results. Perhaps make males and females easier to distinguish if the paper is printed in grayscale.
Data from the paper appear to be available on Zenodo
Experimental design: The study fall within the scope of the journal
The questions are clearly stated
The authors use each fly as an independent sample in analyses, yet they come from only 7 hosts. This does not seem appropriate. Flies within a host experience the conditions of that particular hosts and interact with one another. In addition, they are likely to be genetic siblings. Thus it seems that mean values per host should be used as independent data points. The authors include host as a random variable to account for this non-independence, but this still strikes me as pseudoreplication. The patterns may remain with N=7, but they may be altered and significance of some factors may change.
For assessment of energy allocation, it may be more appropriate to treat each fly as an independent sample despite genetic non-independence.
 Is the energetic content of lab-reared hosts relative to head widths the same as those in the field?
L. 183 it is a little unclear what is meant by “binned?” How many measures were taken per body region?
What is the total number of flies examined?
L. 213 Joy in playing???
Validity of the findings: The study fall within the scope of the journal
The questions are clearly stated
The authors use each fly as an independent sample in analyses, yet they come from only 7 hosts. This does not seem appropriate. Flies within a host experience the conditions of that particular hosts and interact with one another. In addition, they are likely to be genetic siblings. Thus it seems that mean values per host should be used as independent data points. The authors include host as a random variable to account for this non-independence, but this still strikes me as pseudoreplication. The patterns may remain with N=7, but they may be altered and significance of some factors may change.
For assessment of energy allocation, it may be more appropriate to treat each fly as an independent sample despite genetic non-independence.
 Is the energetic content of lab-reared hosts relative to head widths the same as those in the field?
L. 183 it is a little unclear what is meant by “binned?” How many measures were taken per body region?
What is the total number of flies examined?
L. 213 Joy in playing???
Additional comments: see other fields


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: WITHIN-HOST COMPETITION DRIVES ENERGY ALLOCATION TRADE-OFFS IN AN INSECT PARASITOID
Review round: 1
Reviewer: 2

Output:
Basic reporting: OK
Experimental design: The aims are a bit too desciptive and therefore of not too high relevance. Some rewriting can help.
Validity of the findings: Statitical treatment should be more transparent in some aspects.
Additional comments: This study shows that parameters of the host influence body sizes of a gregarious dipteran parasitoid, and that flies of different sizes make different allocation decisions. There seems to be nothing fatally wrong with the study, and the piece of knowledge provided by this paper is definitely welcome. Nevertheless, everything remains at a quite descriptive level, the choice of the examined relationships appears not to be based of any theory-driven a priori hypotheses, and, consistently, the results appear to be underdiscussed. The reader is left with an “and so what?” –feeling. Should we have expected something different, and why?

Specific/minor:
•	It would add to information content of the Abstract if you said something about the magnitude of the differences, e.g. the flies differed in weight X.X times.
•	Line 59. Any conclusions about reproduction and dispersal are indirect at best, so these should not be mentioned in the Abstract at least.
•	Tell us more about the biology of the tachinid. There are aspects important in the context of the present study. Do the parasitoids fully consume the bodies of their hosts? (If not, we should not expect much competition). Do the females adjust their clutch sizes to the size of the host? (If yes, this could eliminate the effect of host size on competition intensity).
•	Line 81, 103 and in many other places. Given names are not normally included in such references.
•	 Second paragraph of the Introduction. I think that here the authors should explain how do they understand/define life-history trade-offs in the context of this study. I think that this would contribute to clarifying both the authors’ and the readers’ thoughts (see below about inferring about trade-offs).
•	Line 125. Also of plants?
•	The description of methods is too detailed in parts. For example, it does not help if we know the size of the cups (line 159), neither need we know that the insects were transported back to Tucson (line 160). Details which could not have affected the results in any way should not be presented.
•	Line 162. It is not very clear what do you mean with ‘quality’ of the host larvae. In particular, do you imply that that there are aspects of quality other than size? If yes, please specify. If not, I think that it is better to avoid the ambiguous term ‘quality’ and to talk about size only.
•	Tell us more about head capsule width. I guess that you mean that head capsule width of last instar describes the weight of the larvae in the beginning of the last instar, and tells us how much food the parasitoids actually had, while the mass of the larva later during the development is affected by parasitism and is therefore not a reliable measure of the initial amount of the resources. If so, please say this more directly.
•	Line 194. I do not understand ‘robust’ here, may be my fault.
•	Line 198-200. I do not fully understand this. Do you mean that you derived a size vs energy content relationship which was common to both sexes? If so, I think that this is not good because the content of abdomen is very different in males and females. If not, please reformulate to avoid misunderstandings.
•	Data analyses. OK, you nicely tell us which models did you have for the analyses of size but you do not tell in sufficient detail how did you select the models to drive the allometric relationships which still constitute the primary output of the paper. How was host individual treated in those analyses? I think that these models should be presented in full in a supplement as a minimum.
•	Line 237. Body size is a vague term. Perhaps ‘with body mass’?
•	Lines 238-239. I do not understand.
•	Line 252. “Normalized” can mean different things. Be more specific.
•	Line 268 and elsewhere: most definitely, you cannot conclude about the existence of trade-offs on the basis of just correlative data. A negative correlation between two things can arise in an indirect way, a correlation as such does not prove a trade-off. As a maximum, you can say that you found a pattern consistent with a potential trade-off.
•	Line 285. “only in hymenopterous…” may be misleading. There are lots of such studies on Drosophila I guess?
•	Line 313. “Flies …”. Here starts a superlong sentence which must be reformulated for the sake of clarity.
•	Line 315. I would cite Davis, R. B., Javoiš, J., Kaasik, A., Õunap, E. and Tammaru, T. 2016. An ordination of life-histories using morphological proxies: capital vs income breeding in insects. - Ecology , 97: 2112-2124  instead of Tammaru and Haukioja here.
•	 References carelessly prepared, e.g. given names of the authors are sometimes presented (unusual), sometimes not.
•	Figure 1 text. “predicted” little unclear here. Averages corrected for sex?
•	May be this is old-fashioned but I am used to  the requirement that figures should be readable also in black and white. Your “green” and “red” cannot be distinguished in my printout.
•	Figure 2. Is “fly weight” (x-axis) and “body weight” (y-axis) the same thing? If yes, please unify. If not, please explain. If yes, then may there be a problem: the variables on the axes contain common elements which may lead to artefacts:  Brett, M. T. 2004. When is a correlation between non- independent variables “spurious”? Oikos 105:647–656. Please check and comment.
•	I understand that I should not teach native speakers but I am not used to see “didn’t” etc in scholarly texts.