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: ANT MOSAICS IN BORNEAN PRIMARY RAIN FOREST HIGH CANOPY DEPEND ON SPATIAL SCALE, TIME OF DAY, AND SAMPLING METHOD
Review round: 1
Reviewer: 1

Output:
Basic reporting: 1. BASIC REPORTING
Clear, unambiguous, professional English language used throughout. OK
Intro & background to show context. No
Literature well referenced & relevant. No
Structure conforms to PeerJ standard, discipline norm, or improved for clarity.
Figures are relevant, high quality, well labelled & described. Rather No; only one figure which needs to be modified and improved.
Raw data supplied (See PeerJ policy). Yes, but one is not able to be open.
Experimental design: 2. EXPERIMENTAL DESIGN
Original primary research within Scope of the journal. Yes
Research question well defined, relevant & meaningful. It is stated how research fills an identified knowledge gap. Rather No
Rigorous investigation performed to a high technical & ethical standard. Likely, but there are too many problems with Fig. 1 to assert that.
Methods described with sufficient detail & information to replicate. Yes
Validity of the findings: 3. VALIDITY OF THE FINDINGS
Impact and novelty not assessed. Not the case
Negative/inconclusive results accepted. Not the case
Meaningful replication encouraged where rationale & benefit to literature is clearly stated. Not the case
Data is robust, statistically sound, & controlled. Likely Yes, but the problems with Fig. 1 do not permit us to verify this.
Conclusion well stated, linked to original research question & limited to supporting results. No
Speculation is welcome, but should be identified as such. Not the case
Additional comments: Comments concerning the manuscript by Kalsum Yusah, William Foster, Glen Reynolds and Tom M Fayle entitled “Ant mosaics in Bornean rain forest high canopy depend on spatial scale, temporal scale, and sampling methods” (#8574).
The basic results presented in this manuscript likely bring new insights to the knowledge on the distribution of ants associated with emergent trees of an already studied Bornean rainforest and seem very interesting. The use of two techniques (fogging and bating) in the forest canopy permitted the authors to provide some information on their effectiveness; these results are within the scope of the journal PeerJ.
Nevertheless, several important modifications are needed.
The definition of “ant mosaics” is misinterpreted, likely under the influence of several authors working in the Neotropics (but see Ribeiro et al. 2013 cited in the text), and by the last author in Borneo. Furthermore, the bibliography is outdated and very incomplete, so that I provide the authors with a short explanation and several useful references (with the links to permit a new version to be written as quickly as possible). Note that the notion of an ant mosaic has been described in four syntheses (Leston 1973; Majer 1993, Blüthgen & Stork 2007; Dejean et al. 2007), with many explanatory facts and many useful references in the two last papers.

Explanation of what is an “ant mosaic”
The notion of arboreal “ant mosaic” was formulated by Room (1971) (cited in the text) who worked on African cocoa plantations. Meanwhile, several British researchers did the same in different African tree crop plantations (among the most recent, see Jackson 1984). This phenomenon is obvious to observe for two main reasons. (1) All of these plantations were composed of small trees, so that the ant mosaic was “in front of the observers’ eyes”. (2) The “territorially dominant arboreal ant species” (TDA ants), with their huge colonies, are easy to determine as the three main genera, Oecophylla, Tetramorium and Crematogaster, have workers with very typical morphologies. Also, Oecophylla is monospecific, Tetramorium is mostly represented by T. aculeatum, and the workers of the different Crematogaster species are not very similar (at least at the local scale). Furthermore, the nests of these ant species are very different from each other, rendering the identification of the different Crematogaster species easy. Voucher specimens of these ant species were deposited in the Museum of Natural History, and Brian Taylor and Barry Bolton (both systematicians) helped ecolo-agronomists when necessary.
Among these researchers, Bigger (1993) showed that conspecific trees of different ages sheltered different dominant ant species (introducing the idea of ontogeny; see Dejean et al. 2016 and papers cited therein). Also, the biology, behavior and ecology of many of these TDA ant species have been studied by different authors, more particularly their territoriality (markings that persist several years: Hölldobler & Wilson 1978; Beugnon & Dejean 1992; Offenberg 2007) and nest site selection (Djiéto & Dejean 1999). Ant mosaics exist in plantations (i.e., presented by Leston in 1973; see also Majer et al. 1994), forest edges, and secondary and old forests (see Blüthgen & Stork 2007; Davidson et al. 2007; Dejean et al. 2007, 2015; Ribeiro et al. 2013).
Note that arboreal ant mosaics exist in Bornean forests (see Davidson et al. 2007) with the fantastic nocturnal, giant ant species Camponotus gigas whose nests are at ground level so that the workers need to climb up the 60-m tall trunks of dipterocarps to forage in their crowns; also, they are territorial (see Pfeiffer & Linsermair 1998, 2001).
Because the authors worked on several ant species able to share a territory with a TDA ant species, they need to state precisely what species are numerically dominant with the aim of detecting territorially dominant species (see definitions in Davidson 1998). “Co-dominant” species can be determined through comparisons, and “non-dominant” species are generally the remaining species with comparatively small colonies. Note that co-dominants correspond frequently to a nocturnal and a diurnal species sharing one or several adjacent tree crown(s) over the nycthemeron (details in Dejean et al. 2007); for example, this is the case for trees N°4, 15 and 17 in “baiting” (Fig.1G and 1H) where the nocturnal species Camponotus gigas is involved.

Comments directly concerning the manuscript
Introduction
This section needs to be entirely rewritten.
- Lines 42-50. It would be better to present the true objectives of the study (i.e., related to two kinds of comparisons: during the daytime, fogging versus baiting; baiting diurnally versus at night) before presenting the seminal studies by Nicholas Gotelli. The relationship between these objectives and the notion of ant mosaics can be presented after along with the definition of arboreal ant mosaics. More importantly, the authors need to define what are territorially dominant ant species and co-dominant species (the latter, for example, because of the presence of the nocturnal Camponotus gigas).
- Lines 51-55. The notion of competition likely misled the authors because ant mosaics are the result of the territoriality of the TDA ant species. The reactions which trigger territoriality here are related to the colony closure, and so, to colony mate recognition. Discrimining colony mates from aliens is based on the comparison of the cuticular hydrocarbons of members of the colony (i.e., these hydrocarbons make up the colony odor which serves as a “template”) with those of encountered ants, a mismatch usually results in aggressiveness (see the synthesis by Bos & d’Ettore 2012).
- Line 59, Dejean & Corbara (2003) is outdated; rather cite Blüthgen & Stork (2007) and/or Dejean et al. (2007).
- Line 61. “Thus it is “possible” ….. This part needs to be entirely rewritten.
- Lines 69-71. “However, their presence in undisturbed tropical forests remains contentious, with ant species being found to be segregated in some studies (e.g. Ribeiro et al. 2013) but not others (Fayle et al. 2013; Floren & Linsenmair 2000)”. This sentence presents flagrant untruths. (1) Several papers other than Ribeiro et al. (2013) deal with the presence of an ant mosaic in old forests (see Dejean et al. 2007 and papers cited therein; Blüthgen & Stork 2007, which is cited in the present manuscript; Davidson et al. 2007 presenting a study conducted in a Bornean forest; Dejean et al. 2015, 2016 for studies conducted in Africa). (2) The paper by Floren & Linsenmair (2000) needs to be read, not only the title, because these authors worked in the lower canopy where they did not find a mosaic as did Ribeiro et al. (2013), so that these two papers are congruent (i.e., they cannot be placed in opposition); Blüthgen & Stork (2007) also showed that the presence of an ant mosaic depends on the stratum studied (absent from the lower canopy). Concerning the paper by Fayle et al. (2013), which is very interesting overall, the approach using separate trees cannot really permit the detection of an ant mosaic (even if the model permits one to see an effect in plantations through the relationships between ants and an epiphytic fern).
- Lines 72-75. Contrarily to what is asserted, fogging can permit to show the presence of a mosaic, but on the condition that the authors work on numerous, adjacent trees (see Watt et al. 2003; Blüthgen & Stork 2007). Working on a small number of distant trees is another approach which is particularly useful for studying ant species diversity, the relationships between a tree species and arboreal ants etc.
Note that when fogging is conducted along a transect, when it reaches the territory of TD ant species “A”, a rain shower of numbed “A” workers falls to on the ground under several trees until the fogging reaches the territory of species “B”, etc. So, the objectives of working on isolated trees are very different from those of working along a transect.

Materials and Methods
- Line 95. Everyone working in tropical forests can easily obtain the identification of at least the emergent species; this is likely the case for the genus Parashorea in a Bornean dipterocarp rainforest. The species name might be useful for certain readers (i.e., congeneric trees of different species can attract ant queens and workers from different species, the resulting nest-site selection can therefore influence the ant mosaic).
- Lines 112-115. It is a shame that at least the most frequent dominant ant species were not identified to species level. This was likely possible for Tetramorium sp.2 (using the collections of the Museum of Natural History, London); the same is true for Myrmicaria spp. and maybe for certain Vollenhovia species (likely deposited in German collections and/or the Museums of Los Angeles, San Francisco and Harvard).
- Lines 122-123. The first Supplemental Appendix is not lisible.

Results
- Fig. 1 needs to be clarified: (1) several colors representing ant species presented in the reference grids appear as a nuance of grey in the figure itself; (2) the colors representing the same ant species through baiting and fogging need to be the same. In other words, to present only one reference grid with the numerically dominant species easily distinguishable from each other at a glance is strongly needed (this is less important for the other species). Some of the colors in Fig. 1 are not represented in the reference grid (ex. the yellow from trees 5 and 15 in Fig. 1G differs from that concerning Polyrhachis ypsilon, but is rather similar to that of Dolichoderus sp. 7 from the reference grid in Fig. 1I)
- I therefore suggest that the authors thoroughly verify all correspondences between the colors selected and the ant species. I indeed suspect some mistakes in the Fig. 1 presented here.
- Readers need to be absolutely sure that the trees examined through baiting (Fig 1D & H) are exactly the same as those examined through fogging (Fig. 1I), and that the sequences of 20 trees in both cases are exactly the same (i.e., tree N° 1 in baiting is also tree N°1 in fogging etc.). This is likely the case but see the last comment above (I suspect some mistakes). If not, this needs to be stated in the Materials and Methods.
- If the sequence of trees is the same, it would be better to present “fogging” first (so, Fig. 1I) and then “baiting” (so, Fig. 1G and then Fig. 1H) and, of course, to change the codes for the figures. Consequently, baiting diurnally will become the reference for both fogging (also occurred diurnally) and baiting nocturnally, something facilitating comparisons in the new Fig. 1.
- Comparison between fogging and baiting (diurnally). It is normal that fogging resulted in many more ant species per tree than baiting. Fogging kills workers of all ant species occurring in the zone of the tree crown treated, while baiting selects (1) species attracted by the baits, and (2) among them, those that arrive first or those that have excluded the other species. Therefore, comparing fogging and baiting on the same tree crowns (diurnally) is interesting as it can permit to determine, among numerically dominant species, those which have the skill to eliminate competitors from the baits (i.e., likely the most territorial). Yet the fact that many colors are replaced by nuances of grey plus others that do not exist in the reference grid renders this comparison difficult in the current Fig. 1.
- Comparison between baiting diurnally and at night. Baiting diurnally (Figs. 1A, 1G) illustrates the presence of numerically dominant species on each tree (we cannot say that they are “territorial” without a specific study on each species). That the model does not show a significant difference for individual trees is not a problem (if we take the reasoning further, only one TDA ant species can occupy an entire tree crown which is in accordance with the notion of an ant mosaic; the case for tree N°9). The comparison with baiting diurnally and baiting at night (Figs. 1B, 1H) is interesting. For example, tree N°4 was occupied by two co-dominant species: Vollenhovia sp.2 was dominant both day and night in trees N°6, 7, and 9, while it was present diurnally in tree N°4 and pushed away from the baits at night by the nocturnal Camponotus gigas. In tree N°19 Tetramorium sp.2 is replaced at night by Camponotus sp.19, but here it is possible that the former is diurnal, the latter nocturnal (so the interest of identifying the ants to species level because the biology of many of them has been studied by German and American researchers).

Discussion
- Lines 166-192. The Discussion, is based from the start on the idea that mosaics do not exist in tropical rainforest canopies, but this is not the case, so that this part needs to be deleted or, maybe, rewritten based on the information I provided above.
- Lines 193-210. This study rather deals with (1) the comparison of two techniques (during the daytime) and (2) one technique (during the daytime and at night). The Discussion needs to concentrate first on the interests of these comparisons in greater depth than currently presented.
The indirect advantage of the results acquired through these techniques can then be presented in light of the notion of ant mosaics. This implies that the authors thoroughly verify that the colors in Fig. 1 correspond to the different ant species they recorded. The comparison between diurnal fogging and baiting will likely provide information on what species dominate the others at baits among those the most represented during fogging (i.e., numerically dominant species).

In conclusion
I followed to the letter the instructions concerning reviewing a manuscript for the journal PeerJ, so that I tried to provide the authors with information permitting them to submit a new version of their manuscript that is in accordance with their true aim and with a correspondence between the latter and the notion of ant mosaics.
The core results of this study are likely much more interesting than the authors realise. They need to rethink Fig. 1 and verify that the different ant species represented are really those observed during the study (i.e., a thorough check is necessary).
The Introduction and the Discussion need to be entirely rewritten. With only 20 trees isolated from each other, an ant mosaic is possible to be suspected, but this needs to be explained based on the results (see above). Indeed, the authors rather showed the presence of numerically dominant species, the existence of co-dominant species sharing the same territory (one during the day the other at night), that one species can exclude another diurnal species at baits during the night, etc. The comparison between fogging and baiting (during the daytime) could permit them to show the domination at the baits by certain species (but Fig. 1 with the same colors both in the PDF and in the Microsoft Office Picture Manager needs to be improved to permit readers to really understand).

References cited (with online links except for Leston 1973; I added Blüthgen & Stork 2007 as I am not sure that all of the authors have read it).
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Bigger M 1993. Ant-hemipteran interactions in a tropical ecosystem. Description of an experiment on cocoa in Ghana. Bulletin of Entomological Research 83: 475–505. https://www.researchgate.net/publication/231887655_Ant_-_homopteran_interactions_in_a_tropical_ecosystem_Description_of_an_experiment_on_cocoa_in_Ghana
Blüthgen N, Stork NE 2007. Ant mosaics in a tropical rainforest in Australia and elsewhere: a critical review. Aust Ecol 32:93–104. http://onlinelibrary.wiley.com/doi/10.1111/j.1442-9993.2007.01744.x/pdf
Bos N & d’Ettorre P 2012. Recognition of social identity in ants. Frontiers in Psychology 3: 83. http://www.ncbi.nlm.nih.gov/pmc/articles/PMC3309994/pdf/fpsyg-03-00083.pdf
Brühl CA, Gunsalam G, Linsenmair KE 1998. Stratification of ants (Hymenoptera, Formicidae) in a primary rain forest in Sabah, Borneo. Journal of Tropical Ecology 14: 285–297. http://journals.cambridge.org/download.php?file=%2F9022_7BA66FE54764E52B55F8A0213E95C87B_journals__TRO_TRO14_03_S0266467498000224a.pdf&cover=Y&code=87b4de4d79ce57bd329e7a33e0a9df0e
Davidson DW 1998. Resource discovery versus resource domination in ants: A functional mechanism for breaking the trade off. Ecological Entomology 23: 484–490. http://onlinelibrary.wiley.com/doi/10.1046/j.1365-2311.1998.00145.x/pdf
Davidson DW, Lessard J-P, Bernau CR, Cook SC 2007. Tropical ant mosaic in a primary Bornean Rain Forest. Biotropica 39: 468–475. http://onlinelibrary.wiley.com/doi/10.1111/j.1744-7429.2007.00304.x/pdf
Dejean A, Azémar F, Céréghino R, Leponce M, Compin A, Corbara B, Orivel J & Compin A 2016. The dynamics of ant mosaics in tropical rainforests characterized using the Self-Organizing Map algorithm. Insect Science DOI: 10.1111/1744-7917.12208. http://www.academia.edu/12887808/The_dynamics_of_ant_mosaics_in_tropical_rainforests_characterized_using_the_Self-Organizing_Map_algorithm
Dejean A., Ryder S., Bolton B., Compin A., Leponce M., Azémar F., Céréghino R., Orivel, J., Corbara B. 2015. How territoriality and host-tree taxa determine the structure of ant mosaics. The Science of Nature 102: 33. http://download.springer.com/static/pdf/936/art%253A10.1007%252Fs00114-015-1282-7.pdf?originUrl=http%3A%2F%2Flink.springer.com%2Farticle%2F10.1007%2Fs00114-015-1282-7&token2=exp=1454351993~acl=%2Fstatic%2Fpdf%2F936%2Fart%25253A10.1007%25252Fs00114-015-1282-7.pdf%3ForiginUrl%3Dhttp%253A%252F%252Flink.springer.com%252Farticle%252F10.1007%252Fs00114-015-1282-7*~hmac=1b848028f339748bb0cc4c30c501e9922c6025ae04a057e2a9c0f4cbbe5a7c9c
Dejean A, Corbara B, Orivel J, Leponce M 2007. Rainforest canopy ants: the implications of territoriality and predatory behavior. Functional Ecosystems and Communities 1: 105–120. http://www.globalsciencebooks.info/Online/GSBOnline/images/0712/FEC_1%282%29/FEC_1%282%29105-120o.pdf
Djiéto-Lordon C, Dejean A 1999a. Tropical arboreal ant mosaic: innate attraction and imprinting determine nesting site selection in dominant ants. Behavioral Ecology and Sociobiology 45: 219–225. http://download.springer.com/static/pdf/131/art%253A10.1007%252Fs002650050556.pdf?originUrl=http%3A%2F%2Flink.springer.com%2Farticle%2F10.1007%2Fs002650050556&token2=exp=1454353055~acl=%2Fstatic%2Fpdf%2F131%2Fart%25253A10.1007%25252Fs002650050556.pdf%3ForiginUrl%3Dhttp%253A%252F%252Flink.springer.com%252Farticle%252F10.1007%252Fs002650050556*~hmac=443f826d6f1da9be8eaa518d0d8b0db1076a770d4712ce7f5f30573fe9d22e02
Djiéto-Lordon C, Dejean A 1999b. Innate attraction supplants experience during host plant selection in an obligate plant-ant. Behavioural Processes 46: 181–187. http://ac.els-cdn.com/S0376635799000327/1-s2.0-S0376635799000327-main.pdf?_tid=085e5d8c-c913-11e5-a2bc-00000aab0f6c&acdnat=1454352108_ccd4ac0c8187a047f20dff11106e7d95
Hölldobler B, Wilson EO 1977. Colony-specific territorial pheromone in the African weaver ant Oecophylla longinoda (Latreille). PNAS 74: 2072–2075. http://www.pnas.org/content/74/5/2072.full.pdf
Jackson DA 1984. Ant distribution patterns in a Cameroonian cocoa plantation: investigation of the ant-mosaic hypothesis. Oecologia 62: 318–324. http://download.springer.com/static/pdf/822/art%253A10.1007%252FBF00384263.pdf?originUrl=http%3A%2F%2Flink.springer.com%2Farticle%2F10.1007%2FBF00384263&token2=exp=1454353271~acl=%2Fstatic%2Fpdf%2F822%2Fart%25253A10.1007%25252FBF00384263.pdf%3ForiginUrl%3Dhttp%253A%252F%252Flink.springer.com%252Farticle%252F10.1007%252FBF00384263*~hmac=74207aba82b785cfe88d08264e8b3b676fd4f784ac51ac67adf0acf00d66eb68
Leston D 1973. The ant mosaic, tropical tree crops and the limiting of pests and diseases. Pest Articles and News Summaries 19: 311–341. https://www.researchgate.net/publication/248979758_The_Ant_Mosaic_-_Tropical_Tree_Crops_and_the_Limiting_of_Pests_and_Diseases
Majer JD 1993. Comparison of the arboreal ant mosaic in Ghana, Brasil, Papua New Guinea and Australia: its structure and influence of ant diversity. In: LaSalle J, Gauld ID (eds) Hymenoptera and Biodiversity, CAB International, Wallingford, UK, pp 115–141.
Majer J, Delabie JHC, Smith RB 1994. Arboreal ant community patterns in Brazilian cocoa farms. Biotropica 26: 73–83. http://www.sidalc.net/repdoc/a3636i/a3636i.pdf
Offenberg J 2007. The distribution of weaver ant pheromones on host trees. Insectes Sociaux 54: 248–250. http://www.biologie.uni-ulm.de/antnet/pdf/offenberg-2007.pdf
Pfeiffer M, Linsenmair KE 1998. Polydomy and the organization of foraging in a colony of the Malaysian giant ant Camponotus gigas (Hym./Form.). Oecologia 117: 579–590. http://www.antbase.net/pdf/pfeiffer-1998.pdf
Pfeiffer M, Linsenmair KE 2001. Territoriality in the Malaysian giant ant Camponotus gigas (Hymenoptera/Formicidae). Journal of Ethology 19: 75-85. http://download.springer.com/static/pdf/410/art%253A10.1007%252Fs101640170002.pdf?originUrl=http%3A%2F%2Flink.springer.com%2Farticle%2F10.1007%2Fs101640170002&token2=exp=1454363869~acl=%2Fstatic%2Fpdf%2F410%2Fart%25253A10.1007%25252Fs101640170002.pdf%3ForiginUrl%3Dhttp%253A%252F%252Flink.springer.com%252Farticle%252F10.1007%252Fs101640170002*~hmac=6273a28a4fed4db5229746d56d743d42672bfb2344d146b9e12abf891c086938
Room PM 1971. The relative distribution of ant species in Ghana's cocoa farms. Journal of Animal Ecology 40: 735–751. http://www.jstor.org/stable/3447?seq=1#page_scan_tab_contents
Schulz A, Wagner T 2002. Influence of forest type and tree species on canopy ants (Hymenoptera: Formicidae) in the Budongo Forest Reserve, Uganda. Oecologia 133: 224–232. http://download.springer.com/static/pdf/212/art%253A10.1007%252Fs00442-002-1010-9.pdf?originUrl=http%3A%2F%2Flink.springer.com%2Farticle%2F10.1007%2Fs00442-002-1010-9&token2=exp=1454353668~acl=%2Fstatic%2Fpdf%2F212%2Fart%25253A10.1007%25252Fs00442-002-1010-9.pdf%3ForiginUrl%3Dhttp%253A%252F%252Flink.springer.com%252Farticle%252F10.1007%252Fs00442-002-1010-9*~hmac=c8ddb54646c191369135f2047c54ad22194b2bd31209b71bc1cf3bafa204e880
Watt AD, Stork NE, Bolton B 2002. The diversity and abundance of ants in relation to forest disturbance and plantation establishment in southern Cameroon. Journal of Applied Ecology 39: 985–998. http://onlinelibrary.wiley.com/doi/10.1046/j.1365-2664.2002.00699.x/pdf


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: ANT MOSAICS IN BORNEAN PRIMARY RAIN FOREST HIGH CANOPY DEPEND ON SPATIAL SCALE, TIME OF DAY, AND SAMPLING METHOD
Review round: 1
Reviewer: 2

Output:
Basic reporting: Line 58 I would specify ‘tropical’ canopies as arboreal ants are not generally abundant enough in temperate canopies for mosaics to form.

The section at lines 72-74 needs to be recast along the following lines:
•	Mosaics have frequently been demonstrated in plantations;
•	Floren & Linsenmair 2000 suggested that they do not exist in forest canopies, but their sampling was in lower canopy;
•	Rebeiro et al. 2013 sampled the canopy in Panama from above and found strong evidence of a mosaic;
•	Rebeiro’s data was tentative as it was from a short-term study;
•	However, Dejean et al 2015 (an important paper that has not been cited), working in Gabon and also sampling the canopy from above, provided a more substantial data set that demonstrated the existence of a mosaic.

Alain Dejean, Suzanne Ryder, Barry Bolton, Arthur Compin,
Maurice Leponce, Frédéric Azémar, Régis Céréghino, Jérôme Orivel,
Bruno Corbara (2015) How territoriality and host-tree taxa determine the structure
of ant mosaics. Sci Nat (2015) 102:3 DOI 10.1007/s00114-015-1282-7

I believe that it is essential to take this approach to the lead in, as the story about mosaics in upper canopy has already started to unfold, and this manuscript is building upon these findings, not discovering them.

Line 174. I disagree with this statement. Surely, the fact is that your findings confirm that Rebeiro et al. and Dejean et al. are correct in suggesting that there is a mosaic in the upper canopy and that Floren and Linsenmair and Fayle et al. were probably incorrect in suggesting that it does not exist there. Floren and Linsemair’s sampling was NOT a representation of what is found in the upper canopy as they approached the canopy from beneath and did not reach the highly insolated upper layers of the canopy.

Figure 2 I don’t know if this is a problem with my computer alone, but many of the bars on the histograms are in various shades of grey, not the colours indicated by the keys.
Experimental design: Line 100 This paragraph should mention the sampling dates as there is a degree of seasonal variation in canopy ant activity, even in the tropics. Also, mention that fogging was (presumably) performed after the trees were baited.
Validity of the findings: Line 212. The lack of segregation within trees during the day is an intriguing matter. However, the analysis does not distinguish between dominant and non-dominant species. The mention of Camponotus gigas is of note, but were correspondingly abundant ants from other species not abundant in the day? Might it not be worth mentioning somewhere which of the sampled species are likely to be dominant species?
Additional comments: Although the findings in this ms are valid, the emphasis needs to be changed in part of the Introduction and again in the Discussion. The finding of a mosaic in the upper canopy of rainforest is no longer novel, although this ms is refining what we know about mosaics in the is stratum of the forest.

I believe that the emphasis of the ms should be changed to reflect the fact that we now know that mosaics do exist in the upper canopy and that this ms sets out to provide further information on the interactions that exist in such areas.


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: ANT MOSAICS IN BORNEAN PRIMARY RAIN FOREST HIGH CANOPY DEPEND ON SPATIAL SCALE, TIME OF DAY, AND SAMPLING METHOD
Review round: 2
Reviewer: 1

Output:
Basic reporting: 1. Basic reporting

The manuscript by Kalsum M. Yusah et al. entitled “Ant mosaics in Bornean rain forest high canopy depend on spatial scale, time of the day, and sampling” is original because it deals with emergent trees of the Bornean rainforest and their relationships with ants. This approach, to the best of my knowledge, has not previously been used by researchers working on ant distribution in tropical rainforests.
The authors used a double, complementary methodology to conduct this study. First, only during the daytime, fogging was limited to the level of the tree crown (to catch ants from this area and not an entire vertical column as in many other studies for which this technique was used). This approach thus permits to have an ‘image’ of what ant species are active when the insecticide is itself active. Second, both during the daytime and at night, baiting was used permitting the authors to gather ant species during these two periods of the nychthemeron, and thus, ant species that were present on the baits when the baits were collected. Indeed, depending on their rhythm of activity and hierarchical position, different ant species succeed one another on the baits, certain ant species being fast at discovering a bait, but others displace them to occupy these baits (i.e., opportunists versus extirpators).
Therefore, the authors obtained precise information on the activity of ants from emergent tree crowns in the very interesting context of the Bornean rainforest.
Because the approach is very, very interesting and original, the experiment apparently well conducted as are the statistics, the rest of my comments will be aimed at improving the presentation of the core results keeping in mind that ants are social insects as I did in my comments concerning the former manuscript. Furthermore, the base study is likely much more interesting than the authors may have expected because in Bornean rainforests one of the dominant ant species is Dinomyrmex gigas whose colonies are ground nesting and polydomous, and the workers, among the biggest in the world, tend hemiperans only at night. Yet, I cannot be very helpful on this subject as the colors in Fig. 2 did not permit me to distinguish this species from four others.
Indeed, although it is not obligatory to present that in detail, the approach chosen by the authors needs to take into consideration nest site selection, polyethism, rhythm of activity, nestmate recruitment and interspecific competition particularly at baits. For the latter case I suggest the authors read papers on ground-foraging ants, including invasive species as this will permit them to “see” that several ant species succeed one another at baits.
Another suggestion: modify the title. I am not sure that the authors really adhere to the concept of ‘ant mosaics’ that deals with the territoriality of ‘territorially dominant arboreal ant species’, and so the distribution of their territories in the forest canopy. Here, the key words are rather ‘emergent tree crowns’, ‘numerically dominant species’, ‘rhythm of activity’, and, indirectly, ‘interspecific competition’.

Thus, this new version of the manuscript is much more elaborated than the previous. Only some modifications are needed to improve it and, in my opinion, the core results can permit the authors to present a much more interesting manuscript than they may think. It is a shame that Fig. 2 does not allow readers to distinguish Dinomyrmex gigas from four other ants species, so that I cannot help the authors in the presentation of the impact of this ant species.
Experimental design: 2. Experimental design

The experimental design is fine on the condition that the authors admit that they did not really work on ‘ant mosaics’. I suggest that they read papers by British researchers working on cocoa plantation with shade trees, a situation that presents some similarities with emergent trees above the forest canopy (see details below). They will see that the ‘ant mosaic’ in the cocoa canopy is influenced by the presence of the ‘tall’ shade trees because certain ant species (of the genus Crematogaster) rather nest in their crowns and occupy the crowns of the cocoa trees surrounding them.
Also, the statistical approach is fine (I asked a specialist to verify that in detail for the first review). Indeed, in a few papers dealing with ant mosaics, the authors mistakenly used a wrong approach, so that they found an absence of ant mosaic where it was obviously present. This is presented in Blüthgen and Stork (2007) and Dejean et al. (2007). I therefore suggest that the authors delete the citation for Sanders et al. (2007) who used this wrong approach (see lines 62, 67, 386) in order to avoid mistakes by readers. Yet, the authors need to remember that they did not work directly on an ant mosaic (and their core results are interesting).
Validity of the findings: 3. Validity of the findings

The core findings are very interesting as explained in the general comments. Only ‘cosmetic’ modifications to the text are needed, although relatively numerous.
Additional comments: General comments for the author

In this part, I shall try to help the authors to write a definitive version of their manuscript.
Before all, I suggest that the authors re-read the main comment I made in the previous review: “The definition of “ant mosaics” is misinterpreted, likely under the influence of several authors working in the Neotropics (but see Ribeiro et al. 2013 cited in the text), and by the last author in Borneo. Furthermore, the bibliography is outdated and very incomplete, so that I provide the authors with a short explanation and several useful references (with the links to permit a new version to be written as quickly as possible). Note that the notion of an ant mosaic has been described in four syntheses (Leston 1973; Majer 1993, Blüthgen & Stork 2007; Dejean et al. 2007), with many explanatory facts and many useful references in the two last papers.”
Although this new version of the manuscript needs only cosmetic changes, the authors will understand why I suggest rewriting the title and modifying several parts of the text (see Abstract / Discussion: lines 38-40).

Abstract
The abstract and different parts in the text: avoid the word “recently” when you cite papers more than 1-year old (and particularly when they are 10 to17 years-old, see below). See lines 23, 54, 73.

Lines 22-23. It is likely that the paper by Dejean et al. 2000 was the first that was conducted on a pristine forest; Nico Blüthgen published a paper shortly after (Blüthgen et al. 2004), the Diane Davidson (Davidson et al. 2007; both are cited in the text). So, reconsider this sentence.
Dejean A., McKey D., Gibernau M. & Belin-Depoux M. 2000. The arboreal ant mosaic in a Cameroonian rainforest. Sociobiology 35: 403-423.

Introduction

Lines 82-88. Better to delete this part. Indeed, ant mosaics deal with territories, so the latter need to be delimited. The other approaches are interesting, but in certain cases do not deal really with ant mosaics (see the part in green above). I suggest that the paragraph lines 82-97 be slightly modified to present the different approaches permitting readers to understand how ants are distributed in the rainforest canopies (no more).
All throughout the text, enter Dinomyrmex gigas rather than Camponotus gigas (see Ward et al. 2016).
Ward P.S., Blaimer B.B., Fisher B.L. 2016. A revised phylogenetic classification of the ant subfamily Formicinae (Hymenoptera: Formicidae), with resurrection of the genera Colobopsis and Dinomyrmex. Zootaxa 4072: 343-357.

I suggest that the authors first revise their Fig. 2 to permit readers to distinguish Dinomyrmex gigas from Crematogaster difformis, Dolichoderus magnipastor, Plagiolepis sp.1 and Crematogaster sp.5.
If Dinomyrmex gigas appears only in a very few situations (likely during the nighttime), I suggest that the authors write a small paragraph on this ant species (see papers by Martin Pfeiffer below). If Dinomyrmex gigas is well represented, I suggest that the authors write a specific paragraph on the originality of the situation as workers of this species climb up these very tall trees each night to tend hemipterans. Thus, these hemipterans are tended by other ant species during the daytime. Therefore, Dinomyrmex gigas plays a major role in the nocturnal hierarchy of ant species (an allusion to the notion of ant mosaic can be made, but cautiously).
Pfeiffer M., Linsenmair K.E. 1998. Polydomy and the organization of foraging in a colony of the Malaysian giant ant Camponotus gigas (Hym. - Form.). Oecologia 117: 579-590. (directly available online: https://www.researchgate.net/publication/235684413_Polydomy_and_organization_of_foraging_in_Camponotus_gigas)
Pfeiffer M., Linsenmair K.E. 2000. Contributions to the life history of the Malaysian giant ant Camponotus gigas (Hymenoptera - Formicidae). Insectes Sociaux 47: 123-132. (directly available online: http://www.biologie.uni-ulm.de/antnet/pdf/pfeiffer-2000.pdf)
Pfeiffer M., Linsenmair K.E. 2001. Territoriality in the Malaysian giant ant Camponotus gigas (Hymenoptera/Formicidae). Journal of Ethology 19: 75-85. (directly available online: http://systax-vm4.biologie.uni-ulm.de/pdf/pfeiffer-2001.pdf)
Pfeiffer M., Linsenmair K.E. 2007. Trophobiosis in a tropical rainforest on Borneo: Giant ants Camponotus gigas (Hymenoptera: Formicidae) herd wax cicadas Bythopsyrna circulata (Auchenorrhyncha: Flatidae). Asian Myrmecology, 1, 105–119. (directly available online: http://www.asian-myrmecology.org/publications/pfeiffer-linsenmair-am-01-10.pdf)

Materials and Methods
First paragraph: please provide the size of the canopy trees and that of the emergent trees on which you worked to permit readers to visualize the situation (and consider at its true value the work undertaken to conduct this study).

Lines 117-118. ’(although given the lack of connectivity, it seems unlikely that these territories often extended to other trees)‘ I suggest deleting this part as it is a supposition (i.e., speculative). If we refer to shade trees in cocoa plantations, so a situation presenting some similarities with emergent trees and the rest of the rainforest canopy, one can see that some ant species nest specifically in shade trees, influencing the mosaic in the cocoa plantations around these trees (Majer 1976; there are other studies showing this situation such as those by Brian Taylor).
Majer J.D. 1976. The ant mosaic in Ghana cocoa farms: further structural considerations. Journal of Applied Ecology 13: 145–156. (directly available online: https://www.jstor.org/stable/pdf/2401934.pdf?refreqid=excelsior%3Ac4a1186a80f06e4a38bdca8fb50df792)
See Figure in Brian Taylor (The ants of Africa; Chapter 3) illustrating directly the importance of shade trees in cocoa plantations: http://antsofafrica.org/ant_species_2012/mosaics9.htm

Results
Daytime. The authors need to keep in mind that fogging and baiting are two complementary techniques. It is therefore normal that differences occurred. As said above, the fogging gave an ‘instantaneous image’ of what ant species were active during the short period of time of the action of the insecticide, whereas baiting showed what ant species were exploiting the bait when the bait was verified by the authors. So, if the period of time is short, the bait permits researchers to gather ‘opportunist species’ whose workers quickly locate recently placed baits and recruit nestmates. They are generally very timid and abandon the baits when workers of more aggressive species, or extirpators, arrive. Combats can occur between successive extirpator species (this is described in Hölldobler & Wilson 1990, cited in the text).
Thus, placing baits once during daytime and once at night is interesting but the information provided is relatively limited as it likely captures different scenarios. The whole, in addition to fogging, gives a relatively good idea of the ant species diversity, but less of the ant mosaic itself. Yet, through the statistical approach, the authors, interestingly, show that some species are numerically dominant in certain situations, but not in the others (particularly, the difference between daytime and night using baits). Due to the peculiarity of Dinomyrmex gigas, I suggest that the authors develop more the fact that this species was present at night on 14 trees out of 20 (see lines 194-195 and then 198-200).

Lines 195-201. It is frequent that tree crowns are shared by a diurnal and a nocturnal species, both being dominant, but with different rhythms of activity (they were called ‘co-dominant species’ by Majer 1976; see also more citations in Dejean et al. 2007 cited in your manuscript). I therefore suggest deleting lines 196-197 ‘a lower degree of turnover than that found between 197 baiting and fogging during the day’, something that corresponds to two different approaches.

Discussion
I suggest modifying or deleting the first paragraph of the Discusion (lines 212-218) as it seems to be a kind of mea culpa by Tom Fayle, whereas lines 260-263 explain very, very well the situation. Furthermore, the authors need to remember that they only indirectly worked on an ant mosaic. Better to explain why the results obtained can be correlated to the notion of ‘ant mosaics’ in a short sentence (not obligatory, of course).
Alternatively, the Discussion can begin with the paragraph in lines 219-231. Furthermore, I urge the authors to complete this paragraph with information on Dinomyrmex gigas present at night on 14 out of 20 trees.
Also, because the paper by Davidson et al. (2007) dealing with ants of the rainforest canopy of Brunei is cited, I suggest that the authors write a small paragraph on the strong difference between the dominant ant species they noted and those recorded by Diane Davidson. For example, they did not record Oecophylla smaragdina (a typical territorially dominant arboreal ant species) whereas Diane Davidson did not record Dinomyrmex gigas (but she noted this species during other studies).

Line 232. ‘The robustness of patterns of segregation to the sampling methods employed might be because dominant ants are those that are both highly abundant in general’ for me, it is not ‘might be’ but rather ‘is due to’.

Line 234. As I wrote above, it is normal that the two sampling methods result in different percentages of ant species (or different ant species) as they select for different ant species. So, better to explain that difference in the Materials and Methods and here to comment on the complementarity of the two methods.

Lines 237-240. There is ONE ant mosaic in the canopy of the forest, not in one isolated tree (i.e. one tree is only part of the mosaic if the ant mosaic exists, something needing to be proven). I suggest that you delete this paragraph rather than to bother writing a new one.

Line 240-243. It is normal that no ant species totally dominates the tree crowns (i.e, not the canopy; you did not work on it) as you gathered both dominant species and the non-dominant they tolerate. So, better to delete this part and to adapt the following paragraph on Vollenhovia (nota: I hope that you sent specimens to well known taxonomists such as Barry Bolton and Brian Fisher as it remains possible that this myrmicine species is a territorially dominant arboreal species with large polydomous colonies).

Lines 252-265. I suggest that you simplify this paragraph in lines 260-263 whose meaning is clear. Maybe, it can be placed elsewhere in the text (so permitting to delete the rest). Anyway, lines 264-265 can be questioned as Dinomyrmex gigas workers climb up the trees each night to attend hemipterans in the crown.

Lines 269-271. It is easy to verify in your data if the dominant species differed between trees, so that I suggest deleting ‘might be’ by ‘was’ after verification.

Lines 271-274. Better to delete this paragraph as differences between methods during the daytime will be already explained in your next version of the manuscript, whereas differences in baiting between day and night are due to different rhythms of activity. The same for lines 275-279, even if temperature also plays a role (note that certain arboreal ants are active at night only during a few hours). Your work is interesting, this is why I suggest to avoid speculations and ways to shorten the text.

Lines 280-286 also can be deleted or adapted.

Line 288 needs to be modified. Yours results indicate that dominant ants are present in the emergent trees, and so are in line with the notion of ant mosaic that is likely present in the rest of the rainforest canopy.

References
To simplify, I grouped the lines needing the same correction.
1- Genus and species names in italic letters; lines: 299, 380, 389; 392; 399-400.
2- Many letters in uppercases need to be written in lowercase; lines: 335-336; 349-350; 382.
3- Line 322: delete one of the two dots before Insect Science.
4- Line 327: Djiéto (not Djieto).
5- Line 337: Abhandlungen der Senckenbergischen Naturforschenden Gesellschaft, Stuttgart.
6- Line 370. I hope that you accessed this site after 2013, so, five years ago.
7- Lines 386-388. I suggest deleting this reference, see above.

Figures
Do not forget to modify Fig. 2 to permit readers to separate Dinomyrmex gigas from the four other ant species appearing in black.

Conclusion of the review
This new version of the manuscript shows major improvement over the previous version. In my opinion, if the authors coordinate themselves well and because we now live in the “computer era”, the changes still needed can be made in less than two weeks, so that I recommend acceptance with “minor corrections”. I agree to review the next version if the associate editor feels that this is necessary.


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: ANT MOSAICS IN BORNEAN PRIMARY RAIN FOREST HIGH CANOPY DEPEND ON SPATIAL SCALE, TIME OF DAY, AND SAMPLING METHOD
Review round: 2
Reviewer: 2

Output:
Basic reporting: All comments by the two referees have been adequately attended to.
Experimental design: All comments by the two referees have been adequately attended to.
Validity of the findings: All comments by the two referees have been adequately attended to.
Additional comments: The manuscript has now been substantially improved and concerns of both referees have been adequately addressed. I have a few editorial comments to add:

Line 34 ‘in a new forest statum’ – a better wording might be ‘in a hitherto under-investigated’ or simply ‘in an under-investigated’. The way it is currently worded implies that this stratum has just developed.

Line 85 I would say ‘’those with generally less populous colonies’ as there could by minute, non-dominant species with large numbers of ants in the colony.

Line 125 Suggest adding ‘and’ before ‘leading’

Line 238 Throughout, I suggest hyphenating ‘within-tree’ and between-tree’.  You have done this on line 242.

Line 347 Suggest deleting the word ‘average’ before ‘bait’

Line 357 Don’t you mean ‘may not be valid’?

Line 363 ‘result’ , not ‘resulting’

Line 498 Remove caps in title of reference

When these are attended to I believe that the article should be ready for publication.


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

Input:
Title: EVALUATING OUTCOMES OF YOUNG FOREST MANAGEMENT ON A TARGET SPECIES OF CONSERVATION CONCERN
Review round: 1
Reviewer: 1

Output:
Basic reporting: The Introduction describes to the reader a decline in Golden-winged Warbler population that has historically been attributed to loss of shrubland and increasing competition and hybridization with Blue-winged Warblers. Then, at the close of the first paragraph of the Introduction, the authors dismiss this decline in shrubland and instead point to non-breeding ground factors as the cause of the decline, asserting that ‘regional declines are more likely tied to non-breeding grounds factors’ and use as support the work of Kramer et al. (2017). Unfortunately, the argument is poorly made. Blue-winged Warblers now co-occur with Golden-winged Warblers in the Appalachians, which may entirely account for why newly created shrublands are not occupied by Golden-winged Warblers (i.e., they are out-competed regionally and locally, leaving considerable habitat unoccupied). Further, the assertion supported by Kramer et al. is determined by a total of 9 birds, 7 from Pennsylvania and 2 from Tennessee. This statement is too strongly stated, especially when Kramer et al. do not make this same assertion themselves. (It should be noted that three of the authors of the Kramer et al. paper author this current study as well.)

Line-specific comments......
Line 112. Warblers, not Warbles.

Lines 111-113. An alternative explanation is that the findings of the previous studies are usually correlative in nature, and it may very well be that the factors correlating to bird response are not most proximal to the species, but instead act as surrogates because they are factors we can readily measure. As such, the variation we see among studies may not be evidence of place-specific differences in bird response, but in place-specific differences in study methods.

Line 151. Replace ‘Ours’ with ‘Our study’.

Line 162. ‘our present our assessment’?

Line 219-221. This sentence is unclear. Did the adjacent ephemeral wetland not host Golden-winged Warblers prior or subsequent to vegetation management, or was it the managed area that did not host Golden-winged Warblers prior or subsequent to vegetation management? I suspect the latter, but cannot be sure.

Line 239 and line 369. ‘spatially explicit’. We never use a hyphen between an –ly adverb (‘spatially’), adjective (‘explicit’) combination modifying a noun (‘models’) or pronoun.

Line 253. Programming, not programing.

Line 259. Insert ‘at’ between ‘cover types’ and ‘predetermined’?

Line 261. This resolution is finer than the resolution of the ‘stand-level effects’ incorporated into the models.
Experimental design: The authors stack the deck against the management action by only examining a linear return to current conditions (e.g, lines 325-329, juveniles recruited 1.04 individuals after management linearly increasing to 1.45 individuals at the time conditions return to a pre-management state); it is likely, and expected, that during the return to a pre-management state that some period of improved performance will occur, over and above that which is observed currently. This improved performance may not be immediate (i.e., one or two years post-management action as in this study), but perhaps some period of years after. After this period of improved performance, the expectation is that this improved performance will decline back to the current state. If this response does not occur, it begs the question why one would implement this management action for Golden-winged Warblers in the first place, because all it can possibly do is exact harm upon the species. No one believes this to be the case, but more importantly this current study does not have the data to examine this issue. This is a debilitating concern that I do not believe the authors can correct if they want to comment on anything beyond the immediate period after management action.

Line-specific comments......
Lines 294-295. It strikes me that this assumption of a linear response by Golden-winged Warblers to management is faulty. The vegetation may respond linearly in its development or succession back to the pre-management state, but the idea behind why this management is expected to prove useful to Golden-winged Warblers is that the post-management state will at some point in time provide greater benefit than is currently observed. This benefit may not be immediate but, instead, may accumulate in time, and then fall off back to the currently observed response, suggesting a parabolic response rather than a linear one (for an example, see https://dfzljdn9uc3pi.cloudfront.net/2016/2156/1/fig-1-2x.jpg and think of the post-management state being on the far left and pre-management on the far right). If we allow only a linear response, then all we can achieve is a return to the pre-management level of biotic response, which begs the question as to why one would implement the conservation action if this is the expected result.
Validity of the findings: The conclusion that vegetation management failed to produce the desired result is reached after only two years of post-management monitoring of bird response. The authors themselves concluded (line 219) that it wasn’t until 3 years post-management that the managed area was visually similar to an adjacent unmanaged area.

Because of errors in assumptions, I have no confidence in the model results. There simply is no reason to believe a linear return to the current state would occur in bird response after management action. This assumption requires that the management action can only harm the species. This is logically unreasonable, and no literature is provided to support this notion.
Additional comments: I thought the manuscript was very nicely written, generally clear, and on a subject matter that should be interesting to a wide audience. Unfortunately, as currently crafted, I think the inferences are fatally flawed. The authors would be better served to restrict their analyses and inferences to the immediate period after management. The scenarios are simply unrealistic given their unsupported and illogical assumption of a linear return to conditions akin to the unmanaged state.


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: EVALUATING OUTCOMES OF YOUNG FOREST MANAGEMENT ON A TARGET SPECIES OF CONSERVATION CONCERN
Review round: 1
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: General Comments: I have very few issues with this manuscript. I think it is an important contribution to the GWWA conservation literature, and a timely assessment of management outcomes in the Western portion of the breeding range.

Specific Edits:
Line 51: Replace nest with net
Line 63: Remove “and purports to have benefited” – redundant
Line 87-88: Include reference to Fig1 to support the trends in GWWA decline
Line 89: Include citations that have referenced these “purported” causes of decline
Line 96: Including a rangemap (or at least reference to one) illustrating species distribution and density would be beneficial
Line 114-130: The impetus for the harvest effort described in this paragraph is unclear given a previous statement “Regional variation in Golden-winged Warbler population declines has likely led to this east-west density gradient, as Appalachian states have experienced declines of >95% since 1965 while Minnesota has seen stable or slightly increasing populations over the same period.” Please provide context by including a more explicit statement describing the need for this harvest/management initiative within the Western portion of the breeding range.
Line 131: Remove “on target species” – redundant
Line 138: Insert “However, the ABC initiative’s…”
Line 161 and 170: Contradiction in wording – one site and two sites. Consider rewording “We studied Golden-winged Warblers at 2 sites (one 80 ha managed site and one 30 ha control site)…”
Line 173-174: Redundant word choice. Consider using another word for “host”
Line 213-221: This section is dominated by results of management. Consider moving to first paragraph of results section.
Line 257: Replace "on" with "of"
Line 270 : Replace “of new” with “for”
Line 316-317: Retain information on core area shifts, but remove unnecessary behavioral description- “although some birds occasionally perched on sparse remaining shrubs or woody debris in the edges of managed areas”
Line 371: Increased area of grassland on the landscape not mentioned in results section. Consider moving post-harvest site description from Methods section to Results to clarify this transition. Further, include a more detailed description of the “grassland” habitat. I do not consider early successional habitat “dominated by a low (0.25 – 0.50 m), dense mat of dogwood” to be synonymous with grassland.
Line 454: Reword “is known not to do so”
Figure 2: Photo credit is unnecessary because photos were taken by authors
Figure 5: Unnecessary. These data are adequately described in 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: EVALUATING OUTCOMES OF YOUNG FOREST MANAGEMENT ON A TARGET SPECIES OF CONSERVATION CONCERN
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: I appreciate the efforts made by the authors to accommodate the concerns of the reviewers. I believe the authors' inclusion of an alternative scenario, one which paints the management action in a less negative light, only bolsters their argument. I agree with the authors' reasoning that abundance is likely linear in its relation to the amount of available habitat, at least at the end of the abundance spectrum they are witnessing in central Minnesota. Thus, the evaluation of a parabolic response solely on reproductive performance is a reasonable means of assessing alternative paths for population performance. Unlike the authors, though, I'm not convinced these alternatives are unrealistic. Do we have the data to suggest that they are? Not that I am aware. Perhaps these alternatives are unlikely, I do not know. I think it is reasonable to elide this connotation relating to its reasonable everywhere it is made, unless data exist to suggest otherwise.

Lines 446-448. I have pored over the Upper Mississippi River and Great Lakes Joint Venture documentation (i.e., The 2007 All-bird Implementation Plan, http://www.uppermissgreatlakesjv.org/docs/JV2007All-BirdPlanFinal2-11-08.pdf, and the 2007 Landbird Conservation Strategy, http://www.uppermissgreatlakesjv.org/docs/UMRGLR_JV_LandbirdHCS.pdf). I also did a literature search in Scopus and Google. I can find no where that the JV asserts 'Golden-winged Warbler needs are met.' This quote should be sourced. The link to the JV website is insufficient, as it does not lead the reader to the quote.

Line 451. 'where they are not replaced by Golden-winged Warblers'. I think you mean Blue-winged Warblers. Further, this revised sentence is a bit awkward in its construction. It begins as 'Even in areas where...' and then after the third comma it then says, again, 'even in areas where...'. I think this might be better crafted as two sentences.


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: GENE-BASED ASSOCIATION STUDY FOR LIPID TRAITS IN DIVERSE COHORTS IMPLICATES BACE1 AND SIDT2 REGULATION IN TRIGLYCERIDE LEVELS
Review round: 1
Reviewer: 1

Output:
Basic reporting: This manuscript was well-written.
Experimental design: The overall design of this study followed generally acceptable standard in the field. The study questions were defined clearly by the authors. The methods they used are reasonable and appropriate.
Validity of the findings: The authors presented their findings following the generally acceptable standard in the filed of human genetics. All findings are presented clearly with sufficient statistical evidence.
Additional comments: One minor issue is about the comparison between two different array platforms. It is not clear whether the authors took any specific steps to ensure that the same variants (allele, strand direction) were compared. A  bit more description in the methods could be helpful.


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: GENE-BASED ASSOCIATION STUDY FOR LIPID TRAITS IN DIVERSE COHORTS IMPLICATES BACE1 AND SIDT2 REGULATION IN TRIGLYCERIDE LEVELS
Review round: 1
Reviewer: 2

Output:
Basic reporting: (1) Clear, unambiguous, professional English language used throughout.
(2) Intro & background to show context. Literature well referenced & relevant.
(3) Structure conforms to PeerJ standards, except for the AKNOWLEDGEMENT section, which should not be used to acknowledge funders according to the PeerJ standards.
(4) Figures are relevant, high quality, well labelled & described.
(5) Although raw data was not supplied, all scripts were shared in GitHub (https://github.com/aandaleon/px_chol).
Experimental design: (1) Original primary research within Scope of the journal.
(2) Research question, which was to clarify the transferability of lipids-associated loci in non-European populations, well defined, relevant & meaningful. It is stated how the research fills an identified knowledge gap.
(3) Rigorous investigation performed to a high technical & ethical standard (GWAS, XPEB, S-PrediXcan).
(4) Methods described with sufficient detail & information to replicate.
Validity of the findings: (1) Data is robust, statistically sound, & controlled.
(2) Conclusions are well stated, linked to original research question & limited to supporting results.
Additional comments: The authors performed GWAS in a Nigerian and a Filipino cohorts, respectively, and XPEB analysis by combining these non-European populations with previously published GLGC GWAS summary statistics in European populations, as well as gene-based analysis through S-PrediXcan. Considering the relatively small sample size of these two non-European populations, it comes as no surprise that no novel loci were identified in the GWAS or the XPEB analysis. Previously reported lipids-associated loci were confirmed in the current study, and novel genes (BACE1 and SIDT2) near known SNP (rs662799) were identified using S-PRediXcan, providing new evidence of the possible underlying mechanisms. The manuscript is well organized and the statistical methods were appropriately implemented.
A few minor comments for the authors.
(1) For the XPEB package, it took SNPs and P values as input as well as the sample size of the included ethnic groups. According to the package manual, SNPs with variation >10% of the median sample size is not acceptable. Roughly half of the GLGC participants were genotyped using common Affymetrix or Illumina GWAS arrays while another half of them were genotyped using Metabochips which included far less SNPs. As a result, a few SNPs in the GLGC dataset showed sample size >10% deviation from the median sample size. Were these SNPs before running XPEB? For the SNPs that were missing in the base population (i.e. GLGC), the package manual provided methods to do imputation. Were the missing SNPs imputed or simply exclude from the analysis?
(2) For Table 3 and Table 4, I recommend add a column showing SNP position in addition to chromosome.
(3) In Supplemental Table 1, results in three different papers were compared. What’s the different between these three datasets?
(4) For Supplemental Table 2, some notes may be needed to explain the meaning of the column names, and also, please be more accurate about the age of the Yoruba study (70-?).
(5) L184-185, six new SNPs for HDL and five new SNPs for LDL had FDR<0.05, at the same loci as the earlier significant SNPs (Supplemental Table 3). This sentence and the results in Supplemental Table 3 were confusing. ‘The earlier significant SNPs’ may refer to the significant findings in the GWAS analysis, which were CETP on chr16 for HDL and APOE on chr19 for LDL. However, there was a significant SNP at PCSK9 on chr1 with FDR<0.05 in Supplemental Table 3. Please rephrase this sentence and correctly describe the results.
(6) For Supplemental Table 4, I recommend re-sort the SNPs first by locus, then by FDR values.


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: GENE-BASED ASSOCIATION STUDY FOR LIPID TRAITS IN DIVERSE COHORTS IMPLICATES BACE1 AND SIDT2 REGULATION IN TRIGLYCERIDE LEVELS
Review round: 1
Reviewer: 3

Output:
Basic reporting: This manuscript is clear, concise, and professionally written. I found the methodology and approach each to interpret.

The introduction was thorough and explained the rationale behind the study.

To the best of my knowledge, basic reporting guidelines were met.
Experimental design: I have some concerns with the experimental design of this study:

1. The authors state that S-PrediXcan/MetaXcan was used on summary statistics from the CEBU and Yoruba cohorts to identify gene-based associations. I do not understand why a summary-statistic based approach was used when raw data is available. Although MetaXcan and PrediXcan are equivalent when using European data, my understanding is that this is not true when using non-European cohorts. I would recommend that authors either a) re-run genic association analyses based on raw data; or b) calculate LD Matrices from the CEBU and YORUBA populations for use with MetaXcan; or c) provide evidence that the two approaches are analogous even when applied to non-European data.

2. I am concerned about the use of the GLGC cohort as a replication data set. The introduction of the manuscript states that the samples includes "7,898 non-European-ancestry individuals, including the children of those in the Cebu cohort". How did the authors account for this potentially substantial relatedness within the cohorts? In particular, I note that the GLGC results have significant overlap with the Cebu PrediXcan results- how was relatedness accounted for in this replication analysis?
Validity of the findings: I have some concern with the validity of the findings in this study.

1. I am concerned that the prediXcan/metaXcan analyses do not include sufficient correction for multiple testing. Currently, authors correct for the number of genes within each tissue, but do not take into account that 44 tissues are tested. My rough estimate (44 tissues * ~5,000 genes/tissue) gives a stricter significance threshold of 2.2e-07. According to this estimate, no genes are significant in the Yoruba population, and <5 in Cebu.
While this correction may be overly stringent given eQTL correlation between tissues, I feel that this is worth noting as a caveat to your results. Perhaps an alternative, less conservative approach, would be to apply a study-wide 5% FDR correction.

2. The authors identify multiple genome-wide significant associations in both the Yoruban and Cebu SNP-based GWAS, which cluster into specific loci.  In my opinion, it would be advisable to carry out some type of conditional analysis to identify lead signals in these loci.

For example, for the Cebu cohort, authors list the top 10 significant SNPs in Table 4- these are all in the same locus (Figure 2), and are all in fairly high LD (>0.6). It therefore seems uninformative to list all these SNPs - instead, why not use GCTA-Cojo, FINEMAP, or similar, to identify the lead SNP (s) in this and other loci, and list those?

The same is true for the S-PrediXacn results (eg, presented in Table 6). Authors identify multiple associations in 11q23.3, across multiple tissues (and presumably there are multiple sub-threshold associations in this region also). It would be interesting to see the correlations of GREX between these genes in these tissues, and perhaps to carry out a conditional analysis of these associations.
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: GENE-BASED ASSOCIATION STUDY FOR LIPID TRAITS IN DIVERSE COHORTS IMPLICATES BACE1 AND SIDT2 REGULATION IN TRIGLYCERIDE LEVELS
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The authors have addressed the issues, and I have no further 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: COST-BENEFIT ANALYSIS FOR INVASIVE SPECIES CONTROL: THE CASE OF GREATER CANADA GOOSE BRANTA CANADENSIS IN FLANDERS (NORTHERN BELGIUM)
Review round: 1
Reviewer: 1

Output:
Basic reporting: Following the guidance of PeerJ I have checked figs and tables, the raw data and language. The raw data and code can be opened, and are well described in English. Language is clear, intelligible and professional. At a few places in the text minor details were found that can easily be corrected in a final stage. The references to literature provide sufficient context to Invasive Alien Species management, environmental economics and the model species. The structure of the article is professional. There are no hypotheses or research questions, but there is a clear aim and relevant results in relation to that.
Experimental design: The study reports on original primary research within Aims and Scope of the journal. A research question or an hypothesis is not provided. However, in my view, there is no need for them given the aim of the paper to demonstrate comparison of scenario’s using a bio economic model. The application of such a model is relevant & meaningful and fills an identified gap. The study uses techniques that suit the purpose. There are no ethical issues that could be an objection to publish the study. The methods are described with sufficient detail & information to replicate the study, provided the reader has a good mathematical background. Below, I will identify how the authors may facilitate readers that are less proficient in mathematics.
Validity of the findings: I appreciate the study as a worthwhile exercise. The data that are used refer to goose census data, harvest data and costs of water sanitation and crop damage. The authors rightly point out that data availability is limited. Still, they are able to put it to good use with their model. The data have not been gathered for this particular purpose but they are used in a logical way and the analyses are statistically sound. The parameters that feed into the models can be regarded as good approximations and the conclusions will certainly be robust for changes in parameter values. The conclusions are well stated, linked to the original aim and limited to supporting results.
Additional comments: By applying this model, it becomes clear under what assumptions the enhanced scenario of population management can be economically justified in comparison to business as usual. This is a general advantage of using (quantitative) models and it also works well in this case. The principal point that application of a Cost Benefit Analysis provides a useful framework to support decision making is well-elaborated.

Maybe it would be good if the authors mention explicitly why an alternative scenario of ‘enhanced scaring of geese’ is not considered. The value of a Decision Support System is greater when all relevant alternatives are considered. In theory, goose damage may be prevented by scaring geese. Probably, the authors have reason to believe that scaring is not effective in practice, rendering the ‘enhanced scaring of geese’ scenario ‘not relevant’?

The sensitivity analysis is restricted to exploring variation in a few relevant parameters (observed capture rate, discount rate and unit costs for eutrophication). The authors have made a selection for parameters they consider relevant. It thus remains unclear whether variation in other parameters may affect the conclusions and what the order is in parameter-sensitivity. For example: The parameters of the logistic growth model have been derived from limited census data. Thus, the value for carrying capacity (K) will be biased if the census results for the last years in the time series are biased. It would be good if the authors could explain that the results are robust for variation in the value for r and K and the unit price of hay.

In words the authors have identified what the main assumptions are and to what extent they can be considered justified. One of these is the assumption that costs of maintaining a constant removal/capture rate are constant over a range of population densities. For this species, under these conditions, I think it is fair to make this assumption. Still I would suggest stating explicitly in the text whether the model conclusions will be sensitive for a change in model formulation with regard to these costs. Am I right to believe that this will not be the case, because costs of management are small relative to damage costs?

Personally I would have appreciated more insight in the (calculation of the) population development under the two scenario’s and the observed field data from 2010-2015. From the text (lines 447 and 328) I read that “the predictions from this model were close to the observed results of a subsequent eradication “ and “at a lower than observed capture rate Bc could not be eradicated within the time horizon “. Is it possible to plot the observed data after 2009 in fig 3 with different symbols? Please consider adding more information on the predicted population development under the two scenarios (either as a graph or in words).

From the information provided (line 276 “...the population level before moult capture in year t equals the remaining post-moult capture population in year t-1 projected one year ahead on the logistic growth curve”), the principle of the calculation of predicted population trajectories is clear. It does, however, require some mathematics to actually implement that into the formula for the growth curve provided (equation 1; in that formula the reference is the start population). The reader will be facilitated if the authors indicate that formula 1 can be used to calculate the population level before moult capture in year t, by replacing p0 by the remaining post-moult capture population in year t-1 and by replacing t by 1. Maybe it is also helpful to provide the script for the full bio-economic model.

The authors point out that the benefits of management may be offset by increase in abundance of other species of geese (native or non-native). Would it be good to provide a little more background information on the status and numbers of relevant species in this respect in the introduction? What proportion of current damage is caused by Canada geese and what by other species?

Given my proficiency in English, I am not in a position to comment upon language and grammar. But to me the text is entirely clear. Below, I present the scant editorial comments that I think are useful to make.

In line 174 remove the word ‘and’ (double word)
Line 244-246. It appears as if information is repeated? Please rephrase
Line 447-449 I do not entirely understand the meaning of the sentence “The predictions from…..” Could you please rephrase this sentence?
Table 1 line 3: a bracket points in the wrong direction


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: COST-BENEFIT ANALYSIS FOR INVASIVE SPECIES CONTROL: THE CASE OF GREATER CANADA GOOSE BRANTA CANADENSIS IN FLANDERS (NORTHERN BELGIUM)
Review round: 1
Reviewer: 2

Output:
Basic reporting: see below - general comments
Experimental design: See below - general comments
Validity of the findings: See below - general comments
Additional comments: Summary
This study presents a cost benefit analysis (CBA) of the management and control of an IAS in Flanders. The BAU scenario is compared with a scenario that includes coordinated moult captures in addition to the BAU actions. The results show that the enhanced scenario had higher benefits (estimated as avoided costs from damage to grasslands and avoided damage from eutrophication) than additional costs. Some sensitivity analyses were performed with respect to estimate of N-damage, capture rate and discount rate.

General comments
The question addressed in this study is an important one. Given a limited availability of funds and resources, biodiversity management options should be carefully selected and motivated. Cost benefit analysis provides a useful tool for making such motivated policy choices. While the case study is an interesting one, the current version of the text raises several issues.

Firstly, the structure of the text could be greatly improved. Most of the motivation regarding the assumptions that were made when performing the CBA were only mentioned in the discussion section, while they should be mentioned in the method section. Examples of these include the selection of damage types, the selection of parameters for the sensitivity analysis and the option not to include rebound effects. In addition, it is only in the section ‘sensitivity analysis’ that the study period is mentioned, while this should again be included in the method section.

Secondly, the text (especially the introduction) seems to use the concepts ‘efficiency’, ‘effective’ ‘economically optimal’ and ‘cost-effectiveness’ as synonyms while they are clearly not.

Thirdly, the CBA is not correctly described and implemented.
-	In the introduction (lines 116-135) the authors mention that a CBA is used to search for the scenario with the ‘lowest total costs’, to select the scenario that ‘maximizes avoided costs’ or the scenario with ‘the highest net PV (=total discounted avoided loss minus total discounted management costs)’. These three statements are contradictory and only one is correct (the last one).
-	In addition, when implementing a CBA it is important to clearly state the standpoint from which costs and benefits are assessed. The current study seems to perform a social CBA from the viewpoint of society in order to minimize the total net social costs associated with Bc management in Flanders. However, the text is not always consistent with this viewpoint: e.g. line 158 mentions ‘… do not represent a direct cost for the regional government or local authorities’ which seems to imply that the CBA is excluding costs from private citizens.
-	In a CBA costs and benefits are valued based on opportunity costs and not based on market prices, since the latter can be distorted by taxes, subsidies, imperfect information and imperfect competition. Thus market prices are unlikely to reflect the true social value of resource. Yet in the current study, the damage to grasslands is based on market prices for hay (line 222) without correction for sales taxes and agricultural subsidies. In addition, the damage from N and P is estimated based on avoided costs (line 193-195) which is a convenient method but has serious disadvantages since it is typically leading to an underestimation.
-	The geographic scope of the CBA should be mentioned explicitly and evaluated. Why look at Flanders and not the whole of Belgium? Are these geese population so local that they do not cross borders?
-	I cannot support the conclusion that ‘limiting the scope or complexity of a CBA is advisable without rendering the analysis unrealistic (lines 519-520)’. The essence of a CBA is to include all costs and benefits to all affected parties. Even though not all these impacts can be valued in monetary values, they should still at least be mentioned and not dropped for convenience reasons. Moreover, the current study is not exactly a good example in this sense since both the costs and the benefits of management actions are underestimated (as the authors acknowledge themselves in the discussion section). When both costs and benefits are underestimated it is not clear how the total result (PV values) are related to the true total impact.

Specific comments
-	Introduction. Line 133. Several other interesting applications of CEA or CBA to invasive alien species management could be mentioned and used in this study (see, e.g., Waigner et al. 2010 or Schou & Jensen, 2017)
-	Line 141: please define ‘Anseriformes’ when you use the term for the first time.
-	Line 172: How do you know these are ‘the main economic impacts’ if the other impacts are not valued?
-	Line 193: The estimated range for the P-value is very high (80-800 euro/kg). Why is this range so large? Why did you decide to use only the lower estimate in the CBA?
-	Line 211: How are these compensation payments determined? What is their typical level?
-	Line 237-248: It is not clear how this ‘number of captures needed to reduce the Bc population’ is calculated. Especially the second step is confusing.
-	Line 275: How realistic is the assumption that the gees population does not migrate?
-	Line 411: ‘were’ instead of ‘ware’
-	Line 429: by applying
-	Line 514: by applying
-	The datasets are not clear to use as an outsider:
o	What is included in the agricultural data? How are these data determined? Sources? How are they used?
o	Why are the Canada goose data not in chronological order?

References
Wainger, L. A., King, D. M., Mack, R. N., Price, E. W., & Maslin, T. (2010). Can the concept of ecosystem services be practically applied to improve natural resource management decisions?. Ecological Economics, 69(5), 978-987.
Schou, J. S., & Jensen, F. (2017). Management of invasive species: Should we prevent introduction or mitigate damages? (No. 2017/06). University of Copenhagen, Department of Food and Resource Economics.


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: DISTRIBUTION OF BACTERIAL COMMUNITIES ALONG THE SPATIAL AND ENVIRONMENTAL GRADIENTS FROM BOHAI SEA TO NORTHERN YELLOW SEA
Review round: 1
Reviewer: 1

Output:
Basic reporting: This manuscript describes a field study designed to examine microbial biogeography in surface water and benthic boundary layer water in the Bohai Sea of coastal China. I am pleased that this contribution focuses on the microbial diversity in marine and brackish environments of China and broader east Asia as this region has traditionally received less attention in the marine microbial ecology/oceanography literature. I commend the authors for their hard work collecting this dataset and for also sampling multiple biogeochemical parameters in addition to collecting samples for sequencing. I also commend the authors on the well curated datasets/tables/figures submitted with this manuscript.

The writing of the manuscript is generally understandable, although there are many places (highlighted below) with awkward English phrasing and syntax coupled with rather simple grammar mistakes. The authors might benefit from having a native English speaker help them clarify certain sentences, remove unnecessary words, and ease overall comprehension. I have noted several examples below where the English writing could be improved to aid in reader comprehension.

Figure 2: “explained” is misspelled

Physiochemical is misspelled throughout text

Abstract:
Line 21: change “matters” to “material”

Line 24: replace “spatial” with “the”

Line 25: replace “communities” with “taxa”

Line 25: remove “the” before “spatial”

Line 26: “coastal gradients” Gradients of what? Please specify

Line 28: “sunlit surface layer” Unclear if this refers to the “shallow coastal water (depth < 20m)” or is a unique depth strata in addition to the bottom layer. Please clarify.

Line 33-34: “Geographic distance enhanced bacterial community dissimilarity and limited bacteria distribution in both surface and bottom water.” Unclear to me what is meant by this sentence... Are you saying that communities became more taxonomically dissimilar as geographic distance between samples increased? And that this trend held in both surface and bottom water? Please clarify

Introduction:
Lines 60-63: “Hence, spatial effects may superficially mask environmental effects when physicochemical factors are spatially autocorrelated, while in fact persistent environmental heterogeneity is possible to overwhelm geographic separation in generating and maintaining microbial diversity at intermediate spatial scales.” This sentence is unclear to me and should probably be split into two sentences. Are you saying that community composition is a function of both dispersion (so called spatial effects) as well as selection due to variable habitat conditions? And that this balance is effected by the scale at which you are defining your study area? As I understand you essentially have a two-factor study design where you must account for the effects of spatial separation/dispersion between similar habitats and combined niche adaptation+spatial separation differences between dissimilar habitats (i.e bethic boundary layer versus surface water). Again, I think this sentence should be clarified.

Line 63-66: “As Wang et al. (2015)…” sentence probably not needed

Line 71: “In the surface water” Please specify. For example, “in the upper 20 meters of the water column”

Line 85: In contrast instead of “by contrast”

Line 86: “shallow coastal water” Again please be specific about depths

Line 91: located instead of “locating”

Results:
Line 197: Strange wording... I suggest instead "Bacterial diversity and abundance"

Lines 198-199: “Thereinto, fourteen phyla including the main classes of phylum Proteobacteria were abundant …” This sentence has unusual wording… Try instead “We focused our analyses on fourteen taxonomic groups that were greater than 1% relative abundance in at least one sample. These groups included the Phyla … and the classes Alphaproteobacteria, Gammaproteobacteria,  Betaproteobacteria, and Deltaproteobacteria.”

Line 205: confusing syntax “This indicated the abundant taxa of P1 and B8 distributed in surface and bottom water with great similarity.”

Line 209: replace “taxa of them were found to be the discriminant taxa in these distinct clusters” significantly discriminant clusters

Line 223: remove “remarkable negative/positive”

Line 226: “III were also strongly” Do you mean Cluster II here?

Line 227: remove “Despite of these discriminant taxa”

Line 227: “Despite of these discriminant taxa, there were still 50 abundant taxa, whose relative abundance together reached over 50 % in each cluster, dispersed indistinguishably in three clusters” Unclear wording... I'm not actually sure what you mean. Do you mean "50 taxa accounting for over 50% of total OTU abundance were evenly distributed amongst all three clusters."?

Line 229: “Moreover, Cluster I-III shared 70 % of total OTUs, and the shared OTUs between surface and bottom bacterial communities accounted for over 89 %” Again unclear wording/syntax/grammar… I'm not entirely sure what you are saying here, but I think it would be clearer if you wrote "Samples from clusters I-III shared 70% of all detected OTUs. Furthermore, 89% of all OTUs were shared between surface and bottom water samples."

Line 247: remove “Driving forces of”

Line 248: Please be explicit about the input data for your PCoA analysis.

Line 248: Replace “exhibited clear clusters” with suggest separation

Line 270: remove “striking”

Line 271: remove “close”

Line 271: “correlationships” should be correlations

Line 276: remove “intriguingly”

Line 276: “geographic distance” Unclear - geographic distance of what? Do you mean pairwise physical distances between two samples? Please specify

Line 248: Replace “exhibited clear clusters” with suggest separation

Line 270: remove “striking”

Line 271: remove “close”

Line 271: “correlationships” should be correlations

Line 276: remove “intriguingly”

Discussion:
Line 283: remove “Generally, environmental variables presented remarkable spatial gradients.”

Line 283: “Salinity and turbidity were related to longitude, shaping horizontal gradients from the Bohai Sea to northern Yellow Sea; collection depth led to vertical dissimilarity of temperature, salinity, pH, DO, Chl a, nitrate, phosphate and silicate between surface and bottom water (Dataset S1).” Again, rather unclear wording and phrasing... I suggest something like "We observed horizontal salinity and turbidity gradients ranging from the mouth of the Yellow River to the northern Yellow Sea while gradients in temperature, salinity, pH, dissolved oxygen, Chl A, nitrate, phosphate and silicate were reflected in sample collection depths."

Line 288: Replace “non-random distribution pattern of bacterioplankton” with patterns of bacterioplankton distributions.

Line 295: replace “actually” with likely

Line 295: “to their physiological requests for adequate light and oxygen, as well as the other beneficial conditions in surface water.” I don't think you have enough evidence to support this statement as it is written. I would say something like "Bacterial taxa discriminating Cluster I were likely adapted to surface water conditions as exemplified by the differential abundance of cyanobacterial OTUs and known aerobic heterotroph OTUs in surface samples.

Line 309: Replace “the microbial hypothesis that some microorganisms are biogeographically restricted.” with their close proximity to mouth of the Yellow River.

Line 369: “This could explain why nitrite was more relative with the bacteria diversity than nitrate in our results.” This statement needs to be revised for proper English grammar. I cannot decipher its meaning as it currently stands.
Experimental design: I think the research question, motivations, and description of the methods is sufficient for publication in PeerJ.
Validity of the findings: The results appear to be derived from sound sampling, processing, and sequencing methodologies, and for the most part (with some exceptions noted below) the statistical analyses appear to be robust. The conclusions are not overstated, appear to be adequately supported, and are largely consistent with the oceanographic features of the region (again I have some additional recommendations below).

Minor Comments:
Figure 1: It would be useful to have a figure inset displaying where the Bohai sea is located with respect to the rest of coastal China. This would give extra context for readers who are not familiar with the region.

Instead of using terms like “surface waters” I would recommend being more specific and choosing something like “the upper 5 meters of the water column,” “the upper 20 meters” and so on.

When mentioning N/P ratios please be more specific if you are talking about total nitrogen or inorganic nitrogen.

DO should be replaced with “dissolved oxygen” throughout the text.

Results:
When discussing correlations between variables in this section please write the correlation and the P value.

Line 248: Please be explicit about the input data for your PCoA analysis.

Line 276: “geographic distance” Unclear - geographic distance of what? Do you mean pairwise physical distances between two samples? Please specify

Discussion:
Line 381: “Additionally, adaption to different pressure might also explain the bacterial community variation in bottom water.” I suspect that pressure differences are not driving the patterns in your study. Pressure is a relevant parameter at great depths (over 1 km) but I don’t really think it would be important at depths of < 100 meters such as in your study.

Line 387: remove “Unlike geographic distance, depth and salinity,”

Major Comments:
Please explain your rationale for assigning sample clusters in this this study. More specifically, how did you classify clusters in Figure 2? Why is B8b classified as Cluster II and not Cluster III? I see strong evidence in Figure 1 for two well-supported clusters but is not obvious to me that Clusters II and III should be separated.

Figure 3: How do you define “most significant taxa of each cluster” are these from the results of your LEfSe analysis? Why did you not include all the discriminant taxa in Fig S1? This should be briefly explained in the figure legend.

Please be precise and clear when discussing sample collection depth and overall water depth, otherwise this terminology can be confusing.

I would recommend trying to distill your tables down to the most relevant correlations for your story. It will help your reader grasp the main relationships presented in your study. For example, “latitude” has no significant correlations in Table 1 at all. I also recommend omitting the P value column altogether and simply only highlight a correlation if it exceeds 0.5 and has a P value < 0.05. Then mention this in the table legend. For me P values are rarely interesting in and of themselves, but that is my own preference.

The structure of Table 1 and Table 2 is somewhat confusing to me. What I think you are intending to convey is that the correlation for “Longitude, ect” is due to the alpha diversity index calculated for all OTUs at that sampling station while the correlations underneath “Longitude, ect” denoted by “surface” and “bottom” refers to correlations for alpha diversity indices calculated only for the surface and bottom depths respectively. Is this correct? If so, you should explain this more clearly in the table legends. Additionally, it is unclear why you need a separate correlation analysis for Wat-Depth and Col-Depth… Indeed, the “bottom” correlation for the two categories are identical and there is no comparison for surface, which I am assuming is because all your surface samples have the same collection depth… But (assuming my above understanding is correct) then why does it make sense to have an integrated surface+bottom Col-Depth comparison here? Again, I think this needs some clarification… Please see my comment above.

Table 2: Please clarify what your distance matrix inputs are for your mantel tests. I am assuming you are performing the mantel test on UniFrac distances versus a distance matrix of pairwise sample distances in each category (Geo-Distance, Wat-Depth, ect) while controlling for the effects of each category in your partial mantel tests. This information would be useful in a table legend.

Lines 388-392 (Conclusion): “meanwhile the N/P ratios in most of samples were much higher than the Redfield's ratio 16 (Redfield 1958), suggesting a severe phosphate insufficiency for biological communities relative to inorganic nitrogen.” You discussed the N/P ratio little in the results, yet conclude with a statement referencing it which does not seem logical to me. N/P should either be mentioned more in the discussion prior to this sentence. Here I suspect the deviation of the measured N/P ratio from Redfield ratios is due to terrestrial inputs – probably from local agriculture. I find it unlikely that these communities would be experiencing “severe” P limitation, but rather they just have a large excess of N relative to P due to riverine inputs resulting from human land use. This distorts the N/P ratio from Redfield, but doesn’t really imply anything about limitation. I think you would need to do a number of additional experiments to claim “P limitation.”

Lines 164-165: (Methods) “Pearson’s and Spearman’s correlations between variables were calculated by R program.” When conducting many statistical tests (in this case correlation) one should correct P values for multiple testing artefacts (ie false positives simply due to the increasing number of comparisons). This can be done using the conservative Bonferroni Correction, but I would recommend using the Benjamini-Hochberg multiple test correction which controls the false discovery rate. Did you use multiple test correction? If so you should include this in your methods.
Additional comments: No additional comments