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: IT’S A MATTER OF DESIGN—HOW PITFALL TRAP DESIGN AFFECTS TRAP SAMPLES AND POSSIBLE PREDICTIONS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The basic reporting is fine except for some minor points listed under general comments.
Experimental design: The experimental design is fine regarding differences between single traps of various types. However, the alternative of using clusters of multiple simple versus single (or few) more sophisticated traps has not been directly investigated (as clusters of simple traps were not studied). Additional data would be needed, here, or more careful wording in parts of the discussion. Information on the handling time and cost of the different types of traps is also highly relevant and should be added to the manuscript if possible. See also general comments.
Validity of the findings: See comment on the limits of the experimental design.
Additional comments: Some minor comments and explanations of the above statements (in the order of appearance in the manuscript).

L27: Long sentence - better split into 2-3.

L31: As traditions differ, it is not clear what the conventional pitfall type is. Please use a more precise term. "simple" would already be better (as is already used in the discussion).

L34: ...more effective than...

L34: Please specify how much more effective p.t. with guidance barriers are (20% more, ten times as, etc.)

L38: I suggest to replace "detrimental effects" with something more direct, such as "reduced catches".

L63: Replace "regard" with "consider".

L66: "pit in the soil" is misleading - it should be clear that a container is involved, e.g. "container sunk in the soil"

L69: Additional traps placed in the same sampling location are usually not replicates with respect to the study design. Better use "sampling effort", here.

L71: Do singletons increase accuracy? I think accuracy applies to the common species that are caught in high numbers. Singletons are always highly stochastic.

L87: "detrimental effects on ... arthropod assemblages" implies that the local populations would suffer from the presence of these structures. You probably mean reduced number or different composition of the catch. This is already said in the first half of the sentence, so the second half can be removed.

L88: "capture efficiency" is return per effort, but you provide no information on effort (e.g. cost, or handling time of the different types compared). Better use a more neutral term such as "catches".

L163: replace "much" with "many"

L180, 183: pitfall trap studies can rarely count as experiments in a strict sense - better use "survey" or, neutral, "study".

L196: The question is (a) if multiple (e.g. 4) "conventional" traps together produce a more or less meaningful catch than a single X-barrier trap, and (b) if the effort (handling time and cost) are higher for either alternative. The lack of comparison between groups of "conventional" to single X-barrier traps does not allow strong conclusion in that respect. As an indication, you could combine the information of 4 (or 5) type A and type B traps in Fig. 4 to approximate the result obtained with such a trap cluster (you can only approximate, because your single A and B traps were spatially spread out over a much larger area than it would be done if they were used as clusters to characterize some local assemblage). I would be curious if the combined A type falls within the single X-barrier traps in terms of species composition.

L197: How do you know that the catch of a single X-barrier trap is not comparable to the sum of four A type traps? Your sentence also suggests that comparisons between studies are possible as long as A type traps are used. Given all the other sources of variation (material, cover, fluid, time, person), comparability is always limited.

L202: How reliable are the results of these species accumulation curves? There were less species in the V than in the X traps, the difference was just not significant. I agree that catching almost as many species among only a quarter of the individuals is striking. Nevertheless, a more careful wording may be advisable, here. Based on your results (and my guess that installation of V is nearly as laborious as X), I think there are good reasons to recommend X-shape (or multiple A) rather than V.

L219: How do you know that the higher catch in A than B traps are not due to the 'digging in effect'? What puzzles me, however, is why the 'digging in effect' is always seen as something negative on the one hand, and on the other hand people put effort in catching more individuals (with barriers etc.). If the 'digging in effect' boosts catches - fine!

L221: Replace "in this design" with "when using PVC rims".

L228: "...due to the reduced and size-biased catches produced by this pitfall..."

L233-235: Please write something more direct. The conclusion from your study is that the type of trap not only affects numbers of individuals and species caught, but also their trait composition.

L239: Please rewrite in a way in which readers get an idea what kind of a nested design you recommend without reading Kotze et al. (2011) in addition to your article.


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: IT’S A MATTER OF DESIGN—HOW PITFALL TRAP DESIGN AFFECTS TRAP SAMPLES AND POSSIBLE PREDICTIONS
Review round: 1
Reviewer: 3

Output:
Basic reporting: See general comments to authors
Experimental design: See general comments to authors
Validity of the findings: See general comments to authors
Additional comments: This manuscript describes a comparative study with a focus on pitfall trap efficiency in cases where an ordinary trap is coupled with an expanded plastic rim plate or with two different guidance fence types. The authors compared the catches of carabid and rove beetles, and spiders, by setting three traps of each “design” in a meadow, and by analyzing the data using GLM, NMDS and abundance plots. The data as such are surprisingly large and the analysis methods are appropriate. Also, the paper is clearly written so my concerns may be considered relatively minor.

1. I understand that this is not a literature review but it is still striking that only three references are before the year 2000. Many key references are clearly missing: for example, the authors refer to “digging-in effect” without citing Digweed et al. (1995/Pedobiologia) or any of the Greenslade or Barber papers from the mid-1900s, let alone many others since then. I suggest the authors make a more thorough literature search and add these original references instead of rather frequent use of a few review papers from 2000s.
2. Summary may benefit from fine tuning. The first sentence is too long and should be split into two. Line 31 notes “rim” but any jar, cup or bottle has a rim: it may be better to call the structure “an extended rim plate” (or something like that). Line 32 mentions “guidance barriers” but strictly speaking these are not really barriers (that would hinder beetle movements) but rather “guiding fences” (or something like that). Regarding “rim” and “barrier”, I strongly suggest check the text throughout to clarify and fix these. Moreover, line 35 requires clarifications (not understandable currently).
3. Text, line 78 should add reference Digweed et al. 1995/Pedobiologia.
4. Please clarify the sampling design a bit: within each plot, how exactly were the traps placed relative to each other: in a row, in a square, randomly…? Also, In data collecting section perhaps say clearly that the trap as such was similar for each “design”.
5. The number of replicates per design was very low (3) which reduces the analysis power and makes the estimates of mean and variance difficult. Perhaps add a few words about this to Discussion.
6. It is kind-of good to check spatial autocorrelation but I would suspect that the use of plot as a random variable takes care of that (as it apparently indeed did).
7. Discussion is very thin as only four references were cited here! I strongly suggest do a thorough literature search and cite many more papers than currently (see comment #1).
8. Discussion could perhaps briefly note that the use of fences to increase catches might result in biases toward more actively moving species.
9. Please add totals for carabids, rove beetles and spiders to the different columns of Table 1.


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: NITROGEN ADDITION INCREASES THE CONTENTS OF GLOMALIN-RELATED SOIL PROTEIN AND SOIL ORGANIC CARBON BUT RETAINS AGGREGATE STABILITY IN A PINUS TABULAEFORMIS FOREST
Review round: 1
Reviewer: 1

Output:
Basic reporting: (1) In the whole article, almost all the unit of N addition rate are wrong. For example, in line 9, the g N-2 y-1 is wrong. Please check and revise throughoutly.
(2) Some literature references, agricultural ecosystems, are not closely related to the topic of this study. For instance, lines 57-63,  88-93---
(3) The figures are not appropriately shown, for example the different colours of the columns are lack of enough distinction. And the lowercase and uppercase letters should be exchanged in order to make a more understandable expression.
(4) Please give the elevation and slopethe of the study area in detail, because these two variables are important to explain the results.
Experimental design: (5) In lines 139-142, the authors said that the levels of N addition rate were designed based on the national mean N deposition rate (2.11) reported by Lü & Tian (2007). First, I think a more reliable value is needed according to references (also includs chinese papers). Second, the year 2007 is long-time ago to support your design. Third, the mean N deposition rate (2.11) is a relative high value which can potential affect the result under the current treatments (0,3,6,9). Please explain or discuss the uncertainty.
(6) Please indicate the distribution of the plots. Randomly? And how to treat the litter layer?
Validity of the findings: (7) In fig. 1, please explain why the micro-aggregates have the highest contents of T-GRSP?
(8) In fig. 2, please explain why the SOC increased so much under the three N addition treatments only over two years?
Additional comments: line 12, 'clay–silt aggregate'? is this correct?
line 15, 'variable' is not a clear word
lines 23-24, Redundant sentences. no clear message
line 32, 'negative effects' All negative below?
line 35, available N? what does it mean?
lines 57-63, delete because these are not closely related.
line 73, EE-GRSP, full name
line 74, T-GRSP, full name
line 128, 'surface soil' mineral soil? in detail of the depth.
line 130, hm2? should be ha?
line 149, why choose 0-20 cm? Does this include the litter layer?
Table 2, mean weight diameter (MWD)? or the aggregates distribution?


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: NITROGEN ADDITION INCREASES THE CONTENTS OF GLOMALIN-RELATED SOIL PROTEIN AND SOIL ORGANIC CARBON BUT RETAINS AGGREGATE STABILITY IN A PINUS TABULAEFORMIS FOREST
Review round: 1
Reviewer: 2

Output:
Basic reporting: Overall the paper is well written and meets the standards of the paper, but it could benefit for another round of editing. There are a few places in the text were the sentences structure needs editing and also place were letters are missing in words. It is possible that I did not catch everything so please take some time to go through it again.
Line 7 - “ changes soil aggregate stability when it alters the” could be clarified by writing “ changes soil aggregate stability by altering the”
Line 30 – also the clarity here could benefit from some editing by changing  “rapid increase in global nitrogen (N) deposition, which is expected to increase by 70% in 2050 than in 2000” to “rapid increase in global nitrogen (N) which is expected to increase by 70% in 2050 compared to 2000”
Line 31 – capital T is needed after punctuation
Line 33 – space needed between “rates” and parentheses
Line 39 - “these aggregate” - needs an “s” at the end
Line 105 – First sentence beginning with “However” is not needed.
Line 131 – the average height of the tree is probably not “11.2 mm”
Line 151 – add capital letter “T” after punctuation
Line 154 – instead of “filtered through” it might be better to use “sifted through” or “passed through”
Line 155 -  plot instead of “pot”
Line 196 – add “in all samples” at the end of the sentence before the parenthesis.
Line 280 – remove “high because”
Line 311 – add “to” between “fails support”

Literature references:
The paper is very well referenced and the author does a nice job giving credit to a diverse group of authors. One of the references is a little old – would it be possible to find a reference of a newer date? Obviously some times that is not possible and many older references are key to the research conducted in this paper.
The reference eluded to is – Line 31 – Galloway et al., 2004
Dirnböck, T., Foldal, C., Djukic, I. et al. Climatic Change (2017) 144: 221. https://doi.org/10.1007/s10584-017-2024-y    might not have the exact year estimates, but adds a nice focus on climate change and therefore supports the importance of the understanding of the effect of N deposition.

The introduction is generally well written and gives the reader the overall level of information that is needed to understand the importantance of the paper and the questions stated.
Improvements in the understanding of the methods used for aggregate stability would be of great benefit to the reader. In line 74 – the mean weight diameter is mentioned, but not thoroughly introduced. Please explain what MWD measures and why this method is used.

It is easy to understand the importance of the study from the introduction, but it might be helpful for the reader if the two hypotheses  were stated in line 119 as a way to wrap up the introduction. That way they are clear from the beginning and it makes it easier to follow the rest of the paper.
The last sentence in the introduction is very bold. The data represented in this paper does not reveal the underlying mechanism for soil aggregation stability in response to N addition. Please rewrite this concluding sentence to more accurately summarize the overall goal with this study.
Experimental design: The research fits with in the scope of the journal and the question is well defined. It is a field were more research is needed and it would be nice to see this study continued beyond 2 years to see what effect time will have on the aggregate stability. For ecosystem studies such as this, 2 years is when you might expect to start seeing changes, but aggregate formation might be much slower process in a natural ecosystem than what has been seen in cultivated fields therefore 3-5 years should be considered.
The description of the study area is impressive and hopefully all the data collected on the biomass can also be use in a long term study on the effect of N deposition on plant community composition, growth rate of trees etc.
 A few edits could improve the understanding of the experimental design
Line 144 – 147 – it is not clear if a sample was collected before addition of N. Please also clarify if samples were collected in 2016. A re-write of this section would make the time line for collection of samples more clear.
Line 149 – saying “In September 2015” makes it sound like that was the only time samples were taken. Please clarify.
Line 151  - no need to say “First” and the line 152 – starting with Second is not needed
Line 159  - it might be worth changing this sentence to saying - “samples (100 g) placed in a 250 um sieve and submerged in deionized water for 5 min”
Methods:
It is not clear to the reader why pits needed to be dug. Sampling from above using a soil corer would seem simpler than to create a larger disturbance in a fairly small plot area.  What was used to “drill” a sample? What was the volume sampled? What is meant by “along natural fissures”. Please clarify the sampling method.
Also in line 155 – how were the samples stored?
Maybe add in line 171 – that it was the pellet that was re-extracted 5 times.
The issue with glomalin extraction is often that it can not be separated from total protein using the Bradford method. The two papers listed below address this issue and one also suggest using another method for detection. It would strengthen the discussion to talk about the bias in the method – and that the increase in T-GRSP could be from an increase in other proteins than glomalin.  Take a look at these two papers and incorporate them in the discussion as suggested above.  Roberts and Jones, 2008. Critical evaluation for determination of total soil protein in solution. Soil Biology and Biochemistry Vol 40 Issue 6. 1485-1495; Zbiral et al., 2017. Determination of glomalin in agriculture and forest soils by near- infrared spectroscophy. Plant Soil Environ. Vol 63, No. 5: 226-230.
Validity of the findings: The results section is well written and complete. The use of statistics in the analysis is appropriate and well done, but the conclusion in writing is some times contradicting the results described from the analysis.  In the section from line 196-201 the author first describes that there is no significant difference between samples and then in the next line differences are described. Line 199-201 should not be included since there is no significant difference between the samples and therefore the pattern described is not valid. In line – 217 another set of data is described where not all of them are significantly different from each other and can therefore not be listed as such.
Three significant digits are provided for the results listed in line 204, 216, 239, 240 – are the methods used in this study sensitive enough to provide that kind for resolution?

In the discussion in line 281-285 speculations are made why the decrease in EE-GRSP  drops while the T-GRSP continues to accumulate. From this study it can not be concluded that the T-GRSP will not continue to go up and the possibility that it will stay high or increase should also be discussed. As mentioned above the measurement of total protein in the soil might not be able to be distinguished from the T-GRSP. Please consider the llimitations of the method used and the possibility of an increase in other soil proteins.
In line 296-297 – could it also be that decomposition rates are increase not just plant growth?
Additional comments: It was a pleasure to read the paper and I look forward to seeing more papers linked to this study to answer some of the questions posed.
Continuing the study for 3-5 more years would be highly recommended and to experiment with using near-infrared spectroscopy for analysis of the glomalin would be interesting. Other methods such as microbial ecosystem analysis and respiration rate would add to the understanding of the complexity of the effect of N deposition. And so would analysis of plant community composition and growth rate of trees over time. Hopefully similar studies will be conducted other places in the world so that we can gain a better understanding how the soil type, texture class, OM content etc. of soils play a role in the effect of N deposition and aggregate stability. Good luck with future investigations!


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: NITROGEN ADDITION INCREASES THE CONTENTS OF GLOMALIN-RELATED SOIL PROTEIN AND SOIL ORGANIC CARBON BUT RETAINS AGGREGATE STABILITY IN A PINUS TABULAEFORMIS FOREST
Review round: 2
Reviewer: 1

Output:
Basic reporting: The revision is acceptable.
Experimental design: The revision is acceptable.
Validity of the findings: The revision is acceptable.
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: EFFECTS OF TEMPERATURE AND SALINITY STRESS ON DNA METHYLATION IN A HIGHLY INVASIVE MARINE INVERTEBRATE, THE COLONIAL ASCIDIAN DIDEMNUM VEXILLUM
Review round: 1
Reviewer: 1

Output:
Basic reporting: The authors investigate DNA methylation in rapid response to environmental stress. The manuscript is quite well written. It is clear and unambiguous, professional English is used throughout. The article conforms to professional standards. It cites relevant literature and sufficient background is provided for readers from diverse backgrounds. The work is also strongly connected to a broad filed of knowledge and a widely-interesting research area.

The manuscript follows professional article structure, sufficient information is shared to judge the conclusions. All tables and figures are easy to follow and present necessary information. It is self-contained and includes all relevant results necessary to support the hypothesis.
Experimental design: The manuscript describes original research that fits the aimss of the journal. The research question is well defined and fills an identified knowledge gap. The research is highly rigorous to a high technical & ethical standard. All techniques are well described and used accurately, following common standards. The methods well described, and no issues exist with what was done.
Validity of the findings: The results are valid and meaningful to a wide audience. Data are robust, methods and analysis were statistically sound, the experiment followed proper controls.
The conclusions were clear and well supported. There is little issue with the manuscript in general and the results and conclusions are quite strong.
Additional comments: I found this manuscript to be extremely well written. The methods, results, and conclusions were sound. I found no issues with the presentation. I think the results are quite interesting. The use of MS-AFLP was appropriate and generated an interesting finding that supports a growing field of research.


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: EFFECTS OF TEMPERATURE AND SALINITY STRESS ON DNA METHYLATION IN A HIGHLY INVASIVE MARINE INVERTEBRATE, THE COLONIAL ASCIDIAN DIDEMNUM VEXILLUM
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript presents an interesting study documenting rapid DNA methylation response to the effects of temperature and salinity stresses in the highly invasive ascidian Didemnum vexillum. This manuscript is well written and easy to follow. However, some modifications on tables and figures are still needed. In Table 1, the ‘/’ in selective primers HapII + TCC is unnecessary. In Figure 4, ‘Time 0’, ‘Time 1’, ‘Time 2’ should be labelled on A), B), C), respectively, to increase the readability. In supplementary Table S9, there may have some errors in the details of sampling times, as ‘T3’ was not referred in this paper. In addition, lines 86-90, I suggest to add several sentences to summarize why ascidians are good models for studying invasion success..
Experimental design: This manuscript takes advantage of asexual reproduction to reduce the possible effects of genetic variation on epigenetic results. However, I got confused why authors conducted the analysis of molecular variance (AMOVA) for NML at different treatments and different sampling time points (TableS4, TableS6, TableS9, TableS11). Colonies allocated in each treatment are assumed to be derived from the same source and the genetic background should be very similar. Furthermore, all colonies survived under stresses, which may suggest both temperature and salinity do not have a selective effect on genetic variation. So the results of AMOVA among groups and within each group should be not significant. However, significant different results were observed between differential salinity treatments at T0 in NML (lines 271-272). This may be due to the very different genetic background of samples (lines 128-129 it may be two or more colonies growing in close proximity). So, it is needed to further discuss how to control the genetic effects on epigenetic results. In addition, based on statistical methods, NML fragments were also produced by methylated sensitive enzymes but classified as non-methylated loci. Therefore, NML may also include some epigenetic information when they represent genetic variation, and the significantly different results of NML may be the reflection of epigenetic variation in another form.
Validity of the findings: In this paper, the number of MSL was dynamic at different time points. For example, in the temperature stress experiments, 586 of the 1157 loci were MSL at T0 while 613 loci were MSL at T1 (lines 235-240). In the R package msap, loci are classified into MSL and NML based on a threshold (the default is 0.05). Therefore, different datasets would result in different numbers of MSL and NML statistically. However, loci, which represent genetic variation or epigenetic variation, are their own in inherent characteristics. It doesn’t make sense that the same loci represent genetic variation (NML) at T0 but represent epigenetic variation (MSL) at T1. I recommend the mixing scoring approach (Schulz et al., 2013) to analyze MSAP data, which may be more suitable for this study.
Additional comments: In the study of Pu & Zhan 2017, several methylation differences have been associated with environmental differences in salinity and temperature (lines 312-315), but it cannot be stated that the temperature- and salinity-related methylation modifications are very small in the genome as it is a locus-specific but not genome-wide level 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: EFFECTS OF TEMPERATURE AND SALINITY STRESS ON DNA METHYLATION IN A HIGHLY INVASIVE MARINE INVERTEBRATE, THE COLONIAL ASCIDIAN DIDEMNUM VEXILLUM
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors have addressed all my concerns that I raised during the first round of review. Thus, I suggest "acceptance" for publication in PeerJ.
Experimental design: no comment
Validity of the findings: no comment
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: DISENTANGLING THE LINK BETWEEN SUPPLEMENTAL FEEDING, POPULATION DENSITY, AND THE PREVALENCE OF PATHOGENS IN URBAN STRAY CATS
Review round: 1
Reviewer: 1

Output:
Basic reporting: I have enjoyed reviewing this paper as submitted to PeerJ. It is well written and has a very interesting hypothesis that was tested using a combination of field data collection, and biological sampling of free-roaming cats. My comments and suggestions are focused on improving the clarity of the paper and on adding additional context for some specific sections of the text. The paper in its current format meets the PeerJ requirements regarding Basic reporting.

In general the flow and clarity could be improved by paying particular attention to sentence length. Many sentences are very long and although they are clear in terms of language the writing could be improved by breaking these into shorter sentences. E.g. line 88-92 1 sentence, 5 lines, line 77-82, 1 sentence, 6 lines

The authors switch between using the following terms, density, crowding, and concentration in the Introduction. These terms appear to be used as substitutes for one another however, I would recommend that it would be more accurate to identify a single, well defined definition and then use that in the text. For instance, different individuals or host-pathogen systems may define crowding in different ways and in the use here, it is less clear what exactly is intended.

The paragraph that begins at line 86 – this section which speaks to the differences between density-dependent and frequency dependent transmission would really benefit from a paragraph that could come before this to introduce more generally the fundamental and theoretical framework regarding these 2 “types” of pathogen transmission dynamics. The paragraph starting at line 86 provides some excellent examples but a more general lead in would add more context and improve the clarity.

Line 96 – here you seem to be saying that contact rates among host individuals are not an important component of frequency dependent transmission. I would argue the opposite, that in fact it is contact rates (sometimes artificially inflated by behaviour) that create the enhanced opportunities for disease transmission in this case.

Line 126-129 – this sentence implies that these species are perhaps endangered. Is there a specific designation that should be mentioned regarding this species? I would also expand upon the specifics regarding why free-roaming cat contact could have important consequences for these populations? Death due to pathogens? If this is the case, then it might be wise to pull in some of the literature here regarding the way in which different “modes” of pathogen transmission might influence species persistence vs. extinction. If food provisioning causes aggregation that increases the risk of transmission via frequency-dependent contacts than pathogen -mediated extinction would be a real possibility (but it is not entirely clear if this is where you were going with this sentence).

Line 140 – Just a note that density-dependent transmission does not exclusively mean direct contact transmission. Sexual transmission is also direct contact transmission. The difference is that behaviorally, even if hosts are rare, individuals will seek out sexual contacts over wider ranges which means that transmission occurs independent of density. In this case, transmission is driven by “frequency of infected contacts”, which means prevalence of the infection. If prevalence amongst contacts is high then you have more transmission.  I have always thought that it would be clearer to use density-dependent and density- independent transmission as the terminology but so far no one seems to have taken up this idea 

Line 148 – the environmental reservoir bit here overrides the direct transmission hypotheses. I would perhaps elaborate on why this is assumed to be positively associated with population density (e.g. is it really shedding into the environment creating a point source exposure?)

I think it would be very helpful to have a summary table of the different pathogens that were the focus of the seroprevelance data with a column for the “mode of transmission” and then some other summary measures. I find it very difficult to read through the text with all of the FCV/FHV/FeLV in the results section and try to keep straight which pathogen is which, which one is transmitted in which way, and how this is tied to your hypothesis about density dependent and density independent transmission. Not a requirement but I do think it might be helpful.
Experimental design: The experimental design meets the requirements of the PeerJ review policy.

Line 176 – the sample size is missing here. N=0000
Line 187 – 190 – this seems to be a result (Table 1) of the PCA rather than a method.
Line 197 – Need to define SP here. This also comes a bit out of the blue. If this was one of the top four than it should be listed alongside the other three and then the justification re: exclusion is clearer, and the reader then sees that you are only using 3 of the top 4 high CCA sites.
Figure 2 – I am not sure of the PeerJ protocol for referencing this sort of figure so will leave it up to the editor to identify if this is appropriate.
Line 217 – change this sentence to say, “For logistical reasons…
Line 224- change this sentence to say “..used for the density survey consisted…(remove the word is)
Lines 250-251 – this is just a thought but I find it difficult to remember which of the site abbreviations is associated with each of the CCA levels. Might it be reasonable for clarity to label the sites as high-site 1, high-site 2, low-site 1, low-site 2 etc. or something similar throughout the text which would make it easier to keep track as the reader moves through the paper? You have done this in the Tables/Figures, but the text would benefit from a similar approach.
Line 266 – I think this must be a typo but this sentence seems to say that all of the cats were determined to be too young for sterilization and therefore were released. I don’t think that is actually what you mean.
Line 294 – The Chong et al. reference here is duplicated
Line 309 -  Just to be clear, capture-recapture was done just based on a visual survey that was handwritten on a data form? I am curious why you did not use other techniques for resighting cats such as by using photos etc. I think that something that is missing in your Conclusion is some discussion of your study limitations in regard to the methodology.
Line 347 – I am a bit unclear how CCA is an explanatory variable for sterilization rates. If this is the case, then it should be more clearly discussed in the intro if there is some known association between these two things.
Validity of the findings: The model findings are valid and interesting. I would suggest the inclusion of a section that speaks to the study limitations as that is not currently specifically included.

Line 391-412 - While I recognize that the results are in the Tables, it would be helpful in the results section where you are talking about the “best” models to perhaps indicate something about the “best” interpretation but putting the AIC in brackets or some measure to help the reader follow along.

Lines 422 –437 – I think this is a reasonable interpretation of the findings which are counterintuitive. I also wonder if it might be the case, that high CCA sites just have lots more people feeding so the cats are more dispersed among the feeding sites making their density less on the whole? Whereas in low CCA sites, because there are few people feeding the cats they congregate more into smaller areas.

Line 551 – I think here that it is more appropriate to state that your findings did not support your original hypothesis.
Additional comments: Line 86 – replace with, “…interactions as a result of host population density..
Line 78 – replace with, “…crowding of host individuals has been…”
Line 89 – replace with, “…likely to be facilitated as host population density increases, as with Brucella…”
Line 90 – replace with, “..success of the pathogens transmission…”
Line 113 –replace with, “…centered around free-roaming cats…”
Line 180 – replace with, “ …in a regular manner..”
Line 336 – replace with, “…50 meters was…”
Line 344 – replace with, “…report..”
Line 365 – remove, “and respectively”
Line 371 – replace with, “…compared…”
Line 400 – replace with, “…showing …”
Nowhere is there any discussion of the sample size related to the blood samples collected. I am wondering if it is possible that some of the results might be a function of just having a small number of convenience blood samples rather than a more targeted sampling protocol that was linked to supplemental feeding sites specifically. I am aware of how difficult that would be but it is worth at least some discussion of the sample size in light of the findings.
Figure 1 – I would tend to label the points in black text rather than red. In the figure caption I would also speak to the point that one of the high CCA sites was excluded.
Figure 3 – I am not sure about the rationale for the order of the x-axis on the figure, but I think it would be easier to compare if all of the sites e.g. DDM1 and DDM2 were side by side. This is true for only some of the sites on the figure.
Table 2 – Need a space between CI and cats in the column header.
Table 4- Again, I would find it helpful to have the abbreviations spelled out here either as a footer, in the body of the table or in the Table heading.


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: DISENTANGLING THE LINK BETWEEN SUPPLEMENTAL FEEDING, POPULATION DENSITY, AND THE PREVALENCE OF PATHOGENS IN URBAN STRAY CATS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The raw data file does not appear to be complete. There is no description of what the variable titles mean (eg. pd), nor is there any code provided for analyses. Data on variables included in this study, including any data concerning pathogen abundance, have not been provided.

It seems to me that the hypothesis of this study is that supplemental feeding leads to increased population density due to the increase of a resource (food) that would otherwise be limiting their populations, and that this has consequences for disease transmission. From this, the authors predict that increased food availability (in high CCA areas) will show increased population density, and also increased transmission of density-dependent pathogens (FCV, FeLV, and FHV-1). They also predict that frequency-dependently transmitted pathogens (FIV, feline hemoplasma, and B. henselae) will not be affected by differences in population density. The distinction between hypotheses and predictions are sometimes well distinguished (lines 422-423), but needs to be clarified in other areas (lines 33-36, 149).

If any special R packages were used in the analyses, please list and cite them.

There is an extensive description of why site SP was not included in the analysis as a high CCA site. However, there is no parallel description of why site GB was not included as a low CCA site. Please provide some information, since this site is highlighted in Figure 1.

This manuscript provides an impressive amount of data to the reader, and it is generally well summarized in tables and figures. There are a few places where additional data summaries would be helpful and I have included them in the line number listing below.

Line number and suggested corrections:
27: “feral or stray animals”
40-41: “Blood samples (n=302) were collected from stray cats by local animal hospitals…”
65: “..urban trash cans and pets fed outdoors)…”
69: “…to pathogen host community…”
113: “..around free-roaming cats, as the availability..”
131: “…pathogen prevalence are associated in urban stray cats…”
136: “…Toxoplasma gondii. Each of these pathogens has a different transmission mode, falling…”
174: “…the number of cat caretakers and the number of cats cared for per caretaker.”
176: What does (n=0000) refer to?
176: “…a 2016 nationwide cat-caretaker questionnaire (Kim et al. 2016)…”
183: I don’t understand the last part of this sentence (“in the total number of respondents from each district”). Is this another (the 7th?) question on the questionnaire?
217: “Due to logistical reasons…”
218: “…was conducted in the fall…”
220: When describing the transect lengths, please provide the mean and the range of the transects in the text.
223: From description in other parts of the manuscript, it is clear that each transect was walked 5 times. Please clarify the language in the Field Survey section to indicate that each transect was surveyed 5 times each (e.g. “ Each transect was surveyed 5 times, once per day for 5 days, within a 2 week period.”)
226: “…to thoroughly cover the blocks, as in methods used in previous studies…”
235: “…two meters of range, close enough to identify…”
336: The metric conversion of 0.3ha is 3000m2, which could be 55m x 55m or it could be 1m x 3000m. The justification for the buffer zone could be clarified a bit.
344: “We calculated the mean and standard deviation…”
361: Please list the average number of cats observed across sites in addition to the range.
382: “..of the pathogens: T. gondii, …”
409: “…and non-significant p-value…”
446: “…conditions where cats live socially.”
465: “…we observed a relatively high prevalence (12-42%),…”
500: “…districts may have enabled stray cats in the area…”
551: “..meet our initial assumption that population density would be lower…”
Experimental design: No comment.
Validity of the findings: The raw data file does not appear to be complete. There is no description of what the variable titles mean (eg. pd), nor is there any code provided for analyses. Data on variables included in this study, including any data concerning pathogen abundance, have not been provided.
Additional comments: This timely and important paper offers new insight into the current conversation on urban, free-roaming cats. This study assesses the prevalence of 8 pathogens in 6 districts across two urban environment types: high and low Cat Caretaker Activity. Taking place in a highly urban center, the authors have done an excellent job at describing methods and reporting the findings of pathogen prevalence, and have very well coordinated a study that combines aspects of wildlife ecology and pathobiology. The interpretation of the results is well-founded and provides an excellent jumping-off point for future studies on the impacts of (zoonotic) feline pathogen risk in urban environments. The hypotheses and predictions, although repeatedly described throughout (which is great), are a bit mixed up in terms of how they are identified. Additionally, there are some linguistic concerns, listed below, and some incomplete information provided. Pending these minor changes, I recommend this paper for publication.


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

Input:
Title: LOW RESOLUTION SCANS CAN PROVIDE A SUFFICIENTLY ACCURATE, COST- AND TIME-EFFECTIVE ALTERNATIVE TO HIGH RESOLUTION SCANS FOR 3D SHAPE ANALYSES
Review round: 1
Reviewer: 1

Output:
Basic reporting: The article meets all requirements in this category.
Experimental design: This paper examined 3D landmark data produced from models created using different scan modalities (3D surface scanning, μCT scanning). While similar studies have been previously completed, all used relatively large specimens. Marcy and colleagues pushed the lower size boundaries of these scanning technologies in using a small rodent (delicate mouse) with cranium around 20 mm in length. The methods are described in sufficient detail including supplementary files with the raw data and stat code.
Validity of the findings: The authors found that biological variation in the crania was largely captured by the two different scanning modalities, but that the surface scanner did seem to produce more error. They make several recommendations for mitigating error and for working with lower resolution data.

This is a very well-conducted study and makes a necessary contribution to the literature on this subject. With the advent of morphosource and other repositories for 3D scan data, researchers are increasingly creating combined datasets and understanding how these data can and cannot be combined into different analyses is essential.
Additional comments: I made a few very minor comments on the attached pdf. Supplementary file “peerj-25642-Bilateral_Landmarks” needs more information about what the columns of data mean – it is unclear. The remaining supplementary files are fine.

This is a well-written and well-designed study! I look forward to seeing it in print.


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: LOW RESOLUTION SCANS CAN PROVIDE A SUFFICIENTLY ACCURATE, COST- AND TIME-EFFECTIVE ALTERNATIVE TO HIGH RESOLUTION SCANS FOR 3D SHAPE ANALYSES
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript is well written, the English being clear and professional. While most of the text is unambiguous two specific sections should be improved to ensure that a non-specialised audience can clearly understand what the authors are trying to explain. The sections where the writing could be improved include lines 147-149 and 306-307. In the first one, I understand that each specimen was scanned three times with each device, which gives a total sample of 114 three-dimensional models (not 114 replicates); however the sentence is somewhat ambiguous and complicated. Please, rephrase it in a more direct way. The sentence written in lines 306 and 307 is imprecise. I agree with the authors that the fact that the asymmetric variation is not significantly greater than the measurement error (ME) does not imply that symmetric variation is not (because asymmetric variation is usually smaller than symmetric variation). And therefore the fact that asymmetric variation is not significantly greater than the ME does not invalidate the use of the technique for the comparison of the symmetric component of shape. However, removing asymmetric variation does not allow investigating shape variation more confidently as state the authors. First of all, asymmetric variation is not strictly removed, but separated and analysed separately from the symmetric one. And second, comparing the ME with the symmetric or with the asymmetric component answers two different questions. The current phrase let the reader understand that analysing symmetric variation alone is “better” that including asymmetric variation. In fact, the more informative option is to include both components of form. However, because of the design of the Procrustes ANOVA, when the asymmetric variation is included the test compares asymmetric variation, but not symmetric, with measurement error.
The Introduction is very useful to put the reader into context and the literature is relevant and well referenced. However, while the main goal is clear, the specific objectives to accomplish it are not indicated in the text. In this part of the text, the authors reference the Figure 2, where the specific analyses and questions are highlighted. Indicating the specific objectives in the text will aid the reader to fully understand the aims of the authors.
Structure conforms to PeerJ standards. Figures are relevant, high quality and well labelled and described. Tables are also relevant but he number of decimals and the type of notation (scientific or decimal) should be standardized within and among tables.
Raw data and scripts are supplied which allow to replicate the study.
Experimental design: The study represents an original primary research within the scope of the journal. The research question is well defined and relevant. In this sense I found Figure 2 very informative and useful (but see comment in the above section regarding specific objectives). The research is an interesting contribution to the field of 3D modelling applied to geometric morphometrics. It adds information about the use of non-expensive methodologies, in particular low resolution 3D scanning, to obtain 3D models for the analysis of biological form. The investigation is rigorous and performed to high technical standards (but see General comments 1 and 2). The experimental design is appropriate to answer the questions formulated by the authors. Methods are described with enough detail and information (including raw data and R scripts), which would allow replicating the study in the future.
Validity of the findings: Data is robust and analyses are, in general, statistically sound (but see General comments 1, 3, and 4). Conclusions are very general and not linked in a one-to-one manner to research questions and supporting results. More precise Conclusions directly linked to research questions should be provided.
Additional comments: 1.	I have several doubts and comments about the last section of the Results (Analyses with a biological example: sexual dimorphism). In Table 4 variation due to sex is obtained together with residual variation. Sex should be analysed as a separate factor in the Procrustes ANOVA in order to test if differences between sexes exist. If differences between sexes are not significant, the cross-validation analysis is not justified and the whole section loses its usefulness, and should be removed from the manuscript. In order to compare the two methodologies in detecting a source of variation, it seems reasonable to assess the effect of a significant biological factor. In this sense, the PCA and the cross-validation analyses suggest that sex differences are at most very subtle. Moreover, the sample size is not the most appropriate to detect subtle differences between groups.
2.	Another important point is the use of the term “interspecific” in the title. The title suggests that the utility of low resolution scans for interspecific comparisons have been tested, and this has not been done. I would change the title.
3.	In lines 221-224 the authors state that “digitization error is large compared to components of asymmetric variation, even a single device…”. This sentence, which is based in the general ANOVA, is somewhat confusing because seems to suggest that both devices are equally affected by error. However, how digitization error affects the analysis of asymmetric variation in each method has not been assessed. In order to assess how digitization error affects each methodology, ANOVAs including the factor side should be performed separately for Micro-CT and 3D scans.
4.	In lines 278-280 the authors say that “This means operators have an easier time repeating their digitisations (i.e. landmark placements) with Micro-CT than with 3D”. However, three types of landmarks have been used in the study: “true” landmarks, semi-landmarks, and patch points. It seems that the operator have played a different role in placing each type of landmark. While “true” landmarks have been placed manually, semi-landmarks have been recorded semi-automate, and patch points fully automate. How this differences affect ME in each methodology have not been assessed. It would be interesting to assess if some type of landmark is more affected by device error or observer error than other types. Performing separate ANOVAs for each type of landmark and method will answer these questions.
5.	In lines 251-252 the authors say that “3D scans score higher than their Micro-CT scan replicates on both PC1 and PC2”. Please, confirm this. I see the •D scan points more left (negative) and below (negative) than Micro-CT points.
6.	In line 260 the authors say “On the PC3 axis, Micro-CT scan replicates consistently score higher”. Again, please, confirm this. I see a lot of the Micro-CT points below 3D scan points.
7.	Move lines 249-251 to Discussion.
8.	Move lines 262-267 to Discussion.
9.	Lines 120-121: change (Pseudomys delicatulus, J Gould, 1842) by Pseudomys delicatulus (Gould, 1842).
10.	Line 204: change (Fig. 2c) by (Fig. 2d).
11.	Line 215: change (fluctuating and directional) by (directional and fluctuating).
12.	Line 251: which Table is Table TK?


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: LOW RESOLUTION SCANS CAN PROVIDE A SUFFICIENTLY ACCURATE, COST- AND TIME-EFFECTIVE ALTERNATIVE TO HIGH RESOLUTION SCANS FOR 3D SHAPE ANALYSES
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors have rephrased properly the parts of the manuscript that were somewhat ambiguous and have clearly defined the objectives of the work.
Experimental design: No additional comments.
Validity of the findings: In the new version of the manuscript the conclusions are clearer and more directly linked to research questions than in the previous version.
Additional comments: The authors have dealt satisfactorily with all the comments that I made in the previous version of the manuscript, adding additional analyses when necessary. Consequently, I consider that the manuscript is suitable for publication in PeerJ after some minor changes. Please, see comments below.

   1.	The reference list should be revised carefully. Several errors have been detected, of which some are
        listed below (the list is not exhaustive):
              •	The reference of Muñoz-Muñoz et al. (2016) has been entered twice. Remove the second one
                (lines 577-579).
              •	Change “Munoz-Munoz” by “Muñoz-Muñoz” in lines 81, 107 and 574
              •	Change “Perpinan” by “Perpiñán” in lines 107 and 574
              •	The reference of Yezerinac et al. (1992) is all written in capital letters (lines 625-627). Please
                correct it.
              •	Line 608, italicise “Ursus spelaeus”.
   2.	Lines 248-250 would be better placed in the Discussion.


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: A MIOCENE PYGMY RIGHT WHALE FOSSIL FROM AUSTRALIA
Review round: 1
Reviewer: 1

Output:
Basic reporting: See the attached file.
Experimental design: See the attached file.
Validity of the findings: See the attached file.
Additional comments: See the attached file.


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: A MIOCENE PYGMY RIGHT WHALE FOSSIL FROM AUSTRALIA
Review round: 1
Reviewer: 2

Output:
Basic reporting: See general comment below.
Experimental design: See general comment below.
Validity of the findings: See general comment below.
Additional comments: I am glad to see this manuscript and was very pleased to be able to review it. This work will be of high interest to other cetacean paleontologist and neontologist. The discovery of additional specimens referable to Caperea and its relatives continue to add to the poorly known evolutionary history of this enigmatic mysticete. The specimen described here is an important addition not only to further understand the history of this group, but also highlights the richness and potential of the marine mammal assemblage at Beaumaris. The description of the specimen is very thorough and concise. All the relevant literature is cited carefully and discussed where appropriate. The results and comparisons are well done and summarized as is the discussion and relevance of the discovery.

The manuscript is well written and the figures are of very high quality and informative. I specially appreciate the authors adding a side-by-side Figure comparing NMV P233333 with Caperea marginata. I do have some comments that are outlined in detail below and that I hope the authors take into consideration.

General comments:

1)	Line 19: here and in several other instances the authors use “Late Miocene”, however being that late is not an internationally recognized division of the Miocene, I suggest they change to “late Miocene”.
2)	Along those same lines, I suggest the authors also use “Messinian” as it is the recognized stage of the late Miocene relevant to the specimen they describe. e.g. line 88, change “… latest Miocene in age,…” to “… latest Miocene (Messinian) in age,…”
3)	Although it doesn’t seem to be required by the journal, I suggest the authors add the taxonomic authority (and reference) at the first use of a taxonomic name.
4)	Lines 35-36, mention the age of the fossils from Argentina and Australia.
5)	Line 110:  “aligned with the proximal portion of the facial canal” – please label facial canal in Figure 2C
6)	Line 111: “The crista transversa” – please label in Figure 2C
7)	Figures: If possible, I suggest the authors adding a side-by-side figure of NMV P233333 with Caperea marginata in dorsal view, even if they do as supplementary figure.


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: A MIOCENE PYGMY RIGHT WHALE FOSSIL FROM AUSTRALIA
Review round: 1
Reviewer: 3

Output:
Basic reporting: The structure and language in this article is impeccable as usual; most data is contained within the main text of the manuscript. I have a few additional suggested references, and I suggest that the authors consider making the CT data and/or STL files available as SI.
Experimental design: The methods involved in the study are appropriate and adequately described in the text.
Validity of the findings: The authors have adequately substantiated their identification of the specimen.
Additional comments: The manuscript by Marx et al. is a short and sweet addition to the rapidly expanding body of literature on fossil baleen whales, reporting a partial periotic of a pygmy right whale from the uppermost Miocene locality of Beaumaris in Australia. Another specimen of a neobalaenine (or neobalaenid as most still prefer) was identified in an earlier study by Fitzgerald (2012) which was an isolated but highly distinctive cone-shaped composite posterior process of the petrosal and bulla. This specimen was identifiable only to the Neobalaeninae/Neobalaenidae. This new specimen preserves the body of the petrosal and the pars cochlearis, which is more diagnostic and thus the specimen is identifiable at the genus level - specifically owing to the very narrow constriction at the base of the anterior process (but see below). I have only a few moderate and a few additional minor comments, which I think the authors can easily address. Overall it is a fine piece of work and I heartily recommend acceptance after minor revision.

Kind regards, Robert W. Boessenecker, Ph.D.

Moderate: Given the high degree of abrasion and polishing of the specimen,  how confident can the authors be in their interpretation of the three features identifying this specimen as Caperea (open facial canal, short posterior cochlear crest, small neck of anterior process)?

Provided the authors can address the above concern, an additional selling point is the fact that now two neobalaenine genera appear to have been present during the late Miocene, pulling the Caprea/Miocaperea split further back and precluding a simple ancestor/descendant relationship between Miocaperea and extant Caperea.

Additionally: I request that the authors comment on the identification of the earlier specimen reported by Fitzgerald (2012). Could it represent Caperea? Do you think it should be tentatively referred to Caperea sp. now that a more diagnostic specimen is known? I understand that if identifiable only to the subfamilial level it leaves open the possibility that two neobalaenines were preserved at Beaumaris, but according to present evidence parsimony would suggest that only one was present in the assemblage.

Minor comments:

Line 30: A citation to Boessenecker and Fordyce 2015 (Tokarahia: ZJLS) is highly relevant as it includes the largest morphological character matrix ever attempted for mysticetes and recovered a monophyletic Balaenoidea.

Line 36: suggest  'uncertainly identified past the level of Neobalaeninae"

Line 52: focus stacked

Line 109: What is the dorsal vestibular area? Please clarify.

Line 119: Please provide some examples. Is this the same feature preserved in some balaenids and certain species of "Kellogg's cetotheres" like Dioroctus/Aglaocetus? If so, there was a character state for one of Boessenecker & Fordyce's characters, though I cannot recall the exact number.

Line 122: shelf like process - this feature is not labeled. Please clarify.


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: A MIOCENE PYGMY RIGHT WHALE FOSSIL FROM AUSTRALIA
Review round: 2
Reviewer: 1

Output:
Basic reporting: Satisfactory.
Experimental design: Satisfactory.
Validity of the findings: Satisfactory.
Additional comments: This paper is more or less ready to go – just two more additional notes.

1. Measurements
There is indeed no standard set of periotic measurements.  But, descriptions of new baleen whales with well-preserved periotics generally provided a wide range of measurements, for example, Boessenecker and Fordyce 2015 PeerJ: table 2, or Tsai and Fordyce 2015 Journal of Mammalian Evolution: table 2, which some measurements could be applied to NMV P233333 and then should give readers a better idea for visualizing the specimen.

2. CT data/STL files
Alternatively, if possible, it would be extremely helpful to provide the CT data or STL files in the Supplementary Information, which should allow readers and other researchers to calculate any measurements they desire and facilitate further comparative work, as Reviewer 3 also suggested.

Regards
Tsai


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: A MIOCENE PYGMY RIGHT WHALE FOSSIL FROM AUSTRALIA
Review round: 2
Reviewer: 2

Output:
Basic reporting: See general comments below.
Experimental design: See general comments below.
Validity of the findings: See general comments below.
Additional comments: The authors have addressed most of my earlier comments and have explained in detail when they disagreed. The finding reported in this manuscript are a valuable addition to our knowledge of the evolutionary history of cetaceans, specially neobalaenines. The figures and illustrations are excellent and very informative. I commend the authors on a well written manuscript and I am looking forward to seeing this work published.


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

Input:
Title: VERTICAL STRATIFICATION OF PLANT–POLLINATOR INTERACTIONS IN A TEMPERATE GRASSLAND
Review round: 1
Reviewer: 1

Output:
Basic reporting: Overall the manuscript is presented clearly and unambiguously.  However, see my comments on the experimental design and validity of findings sections below.

Some of the panels in a few figures could be removed as they contribute little to the findings of this study (e.g. Figure 2, panels F and G).
Experimental design: The design of this study was well thought out, but some additional information is required that could influence the interpretation of results.  Also, I have a few concerns with some aspects of the design.

Given the diverse visiting fauna observed, it is required that the time of day that these observations were made are reported. The behavior of these taxa can change over the course of the day.  For example, many Hoverflies are known to switch from foraging for nectar to pollen around midday. The difference in behavior of nectar vs. pollen foraging can influence flower handling time, and therefore rates of seed set.

In the second experiment, one ramet was bent (lines 126 to 129) close to the ground to produce a “short inflorescence.”  How did the orientation of the inflorescences change? Did they now appear more horizontal, and therefore change how pollinators would encounter them? I feel the description of this manipulation should be clarified.

Also, the seed counts from the second experiment may have been confounded by inbreeding.  Since three inflorescences per genet were manipulated, pollinator movement between ramets of the same genet would result in geitonogamy, and likely result in reduced seed production. An alternative approach would be to retain a single ramet of desired height from each genet (e.g. cut the remaining ramets) until a desired distribution of single-ramet genets are achieved.

The sentence starting on line 161 states that fitness values were assigned to individual ramets.  Fitness is an individual (e.g. genet) level trait, and cannot be assigned to repeated modules on a single individual.  Perhaps the authors should revise this to “ramet reproductive performance.” Therefore selection gradients cannot be calculated for individual ramets.
Validity of the findings: Inflorescence height is just one perceivable trait pollinators use as cues.  This study, while undertaking an important and worthwhile question, confounds many of these (e.g. flower size, floral reward availability) cues, but attributes all observed patterns to inflorescence height.  Overall, I feel that the wording and interpretation of the findings should be more conservative.  For example:

Lines 240 – 241 (and following paragrapsh): I appreciate that the authors whish to place their findings in a broad context, but their finding that certain bee species typically visit certain inflorescence heights does not automatically translate to a taxonomic segregation within inflorescences.  What about the movement of insects once within an inflorescence?  Many bees typically display an upwards pattern of flower movement within inflorescences, that would alter floral reward characteristics of the entire inflorescences and therefore influence the visitation patterns of subsequently visiting insects.

I also disagree with the sentence ending on line 298.  Many factors influence plant fitness besides inflorescence height.  Several studies have shown a large influence of resource availability and even genet age (related to resource accumulation in perennials) that strongly influence inflorescence height.  While other studies have found increased visitation rates on taller inflorescences, pollinator-mediated selection is not the only influencing factor.

Lines 299 – 314: see my previous comment on why fitness, and therefore selection, cannot be ascribed/estimated on individual ramets, bur rather, is a trait associated with an individual organism.
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: VERTICAL STRATIFICATION OF PLANT–POLLINATOR INTERACTIONS IN A TEMPERATE GRASSLAND
Review round: 1
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: This paper provides results of a lovely, balanced experiment manipulating inflorescence height, and relating the treatment to insect visitation (for 2 plant species) and seed set (for 1 plant species). The writing is clear, analyses appropriate, and discussion + literature cited great.

I have 3 general concerns, and a couple of minor ones:

The introduction seems a bit misplaced. It does a great job introducing the adaptive significance of plant height for plants. But it makes a convincing case that plant height also has consequences for pollinator visitation, such that a pollinator perspective is needed, too. But this issue (the pollinator's perspective) is NOT introduced. Presumably, pollinators “care” about rewards (nectar and pollen) and strategies to optimize their foraging gain, based on distance-sensitive foraging costs, and search/sampling costs. None of this is mentioned. It's odd to have a paper that focuses on pollinators pay so little attention to what might explain their behavior. This introduction needs some serious revision, to introduce a pollinator perspective.

The statistics are generally clear, but the conclusions from them often do not follow:
Line 174: “The difference in the shape of the relationship between total visitation and inﬂorescence height…”. No elements of shape are tested here. What differences the shape?  Its height? Its slope? The location of its maximum? We need a more particular test than simply examining the interaction between surrounding veg height * inflorescence height, which should precede such a statement, but needs further qualification.
Line 190: “Inula salicina had a lower visitation rate than Centaurea scabiosa”.  This not supported, as no presented model contained a Species term”.
Line 198: “Inﬂorescences of both species experienced visitation by a very different community of potential pollinators depending on the height of the inﬂorescence and the height of the surrounding vegetation because different ﬂower visitors responded to both factors in a species-speciﬁc way “. There is no presented test of the significance of an interaction between species and surrounding vegetation height, and therefore no support for this statement.

There also seems to be a missing analysis in Experiment 2. We see measurements of insect visitation, and measurements of seed set, but the two are never related in a statistical model. This seems to be an oversight. I tried this quickly with data sets 3 and 4: calculating sums of treatment seeds produced, and sums of visitors and visits. I fit the model sumseeds ~ totalflowers (a nuisance variable) + InfloresenceHeight:sumflowersvisited, I get a significant positive term for sumflowersvisited, but no effect of height. A virtually identical result obtains from using sumvisitors in place of sumflowersvisited.  So while there is strong support for the idea that visitation promotes seed set, there is none for the idea that, independently, height promotes seed set. This conclusion promotes a stronger, more nuanced conclusion: height promotes greater seed set by greater visitation, but height itself has no effect on seed set. Switching to a different model, where Y was sum#ofFlowerswithseeds, the result was similar for sumvisitors, but different for sumflowersvisited (in this latter case, all that mattered were how many flowers were presented). All of this, of course, ignores bee taxonomy.

More minor concerns

Line 129: This experiment is excellent, but more complicated than suggested here. While the only difference between the 3 treatments (positioning inflorescences on a single plant at low, moderate, and high levels) was inflorescence height, this treatment has man y consequences for seed set that are unrelated to bee visitation. First, water transport, and the difficulty of moving it vertically, is a major constraint on plant architecture. Moving water sideways (low inflorescence) is much easier. Second, low inflorescences means shading of their associated photosynthetic structures, and therefore lower rate of local carbon fixation, which should matter when reproductive allocations are made locally. I suggest at least recognizing these complications.

Line 61: Given that high heritability generally implies a weak relationship with fitness (e.g. Price & Schluter 1991), high heritability of plant height suggests the evolutionary non-importance of plant height. Providing a high measure of heritability in the introduction therefore suggests a problem not worthy of 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: VERTICAL STRATIFICATION OF PLANT–POLLINATOR INTERACTIONS IN A TEMPERATE GRASSLAND
Review round: 1
Reviewer: 3

Output:
Basic reporting: Overall, I really enjoyed reading this manuscript. It was well written, the experiments were carefully thought out, and the methods and results were clear and descriptive. I think this paper obviously deserves to be published. My comments below mainly refer to how the paper is framed, not any fundamental flaws.

I do have a few concerns, which are largely in the framing of the paper. It seems to me the theory or background focus of the paper clashes with what the experiment was designed to show. The introduction emphasizes the potential evolutionary implications, but these experiments weren’t really designed to show selection effects (in my opinion). Showing that pollinator preference is driving selection in flower height would require a lot more complexity. As it is, inflorescence height is a plastic trait that changes depending on environmental conditions, likely including the height of surrounding vegetation. This context makes the ultimate effect of pollinator preference much more complex. So saying that you’ve shown “pollinator-mediated selection on inflorescence height” seems to be a stretch to me, given your results.

The last sentence of the abstract seems odd to me as well: even if you show that pollinators are driving inflorescence height, how would that correspond to selection in pollinators? Coevolution requires selection acting simultaneously on both interacting parties.

In this sense, referring to the differing pollinator communities in tropical canopies is also misleading because (as far as I understand) that refers to plants that grow to different heights and have adaptations to different light levels, not the same species that can grow to different heights.

Similarly, some of the conceptual framing seemed misleading to me. For example, the paper mentions in a couple of places that flower visitors “prefer to fly at a certain height” (e.g. lines 39-40), but this experiment doesn’t necessarily show that. It just shows that they prefer to visit flowers at particular heights. Your own study shows that the height at which they visit flowers is context-dependent and not an inherent preference and also that different pollinator groups have different preferences, and are therefore not driving selection for taller flowers (necessarily). Indeed, if you look at the visitation rates for Centaurea scabiosa (going purely on total visitation), there would be selection for an “optimal” height, relative to the surrounding vegetation. In both short and tall surrounding veg, the visitation decreases as the flowers get above 80 cm. (this might very well apply to Salvia above heights evaluated in the study, which were constrained by the maximum stretch of the plants)

I also feel like phenotypic plasticity deserves a description in the introduction, maybe to replace the emphasis on evolution.

Finally, as far as I can tell (I may have missed it), you do not reference the supplemental materials in the main text. It seems they should be cited as the other tables are cited, where relevant.
Experimental design: The only thing I was missing here was the number of bees collected and the number of species identified. It would also be nice just to have a total number of man-hours spent sampling/observing insects visiting flowers. It just gives the reader an idea of sampling effort and how much data are involved in the analysis.
Validity of the findings: No comment
Additional comments: In general, I feel like modifiers are overused in this ms. For example, "strongly" (8 uses in paper) "very" (7 uses) etc. are usually unnecessary.
The first sentence of the abstract is ambiguous.

Line 53: “There are” instead of “there is”
Line 245: “despite the fact that” instead of “despite that fact that”
Line 246: “Previous studies” instead of “previous studies”


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

Input:
Title: IS PUBLICATION BIAS PRESENT IN GASTROENTEROLOGICAL RESEARCH? AN ANALYSIS OF ABSTRACTS PRESENTED AT AN ANNUAL CONGRESS
Review round: 1
Reviewer: 1

Output:
Basic reporting: In this study, the authors employed a common technique for evaluating publication bias in a specialty, namely exploring the publication outcome of research abstracts in gastroenterology presented at Americas Hepato-Pancreato-Biliary Association Congresses.

The manuscript is very well written,  neatly organized and appropriately cited. However, given the  straightforward nature of the undertaken study, I found the Introduction to be a little lengthy. For example, the paragraph elaborating on what happens in scientific meetings might be condensed to just 1-2 sentences.

The authors seem to argue that  evidence-based evaluations of intervention effectiveness are entirely dependent on the results of analyses which aim to test a specific hypothesis, when (the standard flavor of) null hypothesis significance testing (NHST) in medical research is known to have key limitaitons, not the least of which is a general lack of consideration for treatment effect heterogeneity (both across patients and across providers), preferences, and other factors unrelated to outcome but nonetheless relevant to decision-making.

Please edit any statement about what was done in this study to reflect the past tense.

The Discussion section contains a) items which should be in the Results section; and b) repeated items from the Results section.
Experimental design: The search process for published reports seems comprehensive enough. However, it is safe to assume that some percentage of people contacted by e-mail will simply not respond to a request (regardless of what it is). Given that many authors change titles in their manuscript development (after presentation at a conference), or merge multiple conference abstracts into a single manuscript, the risk of missing publications is not ignorable here. I don't know if I have any good ideas of how to make the search procedure more sensitive, though.

In a similar vein, we should allow the possibility of, for lack of a better term, "methodological evolution", in which the results from the abstract "evolve" into something different due to changes in analytic methods, inclusion criteria, etc.

The description of the logistic regression analysis that was undertaken is vague. A more direct statement such as "Logistic regression was used to evaluate the associations of sample size and study type with publication." Further, were nonlinear relationships with sample size considered?  Power has a nonlinear relationship with sample size.  Finally, "study type" needs to be clearly defined in the Methods.
Validity of the findings: How did the authors handle the case where abstracts and/or publications may have reported "non-significant" or "NS" test results (without reporting exact P-values)?
Additional comments: That 86% of abstracts which reported a P-value reported statistically significant relationships is concerning. It suggests that the responsibility of "publication bias" lies with researchers and editors alike.


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: IS PUBLICATION BIAS PRESENT IN GASTROENTEROLOGICAL RESEARCH? AN ANALYSIS OF ABSTRACTS PRESENTED AT AN ANNUAL CONGRESS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript has been written in fluent language. Background of knowledge has been given in detail, yet it has made the introduction too long. There are some sentences that should be included and limited to materials & methods section.There are some minor errors in the text to be corrected before final acceptance (such as 'to to' or writing styles of some reference numbers)
Experimental design: Experimental desing has been well constructed and described throughout the methods section. As the authors stated in the discussion section, they have limited number of missed publications via their method of survey.
Validity of the findings: I have seen that prospective studies had higher publication rates than retrospective studies. Is there significance in that finding?
Additional comments: Thanks for delineating and emphasizing the bias present in publishing papers with null or negative results.


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: IS PUBLICATION BIAS PRESENT IN GASTROENTEROLOGICAL RESEARCH? AN ANALYSIS OF ABSTRACTS PRESENTED AT AN ANNUAL CONGRESS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors commented in their review but not in the manuscript about the shortcomings of using p-values to represent "significant" findings. This has implications to the very concept of "publication bias", and there should be a mention of this in the Discussion.
Experimental design: The authors should incorporate the limitation pointed out in my prior Comment 6 (about non-response to e-mail, changes in title, changes in study results between abstract presentation & publication) as well as within the manuscript. By the way, some of the changes between abstract presentation and final publication are completely appropriate (e.g., refinements to scientific methods in response to peer reviews).
Validity of the findings: The lack of counting "NS" or non-significant results from manuscripts that did not report the value of P-values greater than the chosen significance threshold is a limitation that needs to be reported in the manuscript. Omitting these publications results in a bias in the reported estimate of the incidence of significant results included in the studied publications.
Additional comments: The authors sufficiently responded to my comments, but some of their responses should be directly incorporated into the manuscript itself.


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: IS PUBLICATION BIAS PRESENT IN GASTROENTEROLOGICAL RESEARCH? AN ANALYSIS OF ABSTRACTS PRESENTED AT AN ANNUAL CONGRESS
Review round: 2
Reviewer: 2

Output:
Basic reporting: Mentioned before
Experimental design: Mentioned before
Validity of the findings: Mentioned before
Additional comments: In the conclusion section of the abstract, instead of “finding”, it should be “findings”
Readers should take these findings into consideration when reviewing medical literature.

In the statistiscal analysis msection of methodology, you have made revisions about logistic regression and i have been a little bit confused what was intented to mention in the text. Can u please clarify these sentences as simple as possible.

What do you mean with “negative results”? Is it a result of opposite of what had been expected or is it a non-significant result?

In the discussion section:
In our study, the most common study type (removed) design (added) was a retrospective study. Please omit “a” before “retrospective study”.
It has been stated that studies with positive results were more likely to be published earlier than studies with negative or null results. The actual time difference is only 1.5 month. Is is really clinically significantly important?

In the conclusion it has been said that “Abstracts with significant P values had a higher probability of reaching publication.” To say that this should have been put into the logistic regression model, yet it had not been done. So, please make change in logistic regression or change this sentence accordingly.


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: IS PUBLICATION BIAS PRESENT IN GASTROENTEROLOGICAL RESEARCH? AN ANALYSIS OF ABSTRACTS PRESENTED AT AN ANNUAL CONGRESS
Review round: 3
Reviewer: 1

Output:
Basic reporting: No further comments.
Experimental design: No further comments.
Validity of the findings: No further comments.
Additional comments: The authors have successfully addressed - and incorporated into the manuscript - the issues raised in my review.


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: IS PUBLICATION BIAS PRESENT IN GASTROENTEROLOGICAL RESEARCH? AN ANALYSIS OF ABSTRACTS PRESENTED AT AN ANNUAL CONGRESS
Review round: 3
Reviewer: 2

Output:
Basic reporting: N/A
Experimental design: N/A
Validity of the findings: N/A
Additional comments: All my recommendations have been well addressed by the authors. Thanks.


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: HIGH PREVALENCE OF LYNX RUFUS GAMMAHERPESVIRUS 1 IN WILD VERMONT BOBCATS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The article is well written, and well referenced.
Experimental design: The experimental design is straightforward and the cases sufficient for significance. For both wildlife health, and for a relatively new and unknown virus, I laud the authors for the large study group required for the importance of the results.
A few specific questions that relate to interpretation of the results:
1. The authors should address the choice of spleen. If it is serving as an ersatz for blood in this case then that needs to be justified (what is the correlation in other studies?). I can think of reasons why that would not be correlative, and couldn't find any data about the case for FcGHV.
2. There is no description of how spleens were collected or stored. The inclusion criteria for these wildlife samples should be added.
3. The "trend" for higher loads in younger animals has to be assessed in the context of sample choice and autolysis.
Validity of the findings: With the caveats stated above in experimental design, the study is useful and well organized.
Presence and prevalence are solid.
The significance of the genetic variants is still unclear (to me, as a lay reader) and should could be stated in the conclusions (unless I am simply missing the boat). Do you experts believe that the number of field samples of the variants clearly establishes criteria for significant strain variation? Is the jury still out on potential for viral evolution? This is one of the most interesting questions, I think, because if "species jumping" (if that can be defined) in cats is associated with viral impact or virulence, then these studies could be predictive of important species crowding problems and conservation issues.
Additional comments: Minor comments:

54: "....may result in pathology". Pathology is the study of disease, so rather GHV may result in disease, but not in "pathology".
71-74: "Serologic analysis determined that approximately half of domestic cats
that harbored FcaGHV1 specific antibodies did not have detectable DNA in circulation,suggesting that approximately 30% of cats across the US have been exposed to FcaGHV"  This is a non-sequitor unless I am missing the point?
82-84: Not sure that the statement "...this is the first attempt to document the presence of GHVs in wild or domestic cats in the Northeast United States" is necessary. The significance of the data stands on its own, and since your own previous studies made conclusions about the presence of the virus in wildlife and with widespread geographic presence...in my opinion this sentence dilutes rather than strengthens the impact of the study, which is clearly stated in the sentence before.


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: HIGH PREVALENCE OF LYNX RUFUS GAMMAHERPESVIRUS 1 IN WILD VERMONT BOBCATS
Review round: 1
Reviewer: 2

Output:
Basic reporting: see below
Experimental design: see below
Validity of the findings: see below
Additional comments: High prevalence of Lynx rufus gammaherpesvirus 1 in wild Vermont bobcats (#23555)

The manuscript is very well written. The content is novel, clear and well executed. The manuscript will be of interest to virologists, particularly those interested in gammaherpesviruses, as well as wildlife ecologists.
I have the following specific comments:
Line 35-36: Ultimately, the frequency and physiological locations of reactivation determine the clinical manifestation of herpesvirus infection (Speck & Ganem 2010).
Please reconsider the accuracy of this statement with regard to gammaherpesviruses. Upon infection of the host, GHVs usually enter latency immediately and most GHV disease is manifest during viral latency. Similarly lines 42-43,

line 20: “Intensity…..of infection” is used to refer to virus load. This terminology may be confusing because it is not commonly used in this context, in my experience. Similarly line 51, 78
Line 89: Re bobcat carcasses, a note of explanation to the reader as to their provenance would assist the international audience. Did these animals die of natural causes? Were they hunted? trapped? This information is important to understand how representative the sampled population is of the general population.
Line 97-98. Please comment and reference the accuracy of this method of aging. A caveat to the interpretation of results, as they relate to age might be considered.
Line 156 and throughout manuscript qRT-PCR should be replaced with qPCR. The latter is accepted to refer to real-time quantitative PCR. (The addition or RT is unnecessary and can suggest a reverse transcription step, which is not the case)
Lines 237-242. This information is interesting and informative. However, the limitations associated with analysis of such a short sequence should be acknowledged.
Lines 249-252 Fascinating concept.


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

Input:
Title: CITIES MAY SAVE SOME THREATENED SPECIES BUT NOT THEIR ECOLOGICAL FUNCTIONS
Review round: 1
Reviewer: 1

Output:
Basic reporting: This paper is clearly written and is a pleasure to read. While much of the relevant literature has been cited, I think the authors could provide more background to justify their methods and convince the reader of the robustness of their data.

Figure 2: On the map, would it be possible to indicate the different habitat types?
Experimental design: The research questions are well defined, and are certainly meaningful in the context of the conservation of these two parrot species. The paper addresses an interesting point that despite the conservation value of urban populations for the survival of threatened species, urban populations cannot protect against the loss of important ecological functions in the native habitats. While in general I find the story convincing, I find much of the data to be somewhat anecdotal as presented. The authors could do more to justify their choice of methods and to convince the reader of the validity of their findings by providing more detail of their methods, backed up with relevant literature.

It would be helpful to explain how the ad-hoc observational data of parrot/parakeet presence were included in the statistical analysis. The data from the roadside surveys clearly reflect that urban populations of the parakeet are larger than rural populations, but for the Amazons there is a relatively even distribution between the city and two tropical forest types. I am a bit surprised that the GLMM would have showed a significant effect of habitat given this data as presented in Table 1. I can see that the numbers skew towards higher populations in urban areas if the off-survey observational counts are included in the analysis, so it would be helpful to clarify if this data were or were not a part of this result.
Validity of the findings: While I understand at this point that it would be difficult to go back and collect more data, I do think that a more thorough reporting of the literature on the various methods used could help the reader to assess the strength of the data provided. For example, how confident are the authors that the numbers recorded on the roadside surveys represent an accurate estimate of actual population numbers? Could it be that urban parrots flock more and so higher numbers are observed? (This point could likely be addressed by reporting on the average number of individuals observed in a single observation event.) I imagine that parrots would be more easily detected in urban areas, can the data provided somehow account for that detectability? Perhaps including information on total habitat patch area would help to address this? Were all transect routes only surveyed once, or did the authors do repeat surveys to account for differences in detectability on different days? This seems like it would be particularly important for the forested habitats given that the chance of detecting parrots at a single site in a large forest are surely affected by chance in some ways. There may be some good methods for accounting for this which the authors should flesh out more fully in the methods.

The interview data provides an interesting context for this story and in general I believe the findings are true. But while I fully understand the difficulty of collecting data on illegal activities, more could be done to increase the validity of the data collected. At the very least, more information should be provided on the interview methods used, including types of questions asked and any way that they judged the validity of the answers being provided to them. Also, it is common to conduct pilot interviews in order to improve the interview design and perhaps the authors could comment on whether any pilot studies were conducted, or whether their interview technique changed over the course of the study. I want to emphasize here that I am not criticizing the use of the interview technique nor do I have any strong reason to doubt the data. I am primarily pointing out that there are many methods available to improve the validity of this type of data which the authors might consider. I would refer the authors to a recent paper which addresses some of these concerns and suggests methods for increasing confidence in this type of data: Young et al. 2018. A methodological guide to using and reporting on interviews in conservation science research. Methods in Ecology and Evolution 9:10-19.

Seed dispersal was estimated in part by searching below trees in which parrots were perched to identify dispersed fruits and seeds. Please elaborate on how you were able to determine which seeds were dispersed by the parrots rather than consumed and dropped from that tree, or dropped by other animals/naturally. Did you observe seeds being dropped by parrots? If not, how could you differentiate between a seed dropped by a parrot, or consumed by another species once the fruit had fallen to the ground? Also regarding the seed dispersal, is there any data at all on what they eat in the wild? Are there native species in the forest habitats where the parrots occur that they would be treating in the same way as the urban species? I believe that some data on foraging in natural areas was collected, it would be good to report that here even if the sample sizes are low.

The discussion is very long and could be shortened considerably.
Additional comments: Overall I enjoyed reading this paper which is well written and contains an interesting set of data. I think the paper addresses an interesting and valid concern about the focus on the conservation value of urban populations by cautioning us not to forget about the loss of ecological function if these species no longer occur in their natural populations. While in general I find the story convincing based on the evidence provided, I find that much of the data are fairly anecdotal and more could be done to increase the robustness of the results. At least there could be more discussion to address the potential weaknesses in the data provided. Likewise, I would suggest tempering some of the stated conclusions based on the strength of the data.

Line 98 – replace “assumptions” with “hypotheses”

Line 119 and 327 – Find a more suitable reference than Wikipedia!

Line 225 – change previous to “prior”

Line 245 – not clear how pigeons come into this, more explanation here would be useful.