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: SHIFTING CULTIVATION AND HUNTING ACROSS THE SAVANNA-FOREST MOSAIC IN THE GRAN SABANA, VENEZUELA: FACING CHANGES
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript provides novel insights about the relationship between wildlife and human activities at the Northern amazon based on the Garden hunting hypothesis, despite some caveats (see above), especially in methods sections. A main contribution of the manuscript is a potential baseline to current threats as authors pointed out. In my opinion, it is a valuable contribution for PeerJ. However, it needs some improvement to be considered for publication. With these issues conveniently addressed in a new version, I think that it would be an exciting contribution to this interesting topic for ecology and conservation.
Experimental design: Although authors provide information about the study design, some gaps need to be resolved. For example, how authors assessed the effect of natural heterogeneity of the matrix forest-savanna vs. conocos in modeling? It appears to be considered in the buffer area (1 km). Still, because of the potential effects of the scale, it would be useful to understand what the reasoning was to use 1 km.  So, a potential effect of scale needs to be assessed (or provide support to this scale).  In some cases, specie-specific effects are scale-dependent. How many camera traps in forest? Savanna? Conucos?

Moreover, the matrix of the study area contrast with the lowland Amazon (Savanna is absent in the Amazon forest), so that this issue needs to be considered in discussions.

Authors omitted a goodness-of-fit (GoF), which is a common recommendation to check the fit of the models (including c-hat). Another option is a plot of residuals (See Kery et al. 2016, Mackenzie et al. 2018, MacKenzie and Bailey, 2004). In fact, due to the low number of detections (for several species) overdispersion need to be assessed by each model. Kery et al. 2016 provide some recommendations to deal with this issue.

They need to include this, in addition to AICc. Indeed, based on the number of detections authors need to use AICc, which is recommended for small samples (Burnham and Anderson, 2002). I suspect that they used ∆AICc < 2, according to Burnham & Anderson et al. (2002). Still, this issue is missing in the manuscript and should be included. It is a standard protocol for modeling.

Why blocks are not considered in modeling? It is possible to assess each block as a potential covariate for detectability. Figure 1 suggests that authors need to include each block as a potential covariate (as a factor) at least for detectability because each block has a different landscape configuration in terms of both forest and savanna. I suggest using Royle-Nichols models, which is recommend to camera trap data (see Tobler et al. 2009, Tobler et al. 2015) because of a relationship between abundance and detectability.  For example, in the abstract and discussion authors pointed out the importance of forest cover on mammal diversity; however, they did not include savanna, which is the other primary vegetation type throughout the study area. In fact, authors highlight the importance of savannah for some species (e.g. white-tailed deer)

How many models were included in detection and occupancy by each species? As a common rule, detection models are assessed first. Then occupancy models (Kery et al. 2016) Make it clear for the readers.

There is an effect of a low number of observations (site detections) on occupancy modeling (see standard errors > 1). In these cases, the number of detections is not enough to obtain reliable estimates of the occupancy, so that they are poorly informative about the value of the parameters. For that reason, these should not be considered in results. Provide only results from species with enough data based on standard errors (see Ahumada et al. 2013).
Validity of the findings: The main questions of the studies include:
(1) How much do hunting activity, conuco presence and forest cover affect wildlife occurrence?
(2) Do current hunting pattern of preferred prey and hunting habitat, reflect prey availability or cultural factors?
(3) Does current hunting techniques favour an increase in hunting frequency?
Garden hunting practice is described as hunting of wild animals when these enter swiddens and fallows to take advantage of the resources that these provide them (see Naugthon-Treves 2002 and Linares 1976).  However, the manuscript pointed out that huntig occurs in the forest, so I have some doubts if the hypothesis is properly formulated. In fact, camera traps in agricultural areas appear to be missed in the sampling design. Authors only considered dist_conuco as covariate explaining the issue about agricultural areas.
Additional comments: Authors need to include references which test the garden hypothesis (e.g. Naughton et al. 2003)
Line 39. It is "prey."
Line 54-58. I suggest removing this paragraph to start the Introduction with the main idea…since Line 59
Line 102. I recommend removing "Independently of Amazon region."
Line 157. It is not clear how many cameras by block. Each block had 25 sampling units of 2 km2, but authors pointed out 30 cameras by block
Line 257-259. Also, it would be informative a global result?
Line 267. A parenthesis is missed, 27%)
Line 297. It is species richness
Line 297. "Low number of conucos and all mammals' diet groups". Authors need to define functional groups in methods
Line 308. The procedure to estimate deviance needs to be described in methods
Line 331. I suggest using functional traits, according to Jones et al. (2009) and Wilman et al. (2014). For example, tayra is considered omnivorous based on diet data. It is vaguely described in methods (Lines 222-223). Please, include references
Line 456-457. Include some references about functional groups as an indicator of ecosystem functionality (e.g. Mason & Mouillot 2013, Tilman 2001).
Table 3. It is necessary to include the number of detections for each species. Nagelkerke's coefficient of determination is not described in methods.
Authors should have included a table showing the description of the sites in terms of vegetation type and the other covariates where they were located. I suggest it as Supplementary material.

Figure 1. I suggest including a map with the Amazon basin to locate the study area in this context. It will be useful for readers of other regions.
As supplementary material, if it is possible, include pictures of the species, it would be informative for readers of other regions.

MacKenzie, D.I., Nichols, J.D., Royle, J.A., Pollock, K.H., Bailey, L.L., Hines, J.E., 2018. Occupancy estimation and modeling: inferring patterns and dynamics of species occurrence, 2nd Edition ed. Academic Press, Boston.
MacKenzie, D.I., Bailey, L.L., 2004. Assessing the fit of site-occupancy models. Journal of Agricultural, Biological, and Environmental Statistics 9, 300-318.
Kéry, M., Royle, J.A., 2016. Applied hierarchical modeling in ecology: Analysis of distribution, abundance and species richness in R and BUGS: Volume 1: Prelude and Static Models. Academic Press, Boston.
Burnham, K.P., Anderson, D.R., 2002. Model selection and multimodal inference: a practical information-theoretic approach. Springer, New York.
Tobler, M.W., Zúñiga, A., Carrillo-Percastegui, S.E., Powell, G.V.N., 2015. Spatiotemporal hierarchical modelling of species richness and occupancy using camera trap data. Journal of Applied Ecology 52, 413-421.
Tobler, M.W., Carrillo-Percastegui, S.E., Powell, G., 2009. Habitat use, activity patterns and use of mineral licks by five species of ungulate in south-eastern Peru. Journal of Tropical Ecology 25, 261-270.
Ahumada, J.A., Hurtado, J., Lizcano, D., 2013. Monitoring the status and trends of tropical forest terrestrial vertebrate communities from camera trap data: a tool for conservation. PLoS ONE 8, e73707.
Jones, K.E., Bielby, J., Cardillo, M., Fritz, S.A., O'Dell, J., Orme, C.D.L., Safi, K., Sechrest, W., Boakes, E.H., Carbone, C., Connolly, C., Cutts, M.J., Foster, J.K., Grenyer, R., Habib, M., Plaster, C.A., Price, S.A., Rigby, E.A., Rist, J., Teacher, A., Bininda-Emonds, O.R.P., Gittleman, J.L., Mace, G.M., Purvis, A., 2009. PanTHERIA: a species-level database of life history, ecology, and geography of extant and recently extinct mammals. Ecology 90, 2648-2648.
Wilman, H., Belmaker, J., Simpson, J., de la Rosa, C., Rivadeneira Marcelo, M., Jetz, W., 2014. EltonTraits 1.0: Species‐level foraging attributes of the world's birds and mammals. Ecology 95, 2027-2027.
Tilman, D., 2001. Functional diversity. Encyclopedia of biodiversity 3, 109-120.


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: SHIFTING CULTIVATION AND HUNTING ACROSS THE SAVANNA-FOREST MOSAIC IN THE GRAN SABANA, VENEZUELA: FACING CHANGES
Review round: 1
Reviewer: 2

Output:
Basic reporting: This research, by combining quantitative data and findings from interviews and analyzing the spatial relationships between Indigenous communities, habitat (including anthropogenic habitat) and game species, has the potential to make an important contribution to our knowledge of a significant (and complex) problem. There are very few studies on the spatial ecology of game species in tropical regions where hunting occurs, in part because it is often very difficult to do in remote regions – but it is critically important for managing wildlife. The camera trap data in particular is robust.

However, there are some weaknesses in this paper that should be addressed. One relates to the methodology, in that there is a somewhat “loose” fit between the data used and what is actually happening on the ground. Some of the indicators are somewhat course and/or imprecise, and there is no data on the actual harvest rates of game species, which is a significant limitation (acknowledged briefly on lines 404-405). However, some of these problems can be resolved with the existing data (as discussed below). A second problem relates to the interpretation and analysis of the data and rethinking some of the claims that are made. The literature review is good in some areas, but very limited when it comes to publications on the spatial patterns of hunting and wildlife abundance (see below).

Additional revisions are required to revise the objectives, clarify aspects of the methodology, pay more attention to ethical issues, and correct numerous minor grammatical errors.

Revision of research questions and objectives (lines 123-126 and elsewhere):

The authors state that they “specifically evaluated”
“How much do hunting activity, conuco presence and forest cover affect wildlife occurrence?” It seems to me that the camera-trap survey should provide the data needed to estimate game species abundance, not simply “occurrence” which I believe is a less precise measure (if not appropriate it would be useful to have some exaplanation of why “occurrence” is the primary variable). The question also includes “hunting activity” which is a bit misleading, as this was not measured. As such, I would re-articulate the research question along these lines
“Are there differences in the relative abundance of game species that are attributable to the presence of (i) conuco agriculture and (ii) hunting activity, measured indirectly by game preferences and proximity to Indigenous communities.” This question seems to capture virtually all of the research that is being presented here, and the authors could simply focus on this one with some further elaboration on the question to explain the research design and the rationale for the approach they use. From my perspective, the other questions below don’t belong. Answers to this first question are very valuable on their own and merit publication, but I will comment on the other ones as well.

“Does current hunting pattern of preferred prey and hunting habitat, reflect prey availability or cultural factors?” This research question is a bit misleading, because data were not collected on “hunting patterns”.  Also, the question is not clear.

“Does [sic] current hunting techniques favor an increase in hunting frequency?” This was not measured, so should not be included as one of the research questions. There is some data about the hunting technologies that are reported and anecdotal information about the cost of ammunition, for example, but there is no data on the number of game animals captured using different techniques or the differences in the type and amount game captured by hunters using different techniques.

Finally, all references related to mining should be from the description of the research (lines 126-128) and results sections, and the materials & methods section. It is an important consideration, but the authors did not do any original research related to this. It does belong in the introduction and discussion sections as it is relevant for the significance of the research.

Overall, the paper is well organized. There are numerous grammatical errors, however, too numerous to list here. Further editing will be needed.

Other minor revisions:

The use of the term “ecosystem collapse” (line 96 and elsewhere) is not defined and is also overstating the possible outcomes. Something along the lines of “significant change” is more appropriate. The term “disrupt” is a judgmental term. The term “alter” would be more appropriate.

If possible, separate “hunting and fishing” as separate food sources (line 258).

Camera traps detected 43% of species twice (line 293).  Should this be twice or more?  As indicated elsewhere, it would be useful to have a summary table of sightings.

Table 3 is difficult to interpret. The authors should explain exactly what the values for “estimate” and “SE” are, as well as “detectability”. Also, for L. pardalis, values are given for “hunting” – shouldn’t this be the same as the others? There are other differences for other species as well in terms of what is presented. The table should be reorganized as a single table of rows and columns, instead of what is there now which is several different tables joined together.
Experimental design: Variables used in the analysis

The authors use “species composition” (line 122 and elsewhere) and “species occurrence” in multiple places, which is useful but they are less robust measures compared to abundance. The camera-trap dataset appears to be sufficiently large for calculating relative abundance or even population density estimates. This would provide a more precise variable for analyzing differences between their sites. For an example, as well as additional methodological issues that should be discussed (e.g., variation in detection probabilities associated with sampling design and species behaviour) along with a stronger rationale for the methodology used. For this they could refer to the article:

“A camera trap assessment of the forest mammal community within the transitional savannah‐forest mosaic of the Batéké Plateau National Park, Gabon” by Hedwig et al. (2018) African Journal of Ecology, Volume 56 (4): 777-790.

This article is one of several in a special issue on camera-trap methods. They could also refer to the following to write a more detailed discussion of potential bias and errors related to camera-trap methods and examples of how to estimate game species population densities:

“Camera trap placement and the potential for bias due to trails and other features” by Kolowski et al., (2017) PloS one, Volume 12 (10).

“Drawn out of the shadows: Surveying secretive forest species with camera trap distance sampling” by Bessone et al., (2020) Journal of applied ecology, Volume 57 (5): 963-974.

“Monitoring the Status and Trends of Tropical Forest Terrestrial Vertebrate Communities from Camera Trap Data: A Tool for Conservation” by Ahumada et al., (2013), PloS one, Volume 8(9).

“Abundance and composition of the medium to large-sized mammals in a private area of a REDD+ project in Acre, Brazil” by Botelho et al. (2018) Biota neotropica, Volume 18 (3).

The variable “n_conuco” is based on “the number of conucos reported or observed in a given block” (line 203). This is a fairly crude measure that does not take into account the size of these farms, when more precise measures seem to be available. The authors present a map that includes land cover categories, and used a buffer analysis for forest cover. If this spatial data is accurate, it would be better to make calculations of agricultural areas based on this same approach for a stronger analysis. This data could replace the “n_conuco” variable as well as the “conuco_dist” variable, which again is a course measure. Moreover, any of these quantitative measures are subject to limitations related to their fit with different species. For species with small territories, forest cover within a 1 km buffer might be a good indicator of the available habitat, but for game animals with larger territories, the land cover over larger areas would be more important. Careful consideration the appropriate buffer distance for different species is needed and a discussion of this limitation is needed in the paper.

Another ecological variable that might explain some of the sighting data is proximity to rivers. This is particularly true for the paca, which if I’m not mistaken, prefers to be close to streams. This factor should be considered in the analysis and interpretation of findings.
The variable “dist_com” might be appropriate, but again seems fairly coarse and requires some justification. For example, a site that is located in between 2 or 3 communities might experience more pressure than another one that is only accessible by one community, even if it is closer.  Moreover, there is a large variation in the size of the communities in the study area that likely affects hunting pressure. Uroy-Uaray is about three times larger than Kawi, for example. There are tools available in the GIS software the authors use to make better measures of “closeness” to human settlements, that take into account multiple villages (if appropriate) and differences in population size.
For the camera-trap data, birds and reptiles were later removed from the analysis. How many sightings were used in the analysis then? Was it the reported 7,466 events (line 158), or less? It would be useful to have a table with the breakdown of sightings used in the analysis, by species and each of the 6 blocks.

The authors state that they assessed the “most frequently hunted species” based on “importance of hunting” and “hunting preference” (lines 191-192). Firstly, the “importance of hunting” (which might be better stated as “hunting pressure”) is based on a simple list of game species reported by interviewees. This is problematic, given that the importance of species listed was not ranked in terms of frequency captured or as a food source taking into account body mass. Species that come to mind and that are more memorable, such as the black curassow, might not be the ones that are actually hunted more frequently. This affects what can actually be claimed. For example, the authors state that “These were the most frequently hunted species” (line 275). They do not have sufficient evidence to make this claim. They can only state that they are the most commonly listed game species.

Asking hunters about their game preferences is likewise a weak indicator of hunting pressure, compared to data on the type and amount of game that is actually captured. Preference does not equate to actual harvest rates. For example, armadillos may not be preferred but might actually be captured frequently. Alternatively, a species that is wary or difficult to catch (e.g., arboreal or nocturnal species) might be highly preferred, but captured infrequently. Again, this affects the analysis that can be done and what can actually be claimed.

As an additional analysis that might be useful, the authors could compare the estimated abundance of game animals versus animals that are not hunted by the Pemon (according to the interviews), but this would require an additional analysis with its own complications (e.g., how to determine whether a difference in abundance is attributable to hunting as opposed to a differences related to species characteristics, habitat quality, or something else).

Interview data

More information is needed on how were the interview participants selected and how representative the sample is. If it was not a random sample, this should be stated explicitly and discussed.

The authors note that there were no reports of hunting carnivores (lines 367-368), but do not raise the possibility that legal frameworks might lead to negative consequences for people who hunt endangered species. People might be reluctant to reveal what is considered by officials as illegal hunting. This issue should be addressed.

Related to this, there are ethical issues that are not mentioned. In particular, are there any potential risks posed by the research for local communities who rely on hunting?  Could the research findings be used in ways that might affect their hunting rights?

There is some good information on hunting activity as practiced by the Pemon, but some important aspects are neglected. Firstly, given the emphasis on garden hunting, it is important to know something about hunting in agricultural areas. Even people who say that they are not hunters will often capture game opportunistically in their farms.  The authors refer to “hunting method” (line 265), but this is incorrect as the results refer to hunting technologies. This suggests that the authors only asked about hunting trips, when other methods might be used – for example, the use of traps or opportunistic capture of game while doing farm work.

This leads to another question: do residents of these communities have dogs? Dogs are not included on the list of hunting technologies. If dogs do not play a role in hunting, this would be unusual and should be stated explicitly. There is also the question of how far hunters go to capture game, discussed above.

There are four communities in the study area according to the authors, but there are five on the map provided, although the fifth one is not named. Is this an error?  If not, the presence of this additional community should be addressed.

Note -- I do not feel adequately qualified to review the choice of statistical methods for this study, but I do feel confident in my assessment of the utility of the variables used and overall research design. In any case, some of the statistical methods could change if the authors take my advice.
Validity of the findings: Findings

The research aims to answer questions related to the relationships between game species, habitat, and hunting. Several statements about specific relationships are provided, but the overall pattern that emerges from this research is not entirely clear. The section “Diversity and composition” (lines 289-303) provides several very specific details about game species in different blocks, but again, the overall pattern is not discussed. Answers to the more basic questions should be presented clearly. For example, are there broad differences in relative abundance of game species between sites that are related to the presence (or preferably, prevalence as measured by total area within an appropriate buffer) of conuco farms? Which species are more abundant, less abundant, or the same? A simple scatterplot or line graph would be helpful to discern the overall pattern (e.g., % farmland on the Y axis, and sightings on the X axis), as opposed to the specific examples provided.

The same is true for the influence of distance from Pemon communities – is there a broad difference in sightings related to distance from the nearest community (or preferably in relation to an index that takes into account multiple communities and their population)? Are there significant differences for different species that are either more abundant or less abundant near the communities? Given that these two variables (distance to settlements and amount of farmland surrounding the camera trap) are closely inter-related, the analysis could then examine both together in the occupancy model, after they are examined separately. I recognize that looking at dietary groups is part of the garden hunting hypoethesis, but an additional analysis of individual species would be even more informative. Combining multiple species into dietary groups can obscure significant differences within these groups.

The section entitled “Occupancy models” is similar in providing a series of examples, without an explanation of the overall pattern, which could be presented in the form of text and/or as an additional figure. As discussed above, Table 3 presents results of a model combining several variables and is difficult to interpret and could be reformatted as a single table of rows and columns if possible, not as a series of tables for different species. More explanation in the caption would also be helpful, especially for a broader audience that includes conservation management decision-makers.

A table that presents basic summary data of sightings would be very useful. It would be useful to know how many sightings there were for each species (with more than 8 sightings) in each block and all blocks combined.

The interpretation of the research findings would benefit from engagement with additional studies that have examined the spatial patterns of hunting.  There are five that are particularly useful, that they should include in their discussion (and that could also be helpful in how to re-analyze their data and in other ways):

“Spatial patterns of primate hunting in riverine communities in Central Amazonia” by Pereira et al. (2019) Oryx, Volume 53 (1): 165-173.

“The Spatial Patterns of Miskitu Hunting in Northeastern Honduras: Lessons for Wildlife Management in Tropical Forests” by Dunn and Smith (2011) Journal of Latin American geography, Volume 10 (1), p.85-108.

“The spatial patterns of indigenous wildlife use in western Panama: Implications for conservation management” by Smith (2008) Biological conservation, Volume 141 (4), p.925-937.

 “Dynamics of hunting territories and prey distribution in Amazonian Indigenous Lands” by Constantino (2015) Applied Geography, 56 222-231.

“Spatial tools for modeling the sustainability of subsistence hunting in tropical forests” by Levi et al. (2011) Ecological Applications, Volume 21: 1802-1818.

There are valuable results highlighted in the discussion section, for example the high number of paca sightings in highly modified areas – although as indicated above, it would be useful to know exactly how many sightings there were for each species. Another conclusion relates to the lower number of deer sightings as being the result of overhunting. The arguments would be more persuasive if there was some measure of number of sightings relative to what would be expected in areas where hunting does not occur, if possible. Given the very different sizes and ecologies of different species, one would expect the number of sightings to vary considerably, even in the absence of hunting.

The faunal composition and relative abundance of species is very important from a conservation perspective. The authors examine species richness in their analysis, but do not comment on the absence or lower relative abundance of species that are of greater concern (although they include IUCN status in Table 3). Overall, is there evidence in their findings that certain species are more vulnerable to the loss of habitat converted to conucos and proximity to communities that include hunters? Or conversely, that the presence of Indigenous communities is beneficial for certain species? The answers are perhaps there in the manuscript, but they are not highlighted as part of the overall pattern that was found in this research.

One very important aspect of the spatial patterns of hunting and game species that is not discussed is source-sink dynamics. Firstly, are there any significant areas in the region that do not experience hunting, or very little hunting. Local depletion of game species might still be sustainable if there are adjacent source areas. The map provided suggests that there may be large areas of forest to the east and northeast.

Another related issue is the spatial distribution of human settlements. The authors explain that the Pemon now live in more nucleated settlements, in a less dispersed pattern. Is there any indication that there is now less hunting pressure in more distant areas? Another related consideration that is not discussed is how far Pemon hunters go when they hunt. For example, do they only hunt in areas that are within one day’s walk, or do they also go on overnight trips to more distant areas? This is not an easy question to answer, but it merits some attention. The literature cited above provides guidance on these issues.

The authors state that “the frequency and amount of hunting has been limited because of the high prices of cartridges” (lines 372-373). What is the evidence that they have to make this claim? They should provide evidence or change the wording to acknowledge the uncertainty involved.

The authors state that collared peccaries “were poorly detected” because of seasonal movements. This is true of the white-lipped peccary, but is not as important factor for this species. Other factors may be important, such as habitat, predation, or hunting.

Overall, from my point of view the analysis presented represents a good first step, but a more careful and thoughtful interpretation and discussion is needed.
Additional comments: As stated in another section, this research has the potential to make an important contribution to our knowledge of a significant and complex problem. There are very few studies on the spatial relationships between game species and Indigenous communities in the neotropics -- or anywhere. The camera trap data is very robust, and with some additional work to rethink the analysis and the interpretation of the findings (that takes into account some of the issues raised in this review and that makes use of the literature on the spatial dynamics of hunting), this will be a much stronger paper.


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

Input:
Title: SHIFTING CULTIVATION AND HUNTING ACROSS THE SAVANNA-FOREST MOSAIC IN THE GRAN SABANA, VENEZUELA: FACING CHANGES
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comments
Experimental design: No comments
Validity of the findings: No comments
Additional comments: The manuscript revisions were strong, and I understand and appreciate the points authors made in this new version. It is a remarkable contribution to the Garden hunting hypothesis. If it is possible I would suggest reducing the discussion (~ 3000 words), and prioritizing it according to the main findings of the paper.

General comments
Line 172. Six blocks…because it is the first time that it is mentioned, include in parenthesis (see Sampling design and camera trap survey section)

Line 175 five community leaders known to IS….
personal observation? In parentheses?

Line 283-284. For this study, we calculated tree cover and distance to nearest conuco and river as covariates of species abundance…
Lines 347 – 349 … As site covariates we used tree cover percentage around the camera trap (tree_buffer), distance to river (dist_river), and distance to nearest conuco (dist_conuco)…
It is necessary to standardize terms.

Line 363 …definition of “p” is missed. Why 0.25? It is different to the “p” of occupancy modeling.

Lines 405-406 Thirdly, we compared the predicted abundance of wildlife (based on RN-models see next section) in hunting and not hunting sites.
…see next section?

Dietary group definition is misses in Table 1
Table 2. dsit_rios  (dist_rios?) It is in Spanish.

Figure 5. Scientific names in cursive


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: EMBRYONIC DEVELOPMENT AND PERINATAL SKELETON IN A LIMBLESS, VIVIPAROUS LIZARD, ANGUIS FRAGILIS (SQUAMATA: ANGUIMORPHA)
Review round: 1
Reviewer: 1

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: The authors have crafted a paper that is well written, well delimited, and well illustrated. It makes a small but significant contribution to our understanding of skeletal development in squamates, particularly in this poorly-studied clade. All of my suggested edits below are intended to slightly improve the writing or suggest more appropriate terminology. Otherwise, nicely done!

Line 13: change ‘on’ to ‘of’
14: change to ‘One such group is anguimorphs,…’
15: change ‘described’ to ‘describe’ (keep present tense throughout)
16: delete ‘species of’
17: delete ‘lizard, delete second comma, change ‘observed’ to ‘observe’, delete ‘a’ and ‘that’
18: change ‘concerned’ to ‘in’
19: delete second ‘the’
20: change ‘described’ to ‘describe’
22: delete ‘being’
23: remove hyphen
27: delete ‘the’
28: change ‘rich’ to ‘reach’
29: insert ‘relative’ before ‘importance’
34: delete second and third commas
37: change ‘that’ to ‘the’
39: delete ‘currently’ and ‘of squamates’
40: delete ‘despite the great increase in our knowledge in recent years,’
43: change ‘are’ to ‘is’ and ‘include’ to ‘includes’
44: change comma to colon and delete ‘including for example’
45: here and elsewhere, insert comma after ‘e.g.’; change first comma to semicolon
46: change third comma to semicolon
47: change ‘or’ to ‘and’
50: delete ‘the alligator lizard’
55: delete ‘lizard’
57: Nicolas, 1904 is not in lit cite
58: change ‘buds’ to ‘bud’
65: change ‘aimed to’ to ‘here’
67: change ‘are’ to ‘is’
73-75: change sentence to ‘This study is based on five perinatal slow worms and 33 embryos dissected out of 7-9 ethanol-preserved females (the mother is not known in three embryos).’
75: delete ‘all’ and capitalize ‘these’
78: change first part of line to ‘morphology (Sos, 2011), and locality when known’
102: insert ‘the’ before ‘four’
109: change ‘provided’ to ‘provide’
119: throughout the description, I would move the figure reference(s) to the beginning of the section so readers know when to look while they’re reading that section
121: change ‘posteriorly’ to ‘posterior’
135: insert ‘and’ before ‘presence’
139: change ‘reached’ to ‘reaching’, insert comma after ‘jaw’
147: insert ‘on’ after ‘takes’
150: change ‘started’ to ‘are’
154: insert ‘their’ after ‘only’
169: replace ‘—’ with a semicolon
170: delete ‘also’ and comma
174: change ‘anteriorly’ to ‘anterior’
183: delete ‘being’
190: change ‘is composed of’ to ‘presents’
196: change ‘which’ to ‘that’
201: delete ‘of’ and change ‘approximately’ to ‘approximating’
208: delete ‘the’
214: change ‘simple’ to ‘simply’, delete second comma
224: change ‘in’ to ‘at’
225: delete first ‘dorsally’
228: delete ‘with its’ and ‘end’, change ‘posterodorsal’ to ‘posterodorsally’
230: insert ‘there is’ before ‘no’, delete ‘can be’
231: delete ‘observed’
233: insert ‘The’ at beginning of sentence
235: delete ‘in the’ and ‘part’, change ‘anterior’ to ‘anteriorly’
237: insert ‘the’ after ‘into’ and change ‘otooccipital’ to ‘otooccipitals’
241: change ‘neonatal lizard’ to ‘neonate’
243: delete ‘bone’
249: ‘The posterior margin of the bone…’ – which bone?
253: insert ‘The’ at beginning of sentence
259: change ‘which’ to ‘that’
262: delete ‘to it’
267: delete second ‘the’ and change ‘Meckel’ to ‘Meckel’s’
269: delete second ‘the’, change ‘Meckel’ to ‘Meckel’s’, delete ‘also’
270: insert ‘mandibular’ before ‘bones’, delete ‘forming the mandible’, change ‘other than that’ to ‘otherwise’
274: change ‘was observed’ to ‘occurs’
275: change ‘were’ to ‘are’
276: insert ‘first’ before ‘ceratobranchial’, change ‘was’ to ‘is’
277: change ‘ossified’ to ‘calcified’ (only the first ceratobranchial ossifies in the squamate hyoid; everything else calcifies), change ‘ossifications’ to ‘calcifications’
289: change ‘dorsally’ to ‘dorsal’
292: insert ‘the’ before ‘very’
305: delete ‘relatively’
307: change ‘things’ to ‘features’, insert comma after ‘preservation’
308: delete second ‘in’ and change ‘general’ to ‘generally’
310: delete ‘in squamates’
312: delete ‘that are often’
313: insert comma after ‘tables’
314: change ‘of’ to ‘from’ and ‘to’ to ‘in’
315: change ‘than’ to ‘from’
316: change ‘of’ to ‘from’
324-325: delete ‘which is far less light permeable than the eggshell.’
329: delete ‘, for example,’ and comma after ‘stomach’
332: change ‘was’ to ‘is’
333: change ‘was’ to ‘is’
334: delete ‘The’ and capitalize ‘embryonic’
337: delete ‘it’
349: change ‘Such’ to ‘This’
353: insert comma after ‘fragilis’, rearrange to ‘an almost universal feature’
355: delete ‘apparent’
366: change ‘such a’ to ‘this’
371: change ‘parietal’ to ‘parietals’
389: change second ‘the’ to ‘a’
393: change first ‘are’ to ‘is’
398: change ‘tends to’ to ‘would’
399-400: delete ‘(at least in currently studied species)’
408: insert comma after ‘viviparity’, change ‘potential’ to ‘potentially’
Conclusions: too many sentences are recycled verbatim from earlier in the text; please paraphrase more
412: delete ‘may’ and change ‘represent’ to ‘represents’
413: hyphenate ‘densely sampled’
420: insert ‘have’ before ‘they’
421: insert comma after ‘)’ and ‘and’ before ‘the’
423: remove hyphen from ‘well-ossified’
426: delete ‘the
427: change ‘rich’ to ‘reach’
570: make ‘A’ lower case
Figure 5 caption: please specify which views these are
Figures 7-8: why not label scleral ossicles?
Figure 8 caption: squamosal is missing
Figure 10, 12 and 13 captions: ‘cb’ should be ‘first ceratobranchial’


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: EMBRYONIC DEVELOPMENT AND PERINATAL SKELETON IN A LIMBLESS, VIVIPAROUS LIZARD, ANGUIS FRAGILIS (SQUAMATA: ANGUIMORPHA)
Review round: 1
Reviewer: 2

Output:
Basic reporting: This manuscript entitled " Embryonic development and perinatal skeleton in a limbless, viviparous lizard, Anguis fragilis (Squamata: Anguimorpha) " by Tomasz Skawiński, Grzegorz Skórzewski and Bartosz Borczyk described the external morphology of the several developmental stages of the embryos, particular aspects of their skeletal development and discuss the important aspects of the intraspecific variation in individual development of the enigmatic limbless lizard – A. fragilis.

Since there is no any available information about the early development of this lizard and the variation in individual development have not analyzed so in detail, this is a potentially important contribution.

Therefore, I believe this study is worth publishing for PeerJ, although there is room for improvement, in particular, in accuracy of morphological description and in discussion.

As I am not a native English speaker I do not presume to evaluate English, however, the text contains misprints which should be double checked.

I am opposed to anonymity in the review process and choose to identify myself as Oleksandr Yaryhin.

Minor comments

Line 32 and 43
Wrong citation. Do you mean this one? Uetz P, Freed P, Hošek J, eds. 2021

Line 78
..in areas… Please add information about the localities

Line 81
…date of collection of the mother… Please provide information about the exact dates and information about the number of embryos from each female.
Use term female instead of mother.
Line 83
… from the Standard Event System… Hereinafter it is not clear exactly which Standart Events (SE) do you use. Please add SE codes.
Hereinafter, as you were guided by the SE System, when describing the characteristics of the embryo, you should also indicate the SE code or assign a new one if the character is new.
Line 98
…alcian blue… Alcian blue solution has decalcifying effect which could cause artificial “variation” in the pattern of ossification.
Line 103
…did not bond to the cartilage…
Actually, your figures 4-8 indicate that the cartilage is well visible.
Line 109
…of the “external osteology” of a …
Better to use term – dermal ossifications or bones
Line 118
Embryo morphology
I suggest to rename into – External anatomy of the embryos
Line 119
Stage 1.
As you do not have each developmental stage to make a classical staging table, thus prior to the description of the stages provide the reader with the information, that your «stages» are not equal to the calssical staging system. I would also recommend to replase here the term «stage» with the term - «developmental state».

… neuropore is closed…
Hereinafter, as you were guided by the SE System, when describing the characteristics of the embryo, you should also indicate the SE code or assign a new one if the character is new.
Line 121
Please delete word relatively. Otherwise add something to compare with.
Line 131
…greatest variability in morphological traits… More information is needed here. Where possible, please also provide reader with the measurements.
Line 135
…presence of the hemipenes… The figure is not iformative, please add picture for comparison. Moreover, it could be sexual dimorphism.
Line 140
… is entirely cartilaginous (Fig. 4).
Better to say that there are no evidences of the bone mineralization at this stage. Because the bone could be present without mineralization’s, what also could be a result of a long-term preservation and also due to the Alcian blue staining.
Line 143
The mesencephalon becomes relatively smaller but …
The brain cannot become smaller, it can be that it is less prominent.
Line 165
If possible, I would suggest to disarticulate one skull and to make one figure with all separated bones from one side of the skull in lateral view. This will greatly improve the perception of your description. From the current illustration, many important features are not well visible.

Line 302
…suggest that the developmental sequences are similar…

Here it would be great to show the comparisons between the species in tabular form
Lines 312-347.
Apparently, this is the most important finding in the current study. I would highly recommend to give more information about the differences between the embryos into the result part. It is definitely necessary to add the table about the size characteristics of the embryos from each female.
This also should be somehow included to the title, for attracting broader audience to your research.
Experimental design: see above
Validity of the findings: see above
Additional comments: see above


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

Input:
Title: CRANIAL ANATOMY OF BOLOTRIDON FRERENSIS, AN ENIGMATIC CYNODONT FROM THE MIDDLE TRIASSIC OF SOUTH AFRICA, AND ITS PHYLOGENETIC SIGNIFICANCE
Review round: 1
Reviewer: 1

Output:
Basic reporting: see below
Experimental design: see below
Validity of the findings: see below
Additional comments: General comments: This paper provides a new description of the basal cynodont Bolotridon. As the authors note, it has been somewhat overlooked compared to more common early cynodonts like Thrinaxodon. Using new CT scan data, they have been able to uncover new anatomical features that help resolve its phylogenetic position and potentially the evolution of some characters related to the presence of turbinals in the nasal cavity. The authors also note that Bolotridon was collected at a locality that has produced other atypical small taxa, and discuss the possible implications of this assemblage. The paper is well written and easy to read, with useful illustrations. It represents the kind of ct-based descriptive work that is needed to build up a database of comparative observations than can be incorporated into the next generation of phylogenetic analyses, and it definitely merits publication.

Overall, my suggestions for changes are minor, and most consist of suggestions for clarifications. In a couple of places, I noted cases where revisions to existing figures or additions of images would be helpful.

Line 27: I recommend changing strata to assemblage since you’re not specifically talking about a rock unit.

Line 39: change ‘currently instable’ to ‘previously unstable’

Line 53: I recommend adding a citation for Abdala and Ribeiro (2010) and Lukic-Walther e tal. (2019) as examples of more recent papers specifically about cynodont diversity patterns.

Lines 62-71: This is kind of a run-on sentence. I suggest dividing it up into two sentences, one that focuses on listing the other Karoo taxa, and the other focusing on the Karoo having the best record, potentially including evidence that the cynodont radiation began in the Permian.

Line 78: Maybe divide up the citations so that the ones pertaining to Galesaurids are earlier in the sentence than those pertaining to thrinaxodontids.

Line 89: I recommend replacing section with something like part or portion. I feel like using section here could cause confusion with an actual stratigraphic section at a locality, when that’s not the case.

Line 98: change while to whereas

Line 99: change its to the

Line 127: replace a first with novel

Line 164: Replace since with because. Also, later in this sentence, note which of the duplicate characters your deleted (presumably #64).

Line 170: A minor point, but is there a reason why you didn’t use a random addition sequence? It is unlikely to cause serious bias in the tree search with a fairly compact dataset like this one, but still a bit of a departure from common practice.

Line 183: Saying the septomaxilla is largely missing implies that some portion of it is still present. However, I don’t see it labeled in the figures, and there isn’t any subsequent description of it. Is there any preserved? If not, I recommend stating explicitly that it’s not preserved.

Line 192: change while to whereas

Line 231: I recommend specifying that the medial contact of the maxilla is on the ventral surface of the skull. It might seem obvious, but I think it’s good to be clear given that the approach each other fairly closely on the dorsal surface of the skull.

Line 244: I recommend moving the paragraph starting on line 263 (i.e., describing the internal and external  surfaces of the maxilla) up so that it comes before the paragraph describing the dentition. To me it seems more logical to describe the all the features of the bone first, and then describe the dentition.

Line 246: Is there any explanation for the discrepancy in the Broili and Schroder’s tooth count (e.g., something that is easier to see with CT data)?

Line 260: change while to whereas

Line 283: It’s hard for me to see what you’re calling a ridge in Fig. 4. Anterior to the opening of the lacrimal canal, I see a somewhat rounded, raised structure. Is that what you’re referring to? If so, I think you should extend the leader line down so that it is in contact with it. If that’s not what you’re pointing out, I think you will need to add an image (either a cross section, or a new rendering, something like the one in Fig. 6) that shows the ridge more clearly. This is potentially a very important structure, so you want to make sure that readers can see its morphology clearly.

Line 302: The wording here makes it seem like you think the jugal/palatine contact is an artifact of deformation. If that is correct, I recommend saying that explicitly.

Line 315: I recommend labeling this in Fig. 6 and calling out the figure here.

Line 331: I realize that it probably doesn’t preserve much useful anatomy, but it seems odd that you don’t mention the parietal in the description of the skull roof. Even adding a sentence that says it doesn’t preserve much information would help avoid readers thinking it was omitted.

Line 336: remove only

Line 342: The absence of a grooved anterior section is somewhat hard to see in the figure. Is it possible to add a cross-section that shows this better?

Line 396: and ‘and’ before slopes

Line 398: change to: “...(only the left incisor arcade is complete; the second incisor on the right sidfe has fallen out)...”

Line 405: change mandible to dentary

Line 408: I think erupted might be a better word choice than developed here. I think this is particularly the case for PC 4. It seems to have a crown that is comparable in size to the others, it’s just not as far out of the dentary.

Line 421: I realize that you focus on galesaurids here given their closer temporal and likely phylogenetic proximity to Bolotridon, but it might also be good to add something like “and other basal cynodonts” to the sentence to help differentiate the condition here from what’s seen in the Permian taxa.

Line 479. I think you should start a new paragraph here. There seems to be a shift in main ideas from talking about characters uniting Bolotridon and eucynodonts above, to comparisons with more basal taxa from this line forward.

Line 534: subzones should not be capitalized.

Line 545: It seems like it would be appropriate to cite Hotton’s (1974) describing Kombusia here.

Ken Angeilczyk


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: CRANIAL ANATOMY OF BOLOTRIDON FRERENSIS, AN ENIGMATIC CYNODONT FROM THE MIDDLE TRIASSIC OF SOUTH AFRICA, AND ITS PHYLOGENETIC SIGNIFICANCE
Review round: 1
Reviewer: 2

Output:
Basic reporting: I have a few suggestions for changing the text listed below. The figures are well-done and the description in combination with the figures presents a good representation of the specimen.

line 27: "this strata" should be "these strata"
39: "instable" should be "unstable"
66:  and [add "in"] Europe
67: .... suggesting that [add "the"] cynodont
87: . . . ., 2010) and perhaps Cistecynodon (Brink and Kitching, 19--).
95: taxon [add 'have] made it
103: "Crompton", not Compton
117: . . .505 [add . (period)] Most do not . . .
200: . . . level of [add "the fourth incisor"] (I4; Fig. 2, 3)
202:  delete "but" and add "although" their apparent length . . .
223: median [delete"one" and substitute "ridge"]
231: . . . one another "in the palate" [delete "secondary"]
336: which appears [replace "only" with "to be"] very narrow
401 and elsewhere: The commonly-used convention of lower teeth being indicated by lower case letters (i, c, pc) and upper teeth by capitals (I, C, PC) is not observed in this paper, where all teeth are indicated by capitals. I do not suggest the authors redo the text and especially the figures for this paper, but suggest they cosider using the convention in subsequent papers.
Experimental design: The cladistic analysis is extremely well designed and I have no criticisms of it.
Validity of the findings: The authors are very cautious in their interpretation of the morphology of the specimen. They acknowledge repeatedly that interpreting this crushed specimen can yield differing interpretations of the restored morphology.

The cladogram of relationships among cynodonts is probably the most reliable one I know. The level of uncertainty with the interpretations are laid out, so we can estimate the probability of this particular configuration being the best  possible given the uncertainties involved in interpreting less than complete morphology.
Additional comments: I would only note that the attribution of Bolotridon [Tribolodon of Seeley] to the family Galesauridae in Hopson and Kitching (1972) was in a far different (pre-cladistic) context of family-level relationships than what we accept now. We did not separate out a Thrinaxodontidae or Eucynodontidae, among other currently-accepted monophyletic groiups. So using our placement of early epicynodontians in the Galesauridae does not mean the same thing as it does now in a cladistic context. Perhaps this can be worked into the text.


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

Input:
Title: FACTORS AFFECTING LIVESTOCK DEPREDATION BY SNOW LEOPARDS (PANTHERA UNCIA) IN THE HIMALAYAN REGION OF NEPAL
Review round: 1
Reviewer: 1

Output:
Basic reporting: With a few important exceptions, detailed in my General Comments, the authors employ clear and unambiguous English. Where this is not the case, easy changes are possible (for example, replace “group works” with “workshops”), which I have noted elsewhere.
Experimental design: Methods are not described with sufficient detail to replicate.
Additional details of the study design are needed for the reader to understand if and how you have adequately accounted for unavoidably opportunistic sampling approach.
There are multiple steps in the sampling process with the potential to introduce substantial bias and influence the results, but which do not appear to have been recognized.
Validity of the findings: You have not reported the key data underlying your manuscript - the locations of livestock attacks reported. Instead you have provided auxiliary data on the locations of livestock shelters, and of plant and wildlife sightings or sign - data which are not used in the manuscript. While these are helpful, they are inadequate on their own -   you report collecting 109 conflict locations, which you truncated to 86 “unique locations.” These data should be provided for review, and as a map in the manuscript. Additionally other information is needed to assess and interpret the validity of assumptions made implicitly in your MaxEnt modelling approach. See my general comments for more details.
Additional comments: SUMMARY
The authors use MaxEnt presence-only modelling to explore potential relationships between anthropogenic, biotic, and physical spatial covariates and snow leopard attacks on livestock in Central Nepal. They collected precise location data for over 100 putative (but unconfirmed, and unreported) snow leopard attacks, from which they infer that snow leopards prefer to attack livestock near barns, trails and roads. This finding has potentially important implications for conservation efforts aimed at reducing such interactions, but further details are needed to convince future readers that these findings are representative of the underlying ecology rather than sampling effort.

While the data set is commendable, and the authors are mostly restrained in their interpretations (In particular I appreciate the circumspection offered in Lines 149-156), the analysis and subsequent interpretation should be reconsidered in light of some unavoidable limitations and confounding factors that have not been adequately addressed. Foremost among my concerns is the possibility that the data and findings reflect sampling effort, not biological phenomena. The two dominant themes underlying my concerns are availability (Johnson et al. 1980), and imperfect detection (Mackenzie et al. 2002).

While I cannot recommend the manuscript for publication in its present form, I see opportunity for revisions that could better reflect uncertainties that are inherent in the data, and thus provide more circumspect and interpretable insight into the phenomena of snow leopard depredation on domestic livestock, a problem that has proven to be a major driver of anthropogenic mortality for the species.

MAJOR CONCERNS

I. Raw attack location data are not provided.

II. Consider your central finding that snow leopards “prefer to attack livestock near livestock shelters…” Unfortunately, there are much simpler, more parsimonious explanations for the patterns in your data that have not been accounted for in your analysis. (To be clear, I think the following possibilities need to be addressed and ruled out if you want to convince the reader of your interpretation.)

1. The recorded locations of snow leopard attacks reflect where you spoke with herders and villagers. In other words, although you are trying to map the risk of snow leopard attacks on livestock, you have instead mapped the distribution of those locations where you sampled (or more likely, some combination of sampling effort and attacks). As explained in more detail by Elith et al. (2011):

“A second fundamental limitation of presence-only data is that sample selection bias (whereby some areas in the landscape are sampled more intensively than others) has a much stronger effect on presence-only models than on presence-absence models...This bias will most commonly occur in geographic space (e.g., close to roads) but could be environmentally based (e.g., visiting wet gullies) but, regardless, will map into covariate space. Under biased sampling, a presence-only model gives an estimate of [presence X sampling] rather than [presence]. That is, we get a model that combines the species distribution with the distribution of sampling effort...”

Currently, the manuscript is missing important details of the sampling approach (and the raw data) which are needed to help the reader rule out the explanation above. You state that you assessed a total of 454 km2 yet no details are provided that demonstrate how the area was sampled. Indeed, you do not even provide a map of the attack location data. Given the structure of the terrain (2000-8000 m elevation!), and the nature of the data collection, no one would expect random or even sampling of the landscape. But even though you spoke to people to get your “samples,” you are still, ultimately, sampling the landscape, and should therefore show your reader how that sampling was distributed (. Because the sampling process involves 2 steps (A. a herder/villager observes a snow leopard attack, and B. You talk to that person and they report the attack), I think you will need to provide hopefully 2 pieces of information (as a map preferably) to convince the reader: A. Where on the landscape do the people you spoke to go with their livestock, or, where do livestock graze [in other words, where are the villagers/herders sampling? This information is only partially provided in the supplemental file with livestock shed locations],and B. Where did you talk to villagers/herders [where did you conduct the workshops?].

2. Alternatively (or additionally), the recorded attack locations simply reflect livestock distribution on the landscape. This is related to the detectability issue in the previous possible explanation, but also related to the concept of availability. To illustrate, a snow leopard might prefer to kill livestock far from livestock shelters and people, but, because there are no livestock in those places, you do not have any records of snow leopard attacks there. A reader could interpret your current presentation to mean that there would be fewer attacks on livestock if people simply moved their livestock farther away from shelters, roads, and trails. This clearly problematic conclusion follows logically from your current presentation. ( A more logical conclusion might be that people should move the location of shelters, roads and trails - but I’m sure you can see why that is problematic too).

I think this is also related to the “possible risk zones” mentioned on line 88. In a footnote, you describe that these "were identified based on proximity to shed, grazing/browsing pastures of livestock, grazing
area where herders are normally absent." A map of those would be helpful to better understand the implication of this filtering process, and such a map probably represents the actual extent of your study area (see below), for the purposes of MaxEnt modelling.

While presence-only data can indeed be used to infer preference if detectability has been accounted for, such inference is well-understood to be sensitive to the resources deemed “available.” In your analysis, the “available” resources are represented by the landscape used in the MaxEnt model. But without more details about the sampling process and the study area, we have no way of knowing whether this landscape was truly available for snow leopards to kill livestock. Again, given the huge variation in elevation, it is very safe for the reader to assume that livestock are not present throughout the putative study area. Meaning that to address your stated goal of understanding what factors influence where snow leopards kill livestock, you will be better served by limiting the MaxEnt landscape to include only those parts of the landscape grazed/used by the villagers and herders you spoke with. In its present form, you are probably modelling where livestock occur, instead of where attacks occur (given livestock presence). Symbolically, I think you want to know what covariates influence the conditional probability P(attack|livestock presence) which is relevant to understanding where livestock are vulnerable to snow leopard depredation, rather than where in the world snow leopard depredation occurs (by defniition, it can only happen in places where there are snow leopards and livestock). What you may have modeled is where livestock are, P(livestock presence), in a landscape where snow leopards are presumed to be present. I think the best option is to define a more limited landscape for which you can assume that P(livestock presence)=1, and avoid any chance of confounding presence and attacks. Thus, I suggest that you rerun your MaxEnt models with a landscape that only includes areas where livestock are plausibly present in this landscape (I think this is the “possible risk zones” that you mention).

MINOR CONCERNS:
[I have not provided Line by line feedback, as major analytical revisions will require substantial revision of all sections of the paper]

1. If, after accounting for the distribution of livestock and sampling effort in the landscape, you still find that proximity to livestock shelters roads and trails are the most important factors affecting attack occurrence, what would account for that pattern? Why would snow leopards not attack livestock farther from human infrastructure? Alternatively, suppose that the pattern in your data has more to do with where livestock occur (and that because this critical piece is not included in your model, the other factors you’ve identified come up as the next best indicators). What would that indicate?

2. Figure 1 contains very little information, and somewhat misleadingly implies that the study area is a homogeneous landscape without any major structural variation. I suggest that the current figure 1 serve as an inset for a more detailed map of the study area showing some of the information outlined in my earlier comments, against a background that provides context to the structure of the terrain (e.g., a DEM, or aerial imagery)

3. You have not discussed Suryawanshi et al.’s (2017) paper, and its central finding that livestock predation increases with wild ungulate and livestock density. The scale of the analyses in the their paper is very different, but in light of their findings, I think it would be helpful if you could provide even general contextual information about the density of wild and domestic ungulates in your study area compared to other nearby areas, and consider how this might influence interpretation and general applicability of your results.

4. What (if any) criteria were used to distinguish common leopard, wolf, and bear attacks from snow leopard attacks? Presumably people did not always see the animal that attacked their livestock, or could have mistaken a snow leopard and common leopard?

5. Scale: The area of likely snow leopard habitat in the study area (i.e. excluding heavily glaciated and high elevation portions of the study area) is quite small (250km2) relative to a snow leopard home range (also roughly 200-250km2 based on Johansson’s estimates from Mongolia - Jackson’s VHF-based estimates cited for Nepal (cited on line 37) are regarded even by Jackson himself to be unreliable and an artifact of old technological limitations). This raises the question that the patterns in your data may not be very representative of the broader regional landscape. (Which isn’t necessarily a bad thing, but is a limitation that should be discussed), but rather individual variation among just a few snow leopard individuals (as you rightly note the population in your study area may only be 2-3 animals)

6. 109 unique attacks in a 3 year period suggest that a major proportion of snow leopard diet in the study area is made of livestock. Do you think this may impact the spatial depredation risk you are modeling in important ways?

7. “Group works” is a confusing term to me (e.g., Line 90). I suggest replacing with “group interviews” or “workshops”

8. Line 209-210 is not clear.

9. Footnote 3: “only villagers who received compensation….” what, if any, additional bias might this have introduced to your data? Is there any kind of verification involved in certifying that a snow leopard killed the livestock before compensation is paid? Is there a bias in that process?

10. Figures 3 and 4: Change variable names and axis titles to make them more understandable (e.g. Distance to footpath instead of dist_path)

Some additional references to consider -
Elith, J., Phillips, S.J., Hastie, T., Dudík, M., Chee, Y.E., Yates, C.J., 2011. A statistical explanation of MaxEnt for ecologists: Statistical explanation of MaxEnt. Diversity and Distributions 17, 43–57. https://doi.org/10.1111/j.1472-4642.2010.00725.x

Suryawanshi, K.R., Redpath, S.M., Bhatnagar, Y.V., Ramakrishnan, U., Chaturvedi, V., Smout, S.C., Mishra, C., 2017. Impact of wild prey availability on livestock predation by snow leopards. Royal Society Open Science 4, 170026. https://doi.org/10.1098/rsos.170026


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

Input:
Title: FACTORS AFFECTING LIVESTOCK DEPREDATION BY SNOW LEOPARDS (PANTHERA UNCIA) IN THE HIMALAYAN REGION OF NEPAL
Review round: 1
Reviewer: 2

Output:
Basic reporting: Technically the chosen study area for snow leopard conflict study is not correct. The manuscript lacks some of the recent literature and updates on the topics in this field. The given illustrations are very limited and difficult to understand. Also, data given in the supplemental files is very limited and difficult to link with the manuscript.
Experimental design: It was not clear how the data has been collected? It says 17 group discussion was done. The participants involved in the group discussion belong to which area/ villages or municipalities. The study area is not defined properly. The study area needs to be described clearly with an appropriate figure (s). Which area/landscape the authors is talking about is very important to make it clear to the audiences. Also, the variables used in the models are not enough to conclude with a big statement. Prey is one of the most important variables which is missing in the model. This has to be incorporated in the model to draw a meaning conclusion, without incorporating prey density/abundance, the study is incomplete.
Validity of the findings: It was a good idea to known the risk zone and high attack sites but the variables used are incomplete. Also, it was not clear how the participants were selected from the study area and how the data has been validated in the field.
Additional comments: It was a good study given that the choice of the study area is appropriate. It was very difficult to understand where the sampling was done and who are the participants of the group discussion (villages/municipalities). The most important part of the methods was not clear i.e. selection of the participants for discussion and mapping conflict areas. The authors need to define the study area very clearly. Also, it will be good to mention why this area was selected for this study. The variables used in the model is incomplete, the authors should include prey abundance/density as one of the variables in the model. Without this, the model is incomplete. I suggest the authors re-run the models incorporating this variable to draw a meaningful conclusion.


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

Input:
Title: FACTORS AFFECTING LIVESTOCK DEPREDATION BY SNOW LEOPARDS (PANTHERA UNCIA) IN THE HIMALAYAN REGION OF NEPAL
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: See my general comments for further thoughts on this. As before, the sampling process has the potential to introduce substantial bias and influence the results, and have not been fully considered.
Validity of the findings: There is a mismatch between your interpretations and the extent of the background area used in your MaxEnt Model. To resolve this in my opinion will require either A. rebuilding the model with a more carefully defined extent, over which you can more confidently assume even sampling probablility, or  B. revising the manuscript to reflect that there were likely major sampling biases relative to the extent used, biases which limit and confound your interpretations.
Additional comments: The additional details provided are very helpful and alleviate many of the concerns that I raised in my first review.

However, in my first review I highlighted my concerns about potentially important sampling bias confounding your results and I suggested that you to build a new model with a more limited geographic extent as one possible solution to resolve these issues. I will limit my remarks to this topic, as I remain unconvinced that you have addressed all my concerns.

I see from your rebuttal letter that there is some confusion about what I meant by "sampling." If you are mapping a phenomena, then the “population” that you are sampling from is the population of possible locations on the landscape. In other words – although you are speaking with human beings, you are sampling the landscape (very specifically in the context of MaxEnt models, you are sampling raster grid cells where snow leopard attacks occurred).

The landscape - geographic extent of your model - is equally as important as the data you feed into the model. The extent that you use (and the grain or resolution), can have huge influence on your conclusions, and as such, you should justify your choices, and recognize how those choices impact your conclusions and interpretations. Presently, the manuscript lacks any justification for the chosen extent, and does not recognize the limitations that the chosen extent imposes on the interpretations.

In your introduction you state the purpose of the study was to identify the factors affecting the risk of livestock depredation by snow leopards. Elsewhere, you interpret your findings as indicative of where snow leopards prefer to attack livestock. Together, this suggests to me that you are interested in understanding livestock depredation locations in comparison to all locations used by livestock – thus I suggest that you limit the extent to those areas (even if you have to make some assumptions and use a fixed buffer around livestock shelters or something).

Your model assumes that you had equal opportunity to observe livestock depredation at every point within the model extent. The extent of your Maxent model is presently constructed in such a way that you are almost guaranteed to find “that anthropogenic variables are more highly correlated with livestock depredation risk from snow leopards than environmental and topographic factors,” your stated hypothesis. This is because your model presently confounds snow leopard attack probability with livestock presence probability. This confounding arises out of sampling bias and an overly broad extent, which may be due in part to confusion about what you sampled.

For your results to truly reflect where livestock are vulnerable to snow leopard attack, you need to account for where livestock were present. You identify distance to livestock shelters, roads, and paths, as well as elevation, as the most important variables influencing snow leopard risk to livestock. Unfortunately, the more parsimonious explanation is that this is not snow leopard risk, but instead where livestock were present, i.e., where you sampled the landscape. In other words, the extent of your MaxEnt model is not matched to the extent of the area from which samples were drawn.

 I see two options:
1.	Change the model. This is the best option in my opinion. As I said in my initial recommendations, I still think you should run the model again, using a much smaller landscape that excludes places where livestock are not present, for example, by only considering areas that fall within a set buffer distance of livestock shelters.
2.	Alternatively, if you are willing to shift your interpretation further, and avoid talk of preference or risk, you could change the manuscript to reflect that you modeled where snow leopards killed livestock, but, because you did not account for where livestock are present in the study area you can only speculate as to why that was the case. This approach will require changes throughout the manuscript. For example, If you are comfortable with this confounding, you should change statements such as “Snow leopards prefer to attack livestock near livestock shelters and at moderate distances from human paths and motor roads”, to instead say something more like, “snow leopard attacks on livestock occurred near livestock shelters, but because we did not account for livestock availability, we were unable to determine if this pattern reflected an intrinsic preference on the part of snow leopards, or simply where livestock were most likely to be found.” The management implications of these two things are very different. The preference hypothesis implies that moving livestock to higher, further pastures would reduce attacks. The livestock presence hypothesis implies that livestock need better protection everywhere. Without accounting for livestock presence in defining the model’s geographic extent, you can only speculate - you do not have quantitative ability to distinguish between these two. Intuitively, the livestock presence hypothesis is more believable. That’s why you should probably just change the model. It will make for a much better manuscript. But a more restrained and circumspect presentation that recognizes the limitations of the model as it currently stands is nonetheless possible.


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: CONFIRMATION OF AGE-RELATED ALTERATIONS IN INHIBITORY CONTROL USING A MODIFIED MINIMALLY DELAYED OCULOMOTOR RESPONSE (MDOR) TASK
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript is well written and demonstrates the requisite level of expertise and familiarity with the extant oculomotor inhibition literature.  The structure of the manuscript appears to conform to PeerJ standards and figures are relevant, high quality, well labelled and described.  In terms of raw data, I did not view a statemen indicated that values were available in a public archive.
Experimental design: I have a number of questions, comments, concerns about the methods and statistics and present them in detail below.
•	Line 117: The authors indicate that their previous work showed that the general difference between young and older adults was attributed to a “general age-related slowing in the visuomotor system”.  Having read through the manuscript I now understand this was done by subtracting saccades initiated at target onset with MDOR saccades.  That said, a reference at page 117 to Salthouse (1996: Psychol Rev) would be important, as would a description of how slowing with age can be attributed to hardware and/or software changes.
•	Line 123:  The rationale for the study is – in part – attributed to the fact that the authors’ previous work (which did not employ placeholders) was associated with increased spatial uncertainty owing to the lack of extraretinal feedback.  This might be true; however, the authors could have examined the issue by contrasting the variability of endpoints and peak saccade velocity given that the metics represent hallmark features of spatial uncertainty (Edelman and Goldberg 2001: J Neurophsiol).
•	Line 136.  It is not clear why the study employed the same participants from previous work as well as naïve participants.  This rationale needs to be clearly and carefully made.
•	Line 142.  Was a pharmaceutical screening tool used for older (and younger adults)?  This is not a trivial question as an extensive list of pharmaceuticals commonly used in the older adult population decrease oculomotor/information processing speed (for review see, Reilly et a. 2008: Brain Cogn).
•	Lines 173-174.  What does “[…] stepping through it […]” mean?
•	Line 219.  Persons in the age group with a mean age of 65 years are referred to as the “old” group.  The term “older” group is more appropriate.
•	Line 220.  Not all readers will be familiar with the ACE III (MMSE and MoCA are more common) and as such please indicate that all participants scored in the normal range (i.e., did not have clinical or preclinical cognitive decline/disease).
•	Lines 228-245.  This section is overly dense and requires simplification. The section simply needs to state that main effects were observed for group and TDD and their interaction and that in general RTs were shorter for the younger than older group at the 200 and 600 – but not 1000 ms – TDD.  The between-group comparison is more important than the within-group contrast of TDD (i.e., the decrease in RT with increasing TDD can be inferred from Figure 2).  Moreover, effect size measures are reported for between-group comparison but not p-values, whereas p-values and not effect sizes are reported for the within-group comparison of TDD.  Please be consistent.
•	Related to the above, Figure 2a shows overlap between error bars for young and older adults at the 1000 TDD and the page 244 of the manuscript indicates an effect size for this comparison of 0.78.  If I work backwards from the effect size and compute a t-ratio I find a value of 2.88 which would be associated with a p value <.01.  So, it would appear to be a reliable effect based on the effect size; however, the overlap between errors bars by definition demonstrates that the two groups do not reliably differ.  Hence, the authors need to clearly articulate whether groups reliably differed at each TDD.
•	Related to the above, the same issues apply to Figure 2b and the statistics presented for the corrected RTs.
•	I really like the subtractive technique employed by the authors.  I do, however, think It fair that a revision should note that potential pitfall(s) of this Donder’s-based approach (Ulrich et al. Acta Psychologica: 1999).
•	Lines 261-271.  A regression approach, and the use of slopes, to contrast RT and TDD scaling between-groups is interesting.  I would, however, caution using the approach as it is does not appreciably add to the information presented in the previous two paragraphs and does not contain the experimentwise error rate.
•	Line 280.  The results for total error yielded an interaction between group and TDD and the authors report the effect sizes for each between-group comparison of TDD.  The effect size values appear sufficient magnitude to establish a between-group difference at each TDD; however, the Figure 3 shows that error bars for the 200 TDD overlapped between groups.  Hence, did groups differ at this TDD.  This result needs to be clearly articulated.
•	I liked the analyses associated with Figure 4 and appreciate that the associated histograms provided a meaningful overview of the RT and error data.
•	The Discussion is well-written.  If I had one complaint it is that it was very long.  Of course, the authors’ depth of interpretation stands as their own and I leave it to them as to whether they should abbreviate the Discussion.
Validity of the findings: My opinion is that the validity of findings can be rated as "very high".
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: CONFIRMATION OF AGE-RELATED ALTERATIONS IN INHIBITORY CONTROL USING A MODIFIED MINIMALLY DELAYED OCULOMOTOR RESPONSE (MDOR) TASK
Review round: 1
Reviewer: 2

Output:
Basic reporting: The authors presented pretty clear evidence in the introduction that the MDOR task is a better task for studying inhibition compared to antisaccade and memory-dependent saccade tasks. However, I think the amount of focus on comparing the modified and original versions detracts from the investigation of the effects of aging on inhibition. In particular, I think the comparison of the two versions could be dropped since the sample size for participants who completed both is pretty small.
Experimental design: The task schematic and timeline are clear and informative. I do greatly prefer the figures to be embedded in the body of the manuscript, but this might be in line with journal instructions. The distribution plots are useful for visualizing the erroneous and correct responses.

The analysis is very thorough and considers multiple facets of behavior including peak error rate, residual error rate, latencies, and the relationship between errors and prosaccades. Could you just explain how the residual error rate was determined more clearly? I was a bit confused how the bins between -250 and 0 were used. Relatedly, why wasn’t a larger time range used for the long TDD?
Validity of the findings: No comment
Additional comments: In this manuscript, Knox & Liang used a modified minimally delayed oculomotor response (MDOR) task to investigate response inhibition in young and older adults. Older adults made more errors and were slower compared to young adults. An examination of latency distributions suggested that older adults were capable of successfully inhibiting responses but couldn’t maintain the level of control as well as younger adults. The study is well designed and the analyses were thorough. I have some relatively minor suggestions for improvement, but overall saw no major issues with the manuscript.

The authors presented pretty clear evidence in the introduction that the MDOR task is a better task for studying inhibition compared to antisaccade and memory-dependent saccade tasks. However, I think the amount of focus on comparing the modified and original versions detracts from the investigation of the effects of aging on inhibition. In particular, I think the comparison of the two versions could be dropped since the sample size for participants who completed both is pretty small.

The task schematic and timeline are clear and informative. I do greatly prefer the figures to be embedded in the body of the manuscript, but this might be in line with journal instructions. The distribution plots are useful for visualizing the erroneous and correct responses.

The analysis is very thorough and considers multiple facets of behavior including peak error rate, residual error rate, latencies, and the relationship between errors and prosaccades. Could you just explain how the residual error rate was determined more clearly? I was a bit confused how the bins between -250 and 0 were used. Relatedly, why wasn’t a larger time range used for the long TDD?


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: CONFIRMATION OF AGE-RELATED ALTERATIONS IN INHIBITORY CONTROL USING A MODIFIED MINIMALLY DELAYED OCULOMOTOR RESPONSE (MDOR) TASK
Review round: 2
Reviewer: 1

Output:
Basic reporting: Acceptable.
Experimental design: Acceptable.
Validity of the findings: Acceptable.
Additional comments: I found the paper interesting and appreciate the attention to data analyses.  I also found that the authors provided an acceptable revision.  The only comment I reserve is that the term "old" not be used to describe older adults.  This recommendation is based on APA and APS standards.


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: CONFIRMATION OF AGE-RELATED ALTERATIONS IN INHIBITORY CONTROL USING A MODIFIED MINIMALLY DELAYED OCULOMOTOR RESPONSE (MDOR) TASK
Review round: 2
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: no comment - my questions were addressed


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

Input:
Title: EFFECTS OF FRAGRANCE COMPOUNDS ON GROWTH OF THE SILKWORM BOMBYX MORI
Review round: 1
Reviewer: 1

Output:
Basic reporting: This paper from Kai et al is clearly written well.

Authors are investigating the effects of fragrance molecules leaked into the environment on the growth of insects.

About introduction and background, I have one fundamental question about the influence of the fragrances against insects. There are two possible effects of fragrance. The first is that the leaked fragrance molecules disperse in the atmosphere and affect the activity of insects as odors, and as a result, affect the growth of them. The other is that fragrances are accumulated in the diet of each insect such as mulberry for silkworms, and exposure by ingesting fragrance molecules with food affects growth of insects. In this paper, the authors seem to focus on the latter, but when targeting fragrances, it is preferable to also consider and introduce the former's olfactory effects in introduction section.

・In Figure 2, the Musk tibeten sample which is the most difference appears to have a lower resolution than the other photos. In addition to the image like Fig. 2, I think that it will be easier to understand if you describe the difference in growth by comparing weight and body length of larvae. It looks fine in the other figures.

・At line 206, “Musk tibeten, musk xylene, and all of the other aromatic nitro compounds (except musk ketone) do not contain nitro groups,”
I guess “these compounds contain nitro groups” is the right sentence. Authors should check.

Raw data was suppled correctly.
Experimental design: I had the impression that the standard for the amount of fragrance concentration used in both of the acute and chronic conditions was not clear throughout the experiment.

・About feeding experiments, author described that they fed with fragrance solution. The authors describe the exposure amount of Fragrance to silkworms in terms of concentration (ex 1uM), but the effects of Fragrance should also be affect by actual intake. Therefore, the authors should describe in more detail how to feed.

・Also, did the fed of Fragrance change the behavior of silkworms? If silkworm showed repellent reaction against Fragrance and the amount of food is reduced, it should be possible that there is a difference in growth and cocooning simply due to malnutrition.

・About “Larvae that died before pupation were not recorded.”  at Line 116,
Isn't the proportion of larvae that died by fragrance exposure an important factor in this study titled the effects of Fragrance? Is there a difference in the number of Larvae that died before pupation for the control under Fragrance exposure conditions?

・For the effects by Nerolidol, the hormone titer was not different from the control, but the data show that the growth analysis in Fig. 1 and Fig. 3 showed a significant difference from the control. Did Neolidol cause this change by another mechanism different from hormonal pathway? And was this differences an unexpected event? I think it would be good to discuss this consideration in the discussion.
Validity of the findings: The information on fragrance concentration in wastewater mentioned in the conclusion part is quite old as 20 years ago. If you have the current information, I think it would be more realistic to raise your concerns.
Additional comments: It is interesting that this paper examines the effects of fragrance exposure using silkworms as a model insects. There are some questions described below, so I would like you to deepen the discussion.　Comparing the concentration used in the experiment with the actual leakage concentration described in the conclusion section, the current leakage concentration may not immediately affect the ecology of insects. However, there are concerns about the deterioration of environmental pollution in the future.

The fragrance actually used is generally a mixture of a plurality of compounds. Therefore, it is hoped that this discovery will be the basis for future developments in fragrance mixtures and their effects on other insects.


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 FRAGRANCE COMPOUNDS ON GROWTH OF THE SILKWORM BOMBYX MORI
Review round: 1
Reviewer: 2

Output:
Basic reporting: The authors showed growth inhibition of compounds by the photos of larvae which were fed compounds. But resolution of the photos was very low. The photos were without scale bars. It is hard to check the growth effects.
Experimental design: I wonder the authors choose the insect of which the position in the food chain is low and the most habitats are on ground. The authors did not mention about accumulation of fragrance compounds in soils and plants. Therefore, the purpose of this MS is not very clear. Moreover, the authors did not mention the reason for select these compounds which were tested in the MS.
The author measured JH II levels of day 0 5th instar larvae. But JH I is predominant in the silkworm (Niimi and Sakurai, 1998). The should measure JH I, too.
Validity of the findings: The authors concluded that the effect of compounds on JH and 20E levels lead to death. But they did not measure the hormone levels in the larvae which treated with high dose to lead death. The photos of dead larvae is also necessary to show the effect of the compounds. They measure the hormone levels at only one developmental stage. It is not sufficient to discuss the effect of compounds on hormone level to lead the growth rate.
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 FRAGRANCE COMPOUNDS ON GROWTH OF THE SILKWORM BOMBYX MORI
Review round: 1
Reviewer: 3

Output:
Basic reporting: The manuscript investigates “Effects of Fragrance Compounds on Growth of the Silkworm Bombyx mori”. This information is of interest for ecologists who work to protect the environment and entomologists also study urban pests, forest pests, agricultural pests, and merits publication. The experimental setup of this study appears to bewell-designed and the data collected carefully. However, information about the statistical data (P-values, Mean’s t-test comparisons) obtained in the treatments must be provided and detailed in the results section. I think that this manuscript requires rewriting to make its results clearer and more readily interpretable to the reader.
Experimental design: Line 93: Indicate clearly in detail how the steps were taken to solubilize the chemical compounds, for example, how much dimethyl sulfoxide was added, it was necessary to stir or heat to solubilize the compounds used in the study.

Line 176: Clarify which compounds do not show lethal toxicity to B. mori larvae in this study.
Validity of the findings: My specific comments are listed below:
1.  Apart from Vecchiato  (2018), Zhang (2017) Potts (2016) and Rocco ( 2015),  your most recent reference is from 2012. Please cite more current literature from the past five years (2015 to 2020).
2. Line 44: check and confirm; is it 2000, 2018, 2009 or 2000, 2009, 2018... Simonich; Vecchiato; Schiavone...
3. Line 165: check and confirm; Is it abbreviation stands for Lethal toxicity IC50 or LC50.
5. Improve the discussion from the conceptual point of view for acute toxicity.
6. Line 224: Was the experiment carried out just once or was it repeated?
7. Your conclusion needs to be more concise. I suggest moving lines 250-258 for the discussion.
Additional comments: This is good work and an important topic.
The science is good.


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 FRAGRANCE COMPOUNDS ON GROWTH OF THE SILKWORM BOMBYX MORI
Review round: 2
Reviewer: 1

Output:
Basic reporting: In the Revision edition, the authors have described in detail what I was concerned about in the first edition. As a result, I think it became easier to understand the significance of this paper.

There seem to be some typos as below, so please check the entire text again.
L70　favor -> flavor
L172 The results -> These results
Experimental design: no comment
Validity of the findings: no comment
Additional comments: No additional comments


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

Input:
Title: EFFECTS OF FRAGRANCE COMPOUNDS ON GROWTH OF THE SILKWORM BOMBYX MORI
Review round: 2
Reviewer: 2

Output:
Basic reporting: I have read the revised MS. The MS is nearly acceptable for publication. I have only a remaining concern.
 In the response, the authors stated that the measurement of hormones is to explain the effect on growth. But in line 187-188, they hypothesized that hormone levels which affected by some fragrances was leading death. The sentence in line 187-188 make readers to confuse. I think the authors should change it to an appropriate expression.
Experimental design: In Figure 2, it showed that the effect of the fragrances on the growth from day 0 to day 6. The authors mentioned that “Day 0, second instar”. I guess “day 0” in figure2 is day 0 5th instar. Is it correct?
Validity of the findings: I have some comments blow.
Line 26: Please add “(JH)” and “(20-E)” following juvenile hormone and 20-hydroxyecdysone, respectively.

Line 87: Please add space between 24 and h.

Line 91: “Each animal was treated eith …” Is it “with”?

Line 96: What is insect growth? Weight? Body length? Please specify.

Line 360: In figure 4, it is not found “***”. Please remove from figure legend.
Additional comments: This revised MS is well written.
I did not find any serious problem in the MS.


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 FRAGRANCE COMPOUNDS ON GROWTH OF THE SILKWORM BOMBYX MORI
Review round: 2
Reviewer: 3

Output:
Basic reporting: All requests are answered.
Experimental design: All requests are answered.
Validity of the findings: All requests are answered.
Additional comments: This is good work and an important topic. The science is good.