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: SPECIFICITY TRUMPS FLEXIBILITY—LOCATION-BASED STABLE ASSOCIATIONS BETWEEN SYMBIODINIACEAE GENERA AND PLATYGYRA VERWEYI (SCLERACTINIA; MERULINIDAE)
Review round: 1
Reviewer: 1

Output:
Basic reporting: -The language is mostly fine, but there are still some typos to check for (e.g. several instances of “form” instead of “from,” and some sentence fragments here and there).

-In most areas the literature is well referenced, but there are a few oversights. For example, the idea that shuffling/switching is taxon-dependent and may not be helpful for the majority of highly specific cnidarians has been around for a while, but there are no references to this early debate (e.g. the Goulet/Baker exchanges in the mid-aughts). There’s also some recent relevant work in anemones showing a lack of shuffling (Gabay et al. 2019 ISMEJ) and trade-offs associated with alternate symbionts (Matthews et al. 2017 PNAS; Matthews et al. 2018 Proc Roy Soc B). There are also opportunities to highlight studies that show a lack of meaningful symbiont shuffling (e.g. Lee et al. 2016 Microbial Ecology) around L374.

-I have a few issues with how Symbiodiniaceae diversity is discussed:

1. The markers used for qPCR are genus level markers, so throughout the manuscript the language should only be about Cladocopium and Durusdinium, rather than Cladocopium C3/C3cc and Durusdinium trenchii/glynni (which implies that those are the only potential species in this association in this location). While other studies may have established that these are the main symbionts in these corals, it’s impossible to rule out that other species may have been present based on the qPCR data, and the language should reflect this.

2. It only seems to be a problem in the introduction, but in L50-55 the authors are presenting an outdated view that different Symbiodiniaceae genera have different, genus-wide physiological characteristics. This is somewhat true for Durusdinium, which generally are found in corals in stressful environments, but it’s wrong to say that “Cladocopium species are the most sensitive to stress.” In fact, the most heat-tolerant symbiont we know of is Cladocopium thermophilum (see studies by Hume et al.). There’s just too much physiological diversity among species within genera to support broad statements about genus-wide characteristics.

3. The writing is unnecessarily vague about what constitutes symbiont switching vs. shuffling (they are distinct phenomena with their own definitions; see e.g. the Baker 2003 review). Relatedly, the writing is also vague about the difference between dominant and background symbionts. In my opinion, just because a coral’s symbiont community changes from 100% Cladocopium to 99% Cladocopium/1% Durusdinium, that doesn’t really constitute shuffling; it’s just an increase in a background symbiont population. Shuffling would require a larger, more ecologically meaningful change. One could argue about the threshold value, but with the exception of the Bay study (which is just one case), I don’t think there’s much compelling evidence to suggest changes < 10% are all that important in most situations. I think the authors are trying to emphasize that certain corals went from entirely C to some mixture of C/D, but that’s not what the language implies. It’s very clear to me from looking at the figures (and the title and conclusions!)  that the story should be focused on stability, rather than flexibility, but the wording as is doesn’t really help the case. I think it’s very important to go through the manuscript carefully and make sure this story is clear.
Experimental design: -I feel the manuscript is a bit longer and more complicated than it needs to be. I realize it’s just a portion of a previously published study, but when it comes down to it the reciprocal transplant component is not really necessary to describe in depth (and certainly doesn’t need a figure), as the data are only for parent colonies and smaller fragments of those colonies that were maintained at the same site as the parent. So it’s essentially an observational study of symbiont communities in corals at three locations over several years. That’s not to say it’s not worth publishing, but I think the story could be told far more efficiently.
Validity of the findings: -No comment.
Additional comments: L19: Do you really mean “cores”? Or “corals”? Or “symbiont communities”? This is a confusing opening line and needs a bit more context.

L22: When listing unnamed species, I’d recommend including the entire ITS2 designation (which means adding the former clade letter). So instead of “Cladocopium 3/3cc” I’d write “Cladocopium C3/C3cc.”

L59: Need to define the difference between shuffling and switching.

L80: But what about host mechanisms? Rapid evolution in either partner? I think this line is a bit too narrow.

L108-111: Very confusing sentence. I think you have too many asides. Just split into a few clear sentences.

L171: Which data set? Needs a reference or link.

L299: Here’s the main example of where I think the term “switching” is too strong. I’d rewrite as “In March 2015, cores seemed to have acquired some Cladocopium at various percentages (range: 1-21%; mean: 6%)”

L310: Please provide the mean with the range. Or maybe the median.

L316-318: Long sentence that could be broken into two.

L321: 97% Durusdinium?

L332: Please provide the mean with the range.

L340: typo: Symbiodiniaceae

L341 and 344:


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: SPECIFICITY TRUMPS FLEXIBILITY—LOCATION-BASED STABLE ASSOCIATIONS BETWEEN SYMBIODINIACEAE GENERA AND PLATYGYRA VERWEYI (SCLERACTINIA; MERULINIDAE)
Review round: 1
Reviewer: 2

Output:
Basic reporting: This work looks at the stability of symbionts in one species of coral from Southern Taiwan in colonies located at three different locations. Essentially they observed the presence of two symbiont species. The species from the new genus Cladocopium (formerly Clade C) are found in colonies at locations with environments indicative of the region. All colonies at the third location, the outflow from a nuclear power facility, were dominated by Durusdinium trenchii.  This is in keeping with work on other animals from this region of the Pacific. The finding of symbiont stability in these colonies that have not undergone extensive and artificial manipulation is an expected outcome and is likely the rule for most corals everywhere. Still there remain few studies that conduct long-term monitoring and more of these biopsies/long-term monitoring are needed. I think that the authors are entirely correct in that there exists considerable dogma and misinformation about the propensity “switching” and/or “shuffling” and its ecological significance.

I did find the writing of this work a bit convoluted and feel that it could/should be substantially streamlined. They talk about these samples as being part of a larger reciprocal transplant study but then do not show the results of this other work. This is very confusing to the reader. They should simply present it as a yearlong monitoring of colonies in place and leave these other irrelevant and distracting details out (avoid mentioning reciprocal transplants if these were not studied). This also applies to the fitures.  Figure 2 should be deleted, Figures 4, 5 and 6 could be easily combined, and Figure 1 modified to remove the reciprocal transplant arrows.  With careful editing I think that they could easily reduce the length of this paper by ~50%

I found their taxonomy and taxonomic references of the dinoflagellates symbiont somewhat strange and confusing. For example, the Durusdinium they are tracking in this paper is D. trenchii. This species of symbiont can be found in corals with horizontal symbiont acquisition in Taiwan. Therefore, despite the fact that they are using “genus” level qPCR probes, they should report this Durusdinium as D. trenchii. The only other members of this genus from this region occur in the coral Oulastrea, but these species are specific to that animal.

Moreover, they should remove mention of D. glynnii from the manuscript. This symbiont occurs only in Montiporids and Pocilloporids. The ITS2 sequence variation in both D. trenchii and D. glynnii is very similar and both have one sequence (D1) in common. This I think has created some confusion in their minds
I recommend the authors carefully read the following paper:
Wham, D.C., Ning, G., and LaJeunesse, T.C. (2017). Symbiodinium glynnii sp. nov., a species of stress-tolerant symbiotic dinoflagellates from pocilloporid and montiporid corals in the Pacific Ocean. Phycologia 56, 396-409.

I agree with their general interpretation that the occasional finding of D. trenchii at sites NPP and WLT (and vice versa) is random and that not much emphasis should be placed on these results.  Clearly, P. verweyi associates with two species of Symbiodiniaceae and that depending on the location and environment one or the other symbiont can show up (be detected) in a colony.

This brings me to another important issue that needs addressing. It relates to the findings (actually more the conclusions) from the Chen et al. 2005 paper. The perceived seasonality reported by Chen et al. 2005 cannot be substantiated by the present paper nor by a previous follow-up paper conducted by the same group and published in 2012 (Hsu et al. 2012). The findings by Hsu et al. show difference on relative proportions but honestly no seasonality. What appears to be the source of this variability is that many of the colonies in the region have mixtures of Cladocopium and Durusdinium (trenchii) hence sampling artifact at any given time could (and does) create swings in the measured abundances and/or prevalence of a particular species of symbiont. BUT this is not indicative of a predictable ecological response to seasonality. Therefore, I recommend backing off on this in the discussion now and in the future.

It is often mentioned that changing genera occurs withing P. verweyi. This is not accurate. They are working with two specific species from two different genera.  While one species is formally described, D. trenchii, unfortunately, the other one is yet to be described. I recommend that they call it Cladocopium sp. C3cc throughout the paper.

The use of the word “shuffling” is also somewhat misleading. Its use implies the invisible hand of the host actively controlling the resident symbiont population, which, to my knowledge, there are no data to support this. I would recommend using more neutral language like “…changes in the relative proportions of symbiont occurred…”

With regard to their discussion on stability, the authors also should read (and cite) a paper on a similar story showing prevalent stability in a high latitude system/coral species:
Lee, M.J., Jeong, H.J., Jang, S.H., Lee, S.Y., Kang, N.S., Lee, K.H., Kim, H.S., Wham, D.C., and LaJeunesse, T.C. (2016). Most Low-Abundance "Background" Symbiodinium spp. Are Transitory and Have Minimal Functional Significance for Symbiotic Corals. Microbial Ecology.

There is mention of NGS but this approach is plagued with its own problems, so if they’ve been criticized previously for not using this, I think that this was unfair.

Be careful when reporting the interpreted the findings of the Boulotte paper. This paper is plagued with inconsistencies and some of the data are rather peculiar. To my knowledge and I have worked on these animals across the Indo-Pacific, P. damicornis and Stylophora do not associate with the same symbiont species, yet this work shows the same symbiont in both species of host. See Sampayo et al. 2007 for example of the marked differences in the symbionts harbored by these two Pocilloporidae.

I disagree with the assertion, “Studies have shown that corals that are able to shuffle have a better chance of overcoming stress,” there is very little evidence to support this speculation, further changes in symbiont are more of a sign of severe stress on the animal than an acclamatory mechanism.
Experimental design: see above
Validity of the findings: see above
Additional comments: see above


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

Input:
Title: PHACTR1 IS ASSOCIATED WITH DISEASE PROGRESSION IN CHINESE MOYAMOYA DISEASE
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: In this study, yongbo Yang et al try to find potential association between gene mutations and disease progression in Chinese MMD. The results from whole-exome sequencing analysis on 31 sporadic MMD patients revealed that PHACTR1was associated with disease progression. However,of these patients, only 9 patients had disease progression and 3 of them had PHACTR1 mutant. Though statistical analysis was positive, I still  query the result reliability. More sample would be better.
1 All patients were ischemic type?
2 What is the criterion for disease progression ? Figure 1 only provide the DSA at admission, more details of follow up results of DSA should be added(disease progression evidence)
3 More limitations should added!


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: PHACTR1 IS ASSOCIATED WITH DISEASE PROGRESSION IN CHINESE MOYAMOYA DISEASE
Review round: 1
Reviewer: 2

Output:
Basic reporting: 1. In the discussion, the authors described the known relationship between RNF213 and MMD in detail. However, it is not the major finding in the manuscript. The author should consider rewriting this part. In addition, the limitation of the study was not mentioned in the discussion.
2. In the abstract, it is stated that “8 single nucleotide variant (SNV) were deleterious with PHRED scaled score >15”, which is not accurate and misleading. It should be PHRED-like scaled C-scores, while PHRED scaled score was considered as the quality measure of the sequencing results.
3. Some grammar mistakes should be corrected, such as line 133. “was performing” should be changed to “was performed”.
4. Since no RNA was used in the study, why the RNAeasy kit was mentioned in the line 118.
5. line 166, it should be “Santa Cruz” instead of “anta Cruz”
6. Some abbreviations were not explained. Such as line 152, MAF. I assume it should be “minor allele fraction”? if so, it should be “MAF <0.01” as the threshold. Also in line 153, it is not metioned the term “SO_IMPACT=HIGH”.
Experimental design: 1. The author used Chi-square test to determine the associations between SNV and disease progression. Considering the small sample size and some expected numbers are less than 5, it does not meet the prerequisite of Chi-square. An exact test should be performed.
2. Although the transfection of siRNA showed the reduction of cell survival after 96 h, it will be more persuasive if the rescue experiment is performed.
Validity of the findings: 1. In the results, the sequencing quality and depth was not mentioned, which is a very important factor to evaluate the results.
2. It is mentioned in the methods that “The filtered variants was compared with known MMD 155 related genes, such as RNF213, ACTA2, BRCC3, GUCY1A3, CCER2, R179H, C536G>R, HLA-156 B51, HLA-B35, HLA-B67, HLA-DR1, HLA-DQB1*0502”. Only some of the genes were mentioned in the following text. How many of the known related genes were identified in this work, as well as the potential explanation was not discussed.
Additional comments: The manuscript of Yang Y et al. performed whole-exome sequencing analysis between 31 patients and 10 healthy controls to identify the possible variants related to the progression of Moyamoya disease. They have found twelve predisposing mutations from 7 genes which may be potential, and 8 of them were predicted as deleterious by the bioinformatics tools. Moreover, they have performed experiments to confirm one of the SNVs in PHACTR1 and its function. Generally, the methods and results are clear; however, several major concerns should be addressed before this can be considered further 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: PHACTR1 IS ASSOCIATED WITH DISEASE PROGRESSION IN CHINESE MOYAMOYA DISEASE
Review round: 2
Reviewer: 1

Output:
Basic reporting: Now the manuscript is in a good form to be published.
Experimental design: The issues have been addressed.
Validity of the findings: The findings are substantially improved.
Additional comments: Manuscript of "PHACTR1 is associated with disease progression in Chinese Moyamoya disease" has been improved substantially over an earlier version. There are no further comments on the paper.


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

Input:
Title: INVESTIGATING THE POTENTIAL IMPACT OF 1.5, 2 AND 3 °C GLOBAL WARMING LEVELS ON CROP SUITABILITY AND PLANTING SEASON OVER WEST AFRICA
Review round: 1
Reviewer: 1

Output:
Basic reporting: The study gives information about the possible impacts of three different warming levels in the agricultural sector of West Africa. This geographic area has already been detected as very vulnerable to climate change because most farmers in the region are rainfed farmers and the local economic activity strongly depends on agriculture. Consequently, the food security of the regions is expected to be compromised in the near future. The authors used climatic and crop suitability information to create suitability models under current and future climates. I think that the data and methods used are appropriate to fulfill their research goal and that findings are novel and interesting.
In general, in the text it is possible to see that there are several points missing and there are extra spaces or capital letters when they are not necessary. Authors need to read their manuscript again in order to find these mistakes. I have some other specific comments.
Experimental design: It is an original research with a well defined structure and question. The technical an ethical standards are rigorous and methods are being described with sufficient detail.
Validity of the findings: I think the research and results are novel and important. Data to replicate the model are provided. Conclusions are well stated and linkes to original research question.
Additional comments: Abstract
Even when it is possible to identify the most important components of an abstract, your results and discussion sections are confusing. Your main results and conclusions should be highlighted and clarity. There is also a lack of connectivity between sentences that need to be attended, especially in the last part of your abstract.
Line 24- The first sentence of your result section in the abstract is not clear. What do you mean with marginal suitability line?
Line 31- Is it of or from?
Lines 36- “are most dramatic (…)”- are more dramatic on cereals, roots and tuber crops?
Line 37- “All the projected changes in climatic area suitability…” Clarify that it is for simulated crop suitability that only considers climatic variables.

Introduction
This section gives a good introduction about the importance of the study. However, I think that the introduction could be enriched by giving more information about studies that have been working with climate change and agriculture in the same geographic area.

Line 46- There is an extra space.
Line 65- Which century? The 21st century? In that case, it would be more appropriate to use the most recent scenarios’ reference from the IPCC, which are the RCPs.
 Line 65- A point is missing.
Lines 67- Have revealed that?
Line 98- ()
Lines 80-100- I think it would be better to summarize this information and not to write about it with so much detail. Instead, I would recommend mentioning some studies that have been dealing with topics related to this paper.
Line 101: Indicate which three are the different global warming levels and define IPCC in line 102.
Lines 111 and 116 –°C
112- A point is missing.

Data and Methods
Line 125- A point is missing
Line 129- Could you please give some references about the low adaptive capacity of the area and the reasons of why this adaptive capacity is so low in the agricultural sector.
Line 136- yam
Line 136- What does SSA mean?
Line 142- What do you mean by cash crops?
Line 153- What does RCMs mean? You have not defined it.
Line 158- EcoCrop? Ecocrop? Be consistent
Line 165- There is an extra point
Line 171- I am not sure that can call RCPs emission scenarios. You did not define an RCP. What are they? How many they are? What do they represent? Which are their unities?

Results
Line 268- Why do you write lat. Instead of latitude?
Line 309- February, March…
Line 403- “the region under?”

Discussion
It would be interesting to know if there is any field study in which it is possible to know if some adaptation strategies such as changing the planting months are already taken place in West Africa. Farmers’ traditional knowledge should be helping farmers realize that climate conditions are changing. How are they reacting to these changes? Is there a strong relationship between specific cultures and a cultivar? How difficult would it be for farmers to start growing what is climatically more suitable but not as attached to their culture?
It would also be interesting to mention the importance of other environmental factors to these plants’ suitability, such as soil. I understand that the focus of the work is climate change, but its is important to mention that there are other factors that might also be playing an important role in the future and that for now they are not being considered (limitation of the model).

Line 584- (
Line 593- ..
Line 597- under GWL3.0
Line 645- “These crops” “this crop”

Figure 1- There should be another way to better distinguish between the three areas. I think it is more important to distinguish between the three evaluated areas than showing the topography that is barely being mentioned 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: INVESTIGATING THE POTENTIAL IMPACT OF 1.5, 2 AND 3 °C GLOBAL WARMING LEVELS ON CROP SUITABILITY AND PLANTING SEASON OVER WEST AFRICA
Review round: 1
Reviewer: 2

Output:
Basic reporting: Overall the reading is relatively easy thanks to the use of standard, scientific English with a relatively concise style. However many typographic or syntax errors spread throughout the text made me stop on certain sentences just to guess the meaning. In many of these errors a verb or a word is lacking (‘e.g lines 77 what are the projected impacts, ‘are’ is lacking; line 99 holding temperature increase  below 1.5°C: "increase" is lacking, and see also lines 147, 224, 259, 273, 334, 344, 346, 356 to 359, 426..and then  I stopped noting them).

The manuscript is well structured. Its introduction and background are mostly appropriate. However, the introduction could give less room to well-known generalities about climate change & Africa, and instead focus a little more on the different ways of evaluating the impact of climate change on agriculture, in order to better justify assessing ‘crop suitability’.

The particular concept of ‘crop suitability’, which is absolutely key to this study cannot be used throughout without any definition as if it were a standard concept (as is yield). There are many ways of envisaging if a crop is practicable somewhere, depending not only on biophysical variables but also on economic or social ones. So please give the definition you refer to in this study, either right in the introduction or in the ‘Data and Methods’ section.

The captions of figures 1-3 are not adequate. The variable displayed in column 1 (suitability) is not the same as in columns 2-4 (change in suitability), thus the title ‘Spatial distribution of crop suitability as simulated by Ecocrop over West Africa for Hist. (column 1) and (column 2-4)’ is misleading. It should be changed to something like ‘Spatial distribution of crop suitability as simulated by Ecocrop over West Africa for Hist. (column 1, left axis) and of change in crop suitability (right axis) at different global warming levels (GWL1.5, GWL2.0, GWL3.0) under RCP8.5 scenario (column 2-4)…’ Please apply the same principle to figures 4 and 5 (planting month and change in planting month).

Raw data are not supplied but this should not be an issue since the  primary raw data used for the analysis and the software used are all available from the internet. The processed data of this paper has a great value precisely because the process is extremely demanding in terms of both expertise and labour time, so I don’t see why the team who obtained it would make it available without any counterpart.
Experimental design: The study is not particularly original, as it basically applies to a new case study the method from Ramirez-Villegas et al, 2013 (Ramirez-Villegas, J., Jarvis, A., Läderach, P., 2013. Empirical approaches for assessing impacts of climate change on agriculture: The EcoCrop model and a case study with grain sorghum. Agr. Forest Meteorol. 170, 67-78.). But the new case study is of substantial interest and novelty thanks to the assessment of the major crops of the region studied instead of only one. This gives the study the potential to better link the environmental analysis to social and economic issues, as it is conveniently said in the introduction.

The work is rigorous and well described except for the following key components:
-	1) An explicit and clear definition of the concept of crop suitability used in the paper is lacking

-	2) Crop suitability is many sentences confounded with change in crop suitability, resulting in a lot of confusing statements

-	3) Ecocrop model is not sufficiently detailed for a reader to fully understand the paper (and especially the differences in behaviour across the species accounted for in the study) without reading the references (Ramirez-Villegas et al, 2013, and Hijmans et al., 2001).

-	4) Default crop parameters are assumed to be adequate and the authors assume that they did not perform any calibration or new comparison between Ecocrop’s outputs and observed data, but nothing is said about how and by whom these default parameters were obtained or the model was previously evaluated against observed data. Lines 191-192 say ‘Previous studies have reported a good agreement between climate change impacts projections from Ecocrop model and other crop models’ and are followed by a number of citations, but the agreement referred to in this sentence has little to do with agreement between model and observed data. Who cares about a same thing said by many if these are as many liars ? Moreover, reading Ramirez-Villegas suggests that calibration is not straightforward and model results are extremely sensitive to these parameters. Therefore these key assumptions of the manuscript strongly jeopardize the way a reader can judge the validity of the study.
Validity of the findings: When crossing what is said in the paper with what is said in the key cited papers about Ecocrop model and its calibration, the validity of the finding of this manuscript is dubious.

Anyone with a little expertise on agriculture in West Africa would find at least one strong discrepancy between the real world and the suitability maps predicted by Ecocrop in this study for groundnut and cowpea under historical climate. The part of Senegal between 13.4° and 15.7° latitude and -16.6° and -14.3 ° longitude is known as the ‘groundnut basin’ and at least half of its the cultivated area has been holding groundnut for a century or so. And this zone was classified as unsuitable for groundnut in this study.

Due to this discrepancy, many key statements of the paper are abusive. The following one is especially irrelevant (lines 320-323): ‘These evaluation simulations demonstrate that the (RCA4-Ecocrop) captures the variation in suitability with different crops across the three AEZs of West Africa in the present-day climate and can serve as a baseline for evaluating the changes in crop suitability under global warming levels of 1.5 to 3oC over the region. The model also captures the growing season of crops over the region which varies with different months of the year’

As a result, the paper fails to link its environmental analysis with any socio-economic issues, which was the major condition for it to be a worthy contribution on top of that of previous works using Ecocrop under future climate projections.
Additional comments: Despite the manuscript has unacceptable weaknesses, it is obviously the result of great amount of dedicated work, and it does have a potential for becoming rigorous and valid enough to deserve publication in the Journal.

Therefore I would encourage the author to submit a carefully revised version addressing the weaknesses listed above. A proper recalibration of the Ecocrop model for all the species studied will be the most straightforward, albeit labour consuming solution to the issue #4 I raised in section ‘experimental design’.

The authors are of course free to find other ways to reconcile robustness of their conclusions with the uncertainties about the way simulated crop suitability matches observed crop distribution.

As a means to add value to the paper even when the uncertainties in the modelling exercise remain high, the authors should strengthen their discussion of the causes behind the differences between crops in responding to simulated climate change.


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: CLONING, EXPRESSION AND CHARACTERIZATION OF A CHITINASE FROM PAENIBACILLUS CHITINOLYTICUS STRAIN UMBR 0002
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The  work described in the manuscript entitle  “Cloning, expression and characterization of a chitinase from Paenibacillus chitinolyticus strain”, although not very new, deserves to be published in this Journal. Chitinases have great utility in different areas of Biotechnology, so the characterization and study of new enzymes with this activity would already constitute an interesting piece of work for biotechnologists. However, the following general and particular aspects must be improved.

General aspects
The main problem I see in this work is that many data that readers need to know to say if the work is novel, or not, have been omitted. For example, the characterized gene (the protagonist of this story) is very similar to different genes from organisms of the same genera, among them, from a different strain of the same species (Fig.2), and nothing is said about the % identity (sequence coverage!) of the corresponding encoded proteins, nor if there were any characterized chitinase from this microbial species. Nor is anything said about how many potential chitinolytic genes have been found in the genome of the Paenibacillus spp, and  P. chitinolyticus, or about sizes of the potential chitinases, which can be deduced from the genome already sequenced, or if had any of them been characterized from a functional point of view, etc.
In general, the full text should be reviewed and corrected.

Some particular aspects
1.	Ln 55; Chitin can be cleaved into chitosan!, it is beaks into chitooligosaccharides!
2.	Ln 57: GlcNAc or Glc NAc?, unify throughout the manuscript. Take care of the writing because this abbreviation is described in Ln 133 and is used repeatedly before!
3.	Ln 68; three structural families based on their structural motives not on their sequences!
4.	Ln 103; vector (no vectors) pET-22b(+) and it is not enough to say that it is already in a laboratory, indicate provider
5.	Ln 117; What kind of commercial chitin, in shrimp flakes? Is chitin powder already soluble in water?, and if not in what? and form colloids?
6.	Ln 118 ….acid mM?
7.	Ln 122; how the colloid mass was calculated to indicate concentration in g / L
8.	Ln 133; the definition of OD is indicated later in the text, in ln 166!
9.	Lns 139-142; genera of organisms are abbreviated from the 2nd time they are named!.
10.	Ln 182; which protein was used as a control pattern?
11.	Ln 204; Carboxymethyl cellulose/chitosan: suppliers, how are they prepared?
12.	Ln 217; gene was isolated from ..not cloned from..
13.	Ln 218; CHI was heterologously expressed  in …
14.	Lns 221-224, any explication for the 2 bands?,  Both have chitinolytic activity ?, could have done a triptic digestion and MALDI of both proteins to see if one is a product of hydrolysis or a less glycosylated protein variant?
15.	Lns 230-232; give data on the analyzed sequence, indicate found domains, position them by adding between what and what amino acids are the domains, etc ... Are there any sequence / domain of binding to Ca, Mg, etc. since they are then used and the activity of the enzyme changes?
16.	Ln 236, Fig 2. Phylogenetic tree: to give % identity and sequence coverage!!
17.	Ln268-280; Very repetitive, the data that are already shown in Fig 4 are described! and nothing is said about Mn, which is the one that produces the greatest effects! Sort and summarize all this.
18.	Ln 301..industrial applications, to give examples/references…
19.	Lns 317-322; mass of some non-totally acetylated chitooligosaccharide is also not detected in Fi8?, for example, that of 405.144 could be due to GlcNAc-GlcN, and if this is so, this should also be commented and discussed.
20.	Table 2, relative percent column, it says nothing, repetitive with the part of the specific activity; few data to justify a table. All this could be indicated in the text..
21.	Bibliography has to be reviewed and unified! now, before indicating the pages (, or :), the names of the journals abbreviated or complete, volume number in italics or not….


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: CLONING, EXPRESSION AND CHARACTERIZATION OF A CHITINASE FROM PAENIBACILLUS CHITINOLYTICUS STRAIN UMBR 0002
Review round: 1
Reviewer: 2

Output:
Basic reporting: It is difficult for reviewer to understand the contents of this manuscript, in particular introduction section. Authors should improve this manuscript throughout using language editing service.
Experimental design: Authors stated that One unit of chitinase activity was defined as the amount of enzyme required to produce 1 micromol of GlcNAc from colloidal chitin per min per liter of solution at 45 °C. Does 3,5-dinitrosalicylic acid (DNS) react with only monomer, GlcNAc? Does DNS react with reducing ends of oligosaccharide or of polysaccharide? Is it correct ‘per min per liter’, that is U/L? Why did enzyme reaction time require 60 minute at 45 degrees C? Authors should describe in a careful manner. For example, in legend of Figure 1 reviewer could not find ‘Crude extract’ and ‘250 mM imidazole’ in materials and method section.
Validity of the findings: Authors stated that ‘This is the first report that cloning, heterologous expression and purification of a chitinase (CHI) from Paenibacillus chitinolyticus strain UMBR 0002, and the results indicate that CHI is a good candidate enzyme for the green degradation of chitinous waste’. However, about CHI authors should emphasize what is superior to other reported chitinases, what is similar to other chitinases, and should discuss why CHI is different from other reported enzymes and is similar to them, because some chitinases from Paenibacillus sp. were well studied and a chitinase is one of enzymes that are more resistant to pH and temperature.
Additional comments: Line69 glycoside hydrolase families 18, 19 and 20.  Not glycoside hydrolase chitinase families
Line85 should refer a reference
Line88 Are enzyme activity (4.16 and 3.65 U/mL) high compared with other chitinases?
Line103 should state company etc. not stored.
Line 221 should show the zymogram. Could authors analyze both N-terminal sequences of two bands?
Line 232 Does CHI possess CBD at N-terminal side of catalytic domain?
Line 236 should compare with other reported chitinases that are well studied on phylogenetic analysis and show their amino acid sequences. Title of Figure 2, Amino acid sequence similarity tree, is strange. Reviewer could not access MN121846 on the National Center for Biotechnology Information.
Line 242 novel Streptomyces strain (Hoster, Schmitz & Daniel, 2005). Is it novel?
Line 265 purified CHI activity
Line 267-274 should explain why Mn2+ and Ca2+ increase CHI activity.
Line 280 should explain why authors think that Cu2+ and Fe3+ may destroy the 3D structure
Line 313 should state acetylated value or deacetylated value of chitosan. All glucosamine (GlcN)?
Line 320-322 It is known exo-typed chitinases could produce GlcNAc, GlcNAc2, and GlcNAc3. Therefore, the statement that CHI is endo-typed chitinase is questionable. If CHI has characteristics of endo-typed chitinase on primary structure compared with endo-chitinases, could discuss them.


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: CLONING, EXPRESSION AND CHARACTERIZATION OF A CHITINASE FROM PAENIBACILLUS CHITINOLYTICUS STRAIN UMBR 0002
Review round: 1
Reviewer: 3

Output:
Basic reporting: The manuscript needs extended revision from a native English speaker. This is a very good scientific work with good data and novelty. Due my native language is not English; no corrections on my behalf have been submitted.
Experimental design: No comments. The approach is pertinent and meaningful. Description of methods is good.
Validity of the findings: No comments
Additional comments: This is a very good scientific work; it only needs editing in English. I suggest the authors to get help in English to present their valuable work and submit again a reedited version to the journal.


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

Input:
Title: A LONG-TERM STUDY ON ZOOPLANKTON IN TWO CONTRASTING CASCADE RESERVOIRS (IGUAÇU RIVER, BRAZIL): EFFECTS OF INTER-ANNUAL, SEASONAL, AND ENVIRONMENTAL FACTORS
Review round: 1
Reviewer: 1

Output:
Basic reporting: There are two instances are missing a bibliographic reference to endorse the authors arguments:
- In the Introduction section, lines 85 and 86, where the authors indicate say “Fast responses to climate change are expected in systems where lotic conditions predominate, unlike reservoirs operated as lentic environments.”
- In the Discussion section, line 454 to 457, when the indicate “a. The primary productivity of algae is often lower than secondary productivity by zooplankton. Primary productivity by algae may not cover the high rates of assimilation by zooplankton. At this point, the zooplankton probably begin to consume suspended detritus or bacterioplankton. When this happens, TP could be a better indicator of food availability.”.

Finally, in Table 2 and the Supplemental data must be revised. The numbers are displayed with commas, where they should be stops. Ex: "3,313" should be changed to "3.313".
Experimental design: There are two instances that should be reviewed in the Materials & Methods section:
First, in line 144, the brand and model of the “portable digital devices” that the authors used is missing.
Secound, in line 202, the authors should explain, in the Materials & Methods section, why they transformed all data to log (x + 1).
Validity of the findings: The authors didn’t answer if the Salto Santiago and Salto Osório reservoirs are independent systems. That was the second hypothesis stated in the manuscript introduction. I think that it should be clearer in the conclusions.
Additional comments: The manuscript is very interesting and has been conducted with extreme dedication, evident in an impressive sample effort.
Owing to the fact that dam environments are not significantly influenced by seasonality, according to the authors, a long-term study, like the 16 years carried out in the reviewed study, may indicate how the zooplankton community varies between inter-annual climatic phenomena. Results such as these may greatly enrich many studies discussions, such as those concerning aquatic environments susceptible to eutrophication and toxicity processes caused by urban growth, species substitutions over time, as well as research concerning climate change effects on closed aquatic ecosystems.


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

Input:
Title: A LONG-TERM STUDY ON ZOOPLANKTON IN TWO CONTRASTING CASCADE RESERVOIRS (IGUAÇU RIVER, BRAZIL): EFFECTS OF INTER-ANNUAL, SEASONAL, AND ENVIRONMENTAL FACTORS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript titled “A long-term study on zooplankton in two contrasting cascade reservoirs (Iguaçu Ricer, Brazil): Effects of inter-annual, seasonal and environmental factors” is an interesting read. The paper focuses on a long-term compilation data from two reservoirs. Studies focusing in the understanding of zooplankton and environmental metadata are very important to possibility the variations of man-made lakes in a large temporal scale. The authors had a significant sample size which allowed them to perform a good statistical analysis, comparing two different reservoirs with different hydrodynamics and environmental conditions. Therefore, the authors could improve the discussion of the hypotheses and do provide evidence for its discussion and conclusion. The main hypotheses of the study should be presented and discussed more objectively. The Discussion section would need to address the aspects that support the changes in the zooplankton community in a more concise manner and supported by the real results obtained. An English revision is also suggested. Therefore, I would recommend major revisions to the manuscript that would make it suitable for publication.
Experimental design: No comment
Validity of the findings: No commet
Additional comments: General comments:

1.      The paper would greatly benefit from rewriting the Introduction using more relevant and recent references and more ecological theory could be included. The authors could also show how their work builds on previous research and how they reached their conclusions. It should be clear where and how this research fits in with this specific field and what knowledge gaps are attempted to be filled.
2.      Some results should be reanalyzed and rewritten. It is not clear, for example, if the sampling of the environmental variables was conducted at surface or in vertical profiles of the water, so it would be important to provide information on this.
3. The authors should emphasize that zooplankton studies may be useful in the prediction of long-term changes in dynamic aquatic ecosystems such as reservoirs and used in water quality assessment initiatives. They only considered this aspect in the final paragraph of the conclusions.
4.      The temporal aspects of the changes in zooplankton community are attributed by the authors to the eutrophication, but the trophic state index indicates a predominance of meso/oligotrophic conditions in the last 5 years in the reservoirs (mainly in lacustrine and downstream regions – supported by the ANOSIM test). The pattern of change in the zooplankton community should also be discussed considering this aspect.

Specific remarks:

L105 There is a contradiction here. The authors made the statement that “zooplankton richness, composition and abundance were negatively affected by ‘decreased trophic conditions”, but in the Discussion the eutrophication is considered the main trigger to the changes in the zooplankton structure.
L116 – “and is caused” … should be rephrased
L143 – Limnological parameters were obtained at surface of the water?
L151 – Data of water flow provided by ANA was measured in one area at the downstream of the reservoir? Details about the collection of these data should be provided. Precipitation values were also obtained from ANA through a local climatological station?
L 155 – suggestion: “The zooplankton samples (720 in total)”
L167 – Rephrased the last line “there were 720 samples in total”
L211 – “precipitation had no direct effect on water flow regulation”. How is this result supported by statistical analysis? This phrase is not clear, should be rephrased
L213 – Please see Fig 2. In 2005 and 2017 there were high peaks oh cumulative rainfall. Recheck the results.
L218 – “revealed that a small amount of eutrophication had occurred”… This phrase makes no sense. The trophic condition of the reservoirs is a dynamic, successional event.  Please rephrase
L346 – It should not also be related to the highest WRT?
L375 – Is this observation supported by the obtained results? The most abundant species of rotifers registered in the reservoir are planktonic, except Euchlanis.
L395 – How could the process of oligotrophication observed in the reservoirs explain the results?
L477 – the authors are considering again the aspect of fluvial transport of zooplankton, already considered in line 375. I suggest considering the aspects of global influence of environmental features of the reservoirs to discuss this aspect of the zooplankton community.


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

Input:
Title: A LONG-TERM STUDY ON ZOOPLANKTON IN TWO CONTRASTING CASCADE RESERVOIRS (IGUAÇU RIVER, BRAZIL): EFFECTS OF INTER-ANNUAL, SEASONAL, AND ENVIRONMENTAL FACTORS
Review round: 2
Reviewer: 1

Output:
Basic reporting: I believe that all revision concerns have been carried out.
Experimental design: I believe that all revision concerns have been carried out.
Validity of the findings: I believe that all revision concerns have been carried out.
Additional comments: I believe that all revision concerns have been carried out.


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

Input:
Title: A LONG-TERM STUDY ON ZOOPLANKTON IN TWO CONTRASTING CASCADE RESERVOIRS (IGUAÇU RIVER, BRAZIL): EFFECTS OF INTER-ANNUAL, SEASONAL, AND ENVIRONMENTAL FACTORS
Review round: 2
Reviewer: 2

Output:
Basic reporting: The authors of the manuscript made an appropriate correction to the text and clarified all the reviewer questions. The results are supported by appropriate statistical analysis.
Experimental design: Sampling design is appropriate for the main questions of the study. The authors clarified the review doubts about zooplankton and environmental data sampling. The manuscript is an excellent contribution to the ecology of tropical reservoirs, with emphasis on the potential of the zooplankton as bioindicators of environmental conditions.
Validity of the findings: The conclusions of the manuscript are linked to the main question and support the results.
Additional comments: The authors of the manuscript made an appropriate correction to the text and clarified all the reviewer questions. The results are supported by appropriate statistical analysis. The manuscript is an excellent contribution to the ecology of tropical reservoirs, with emphasis on the potential of the zooplankton as bioindicators of environmental conditions. In this way, I consider that the manuscript could be accepted for publication and would be an interesting theme for the Peer J readership.


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: REBUILDING SOIL ORGANIC C STOCKS IN DEGRADED GRASSLAND BY GRAZING EXCLUSION: A LINKED DECLINE IN SOIL INORGANIC C
Review round: 1
Reviewer: 1

Output:
Basic reporting: This is an interesting studying. But there are some critical problems in this study. Firstly, you haven’t explained the research question. Why did you do this study? And the Introduction only summarized the studies about soil organic carbon and ecological restoration. This is not enough. You should show the gaps, between the previous studies and yours. Highlight your own innovation.
L68-91: Please simplify this paragraph.
L94: The reference style should be revised.
L97: The same problem.
L116-124: Please extend the article review about SIC, which also played an important role in your article.
Experimental design: L148-151 Please adjust those sentences. The “At each of the nine sites,….” was looked too abrupt. You should explain the context.
L185-186 Why use the repeated measures ANOVA? Your time-variable looked like a kind of treatment, not real time-variable. Please check the statistic method. If other studies used a similar method, please cite it.
L187-189 Please simplify the explanation. I suggest you add the F value to the p value’s bracket in the Results.
L198 Which correlation analyses have you used? Pearson or Spearman?
Figure 1 Please detail the study area. Because it only showed the study city. The experimental area was not clean.
Validity of the findings: I think you should ask your colleagues to help you revise the Results and Discussion.
L226 “total soil C” or “total C stock”. It is not clean. Please revised it.
L200-252 The “Soil organic and inorganic carbon” should be reversed with the” Soil bulk density, soil moisture (SWC), and pH”. Because the third part of Results named “Total carbon stock percentages of the soil organic carbon and soil inorganic carbon pools”, which showed more relations with the “Soil organic and inorganic carbon”.
L217 Please present the table or figure one by one. And please put together the results of each table or figure.
L239-240 There is not necessary to repeat the table 4 in p value’s bracket.
L298 It is not necessary showed the name of the table and figure again in Discussion.
L341-343 The words are a bit exaggerated. And the same question showed L47-48. Please revised it.
Table 4 Please show the asterisk which could present the significance. And the software’s name should be discarded.
Figure 2 Why is no error bar disappear? Please explain it.
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: REBUILDING SOIL ORGANIC C STOCKS IN DEGRADED GRASSLAND BY GRAZING EXCLUSION: A LINKED DECLINE IN SOIL INORGANIC C
Review round: 1
Reviewer: 2

Output:
Basic reporting: (1) Very sorry for my own poor English, so no comment here is given on language level of this manuscript.
(2) In Table 4, add * or ** after the values of correlation coefficients
(3) Figure 1, strongly advise to delete the small chart on the top left corner due to the reason well known, and add longitude and latitude in the border around the chart.
(4) Figure 2, the error line should add in the curves of SOC and SIC as Figure 3 did.
Experimental design: (1) The method using a 6 m auger to collect soil bulk density samples should describe more clearly.
(2)  For the fenced plots, were the grasses planted by human or appeared and grew naturally? and any fertilizing or ploughing activity happened for the grasses in the fenced plots?
(3) From a statistical point of view, only three fenced years (0a, 15a and 30a) are insufficient to form a real time sequence, thus it is very hard to disclose the real change of soil carbon with the fenced year, the convincingness of the obtained results is insufficient. It is strongly advised to add 1-2 other fenced years to the time sequence!
Validity of the findings: no comment
Additional comments: The other following problems need to consider,
1. Ningxia in China is “autonomous region”, not “province”.
2. Why defined the depth as 500 cm, can the grass roots appeared in this study grow down to 500 cm or can the 425 mm precipitation can move down to 500 cm? If so, why seems no change happened to carbon below 200 cm as the study found.
3. mountain gray cinnamon and black loess, in my opinion, not as Spodosols and Inceptisols in USDA Soil Taxonomy, more likely as Alfisols or Inceptisols and Mollisols.
4. What is real soil types in the three kinds of studied plots? Is there any difference in the grass composition in the studied three kinds of studied plots? what is the method to get the grass coverages of the studied plots?
5. Table 1, there are obvious differences in the slopes even in the plots with the same fenced year, is there information available on the influences of different slopes on soil carbon?
6. The unit currently used for SOC and SIC is g kg-1, not %.


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: REBUILDING SOIL ORGANIC C STOCKS IN DEGRADED GRASSLAND BY GRAZING EXCLUSION: A LINKED DECLINE IN SOIL INORGANIC C
Review round: 2
Reviewer: 1

Output:
Basic reporting: The article has been well revised. There were only some small errors.
Experimental design: L180 and 185: in my opinion, it may be better to replace the "repeated measures“ by “mixed effect model”.

L186: the “x” should be replaced by “×” or “and”.
Validity of the findings: Figure 1B is it “C” or “c”

Please revise the Figure 2B and Figure 3B. The letters were too indistinct and ugly.

Figure 5
The figure’s orders should use “A)” which is consistent with previous figures.
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: CONDITIONED MEDIUM FROM M2B MACROPHAGES MODULATES THE PROLIFERATION, MIGRATION, AND APOPTOSIS OF PULMONARY ARTERY SMOOTH MUSCLE CELLS BY DEREGULATING THE PI3K/AKT/FOXO3A PATHWAY
Review round: 1
Reviewer: 1

Output:
Basic reporting: This article is clearly and unambiguously written and uses professional English language throughout. Sufficient reference to prior knowledge in the field is given. Article structure and production is professional, the raw data has been shared and the results are relevant to the hypotheses.
Experimental design: This article contains original primary research within the scope of PeerJ. The research question is well-defined, as is the knowledge gap. The methods need extra details adding in order to replicate, and rationale for some of the techniques needs to be provided (please see comments below). Ethics are fine.
Validity of the findings: The impact and novelty of this article are not clearly communicated - the mechanistic insight is an association rather than a definitive cause-effect relationship and so the discussion and conclusion needs to be presented as such. Underlying data has been provided and is sound, however some revision of statistics in Figure 1 needs to be completed (please see comments below).
Additional comments: This article is well written in an easy-to-understand manner and contains sufficient new experimental data. I have a number of comments that should be addressed prior to publication.

1. Discussion: The proposed pathway of M2b inhibiting PI3K / Akt / FoxO3A causing reduced proliferation, migration and increased apoptosis has not been definitively proven. Further experiments e.g. showing that restoration of these signalling pathways abrogates the functional effects of M2b would need to be completed.

2. Methods: How many SD rats were used for SMC isolation and how many for BMDMs? Were any used for both? What was the age of the SD rats at MCT injection?

3. Methods: Line 153 suggests a 1:1 ratio of the number of SMC and macrophages used in the experimental studies. Does this correlate with the ratio of SMC and macrophages in vivo in PAH? Also, does the n number refer to the number of SMC donors, macrophage donors or both?

4. Results: Line 324 says PI3K was 'blocked' however the data in Figure 5 shows only a ~30% inhibition of PI3K with the LY294002.

5. Statistics: The data in Figure 1 is a comparison of two groups and so cannot be analysed by one-way ANOVA. Please re-analyse using two-tailed t-test.

6. Methods: Fibroblasts can also stain positively for a-SMA. To definitively prove the presence of SMC, co-staining for both a-SMA and SM-MHC should be observed.

7. Methods: Was the cell cycle of SMC controlled by serum-starving prior to the proliferation experiments being conducted? If not, how do you know that changes in proliferative rate are not simply a result of different SMC populations being in different stages of the cell cycle? Would you expect these SMC to proliferate within 24h?

8. Methods: How can you be sure that the observed changes in migration at 24h are not due to the changes in proliferation? Also, the chemoattractant gradient in transwell chambers only lasts for ~8 hours so will not be present at 24h.

9. Figures: Figure 3A has an apoptosis rate of 0.05-0.18, whereas Figure 3B has an apoptosis rate of 5-15%. Please can you explain this discrepancy?

10. Figures: Figure 1A, Figure 2B and 2C, Figure 3A and Figure 5C all need scale bars, and Figure 1 needs n numbers.

11. Figures: The bands for Bcl-2 and Bcl-xl in Figure 3C are overexposed.

12. Figures: Bands 3 and 4 in Figure 5A for p-PI3K do not match with the densitometry.


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: CONDITIONED MEDIUM FROM M2B MACROPHAGES MODULATES THE PROLIFERATION, MIGRATION, AND APOPTOSIS OF PULMONARY ARTERY SMOOTH MUSCLE CELLS BY DEREGULATING THE PI3K/AKT/FOXO3A PATHWAY
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper is clearly written and generally easy to follow.  Literature is supportive of the manuscript scope with good coverage and breadth of the field.

I have provided minor comments for improvements to introduction, results, figure presentation and processing which i feel with strengthen the manuscript.

Introduction:
The introduction easy to understand – suggestions for text for improvement are below:
Text Minor Points:
Line 63: consider re-wording the opening line – the Tuder et al., (Tuder et al., 1994)’ is repetitive. Consider placement of reference here at the end of statement.
Line 73: can the authors give examples of the drugs used to target macrophages here.
Line 81: ROS in full first before abbreviation
Line 88: M2b macrophages are ‘recently regulated macrophages’ – the wording needs to be more clearly articulated.
Line 101: ‘We also explored the possible mechanisms’ – I feel this should be more elaborate.
Line 387: define DDS

Results Text:
Section 254-267:  This section needs to be more clear.  The authors use the supernatants from M0 and M2b for their assays.  For me, the effects observed in this section is therefore the result of the products released into the M0 and M2b supernatant, not the M0 and M2b directly themselves.  I think this needs to be more carefully worded.

Line 266: Can the authors clarify if it is M2b macrophages themselves that inhibit proliferation / migration (as stated) or is it the products released into the supernatant from M2b macrophages (lines 257-258). This is linked to the lack of clarity in the section above.  Can the authors comment here on this.

Results Figures:
•	Can the authors provide molecular weights for all Western blot data throughout the paper to indicate the band sizes of the proteins being presented.
•	The authors need to take care with the contrast adjustments and cropping made to blotting panels.  Please refrain from cropping close to the bands. See comments below.

Figure 1: Please state the number of repeats carried out for these experiments in the legend.
Panel A: Please provide the quantification data to support the >80% αSMA expression statement.  Scale bars are missing from the images. Please add this information to the image.
Can the author comment about the cells in the IF that did not stain for αSMC.  Was any other cell marker used to confirm the other cell population?
Figure 2: Panel C. The background of transwell M0 image has been adjusted and is clearly different from control and M2b. Can the authors explain this?

Figure 3: Panel A.  Apply scale bars to the images.  The IF images are not clear what the arrows are pointing at.  It would be better to apply the arrows to the merged image rather than DAPI with a zoom into a defined area.  Whilst the authors provide an n number for this experiment, can the authors indicate in the legend the total number of PASMCs counted across the N=5.
Panel B: The flow cytometry figure needs to be bigger. The text size on the axis is small and cannot be easily viewed.
Panel C: the blotting signal in the representative blots for Bcl-2 and Bcl-xl looks saturated which makes it difficult for reliable densitometry data to be quantified. Please provide representative blots that are not saturated (less exposed).
Panel C: The cleaved caspase band has almost been cropped from the blot. Please adjust this blot panel to that the band is not at the edge of the panel and more centrally aligned.

Figure 6: Panel A: Flow cytometry quadrant plots are too small which makes the axis and information difficult to read.
Panel B: Bax blot panel is cropped too close to the top of the protein bands.  Please adjust.
Experimental design: Overall the methods are clear with sufficient details to repeat experimentation.  Additional information is required at key parts prior to publication.  See below:

Minor points:
Line 105: Age of the mice should be included and explanation of why only make mice were used for this study.
Line 152-153: ‘The stimuli of a certain number of PASMCs…… by the same number of macrophages’. Clarity is needed here in this statement.  This needs to be more scientific.  The authors need to define the cell number here.
Line 239: ‘The cells were then tested’.  This needs to be more clear – what assays? More details are needed here.
Validity of the findings: The study reveals interesting results that demonstrate differences in M0 to M2b macrophage upon PASMC function.  The findings in the manuscript would be of interest to the field.  The authors clearly acknowledge the limitations to the study with the secreted products of M2b macrophages being unknown.  Knowledge of these products would add impact to the paper however I do recognise that this would mean a significant volume of additional work which I feel would be unfair to request the authors to do. That would be a whole new paper in itself.  I do request that the authors be more clear in the conclusions/abstract. I feel the authors needs to state that it is the supernatants from the M2b (and therefore the unknown products that they secrete) that give rise to the effects. At the moment it reads as if it is the M2b macrophages directly.

With the minor changes that i have recommended, I feel that the paper would be of interest to the readership of PeerJ.
Additional comments: No further comments to include.  Please see individual comments related to the different section.  Thank you for submitting your work to PeerJ.  It was a pleasure to peer review your paper and I hope the comments can help you improve areas of the manuscript.


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

Input:
Title: MUCOACTIVE AGENT USE IN ADULT UK CRITICAL CARE UNITS: A SURVEY OF HEALTH CARE PROFESSIONALS’ PERCEPTION, PHARMACISTS’ DESCRIPTION OF PRACTICE, AND POINT PREVALENCE OF MUCOACTIVE USE IN INVASIVELY MECHANICALLY VENTILATED PATIENTS
Review round: 1
Reviewer: 1

Output:
Basic reporting: Basic reporting
Clear and easy to read language and form.
Introduction and rationale is clear with relevant literature.
Figures are clear.
Experimental design: Experimental Design
The study is reporting on 3 different surveys of clinical practice, perception of benefit and point prevalence use of mucoactive in ventilated patients. The design is appropriate to answer the aim of the work.

I would have like to see the exact questions that were asked in each survey and how phrased to ensure they were not leading - could the authors add this in supplementary documents.

I believe there is a review that should be referenced (Icard et al, Expert Rev Respir Med. 2017 Oct;11(10):807-814.). I do not think there are other meta-analysis or systematic reviews
Validity of the findings: Validity of the findings
This study reports the widespread use of mucoactives in ventilated patients in he UK. Although this is known anecdotally this is the first survey to show this and present the need for confirmatory studies to prove their efficacy or indeed harm in this patient group.
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: MUCOACTIVE AGENT USE IN ADULT UK CRITICAL CARE UNITS: A SURVEY OF HEALTH CARE PROFESSIONALS’ PERCEPTION, PHARMACISTS’ DESCRIPTION OF PRACTICE, AND POINT PREVALENCE OF MUCOACTIVE USE IN INVASIVELY MECHANICALLY VENTILATED PATIENTS
Review round: 1
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: The response rate to the practitioner level survey is quoted as 37% which is the proportion of ICUs who returned at least one reply. But the unit for analysis is the individual practitioner (n =255/3099) which suggests a lower response rate of 8%. This should be acknowledged in the text. It would also be useful to see if the 255 respondents were spread evenly across the units or if there were a concentration of replies from individual units. Likewise, reporting at least some results by role of respondent may be useful (of those who supported the idea of a clinical trial, how many were doctors/nurses/physiotherapists? What was the response rate in each of these groups)? At least one additional table showing the results in more detail would help – I would suggest two additional tables, one describing the characteristics of the responders (how many units, how many people, summaries of distribution of people across units, and counts and response rate by role) and one giving more detail of the responses by unit and role.
Additional comments: The results are presented in figs 1 to 4 using Borda counts, this should be explained in the methods section to aid interpretation by the reader.


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

Input:
Title: THE IMPACT OF SLEEP LOSS ON SUSTAINED AND TRANSIENT ATTENTION: AN EEG STUDY
Review round: 1
Reviewer: 1

Output:
Basic reporting: 1)Summary: The summary needs to be re-written as it is not clear enough.
- Particulalry, please remove the term "novel finding" as it is now adequate here, given the rest of the summary.
- Also, please be more precise with the EEG method.
- The relationship between teh results described and the conclusion are not clear enough and this should be modified.

2) Introduction
- The paragraph from ilne 46 ("Considerable empirical evidence...") is nto clear. Why are you referring to the central nervous system? I also miss a clear conclusion related to Owen 2009, more precision are needed.
- I miss a reference related to the effects of sleep loss on attention.
- Why are you talking about fatigue? This is different from vigilance/attention etc, please remove as it is not appropriate.
- I miss references and global conclusions related to the effects of sleep loss on both the PVT and the AB.
- EEG paragraph: The first sentence lacks precision. The sentence line 102 ("However, the majority") lacks a conclusion and more precise information related to the importance of sleep restriction versus total SD. I also miss the effects of the one versus the other.
- In the EEG part, I also miss the link between sleep loss and its effects on EEG, notably on alpha.
- You refer to AB performance in the middle of various forms of attention, pelase correct (line 112).
Experimental design: Study 1
2) Methods:
- Did you assess actigraphy? If yes, it should be reported.
- According to me, training shoud be done 1 week before the actual study and not just before, this can create a bias and authors should aknowledge for this is the discussion.
- The PVT description should be more precise.
- In the statistical analyses, did you check for noramality and homoscedasticity and adapted your statistical analyses in function?

3) Results:
- You did not assessed sleep but actigraphy that record sleep-wake alternation. This is different and should be changed in all the manuscript.
Please replace sleep restriction by SR in the PVT part.

4) The discussion is very short and the second paragraphe should have been in the introduction. Please adapt the manuscript according to these comments (ex: maybe remove the discussion for the Study 1).

Study 2:
2) Methods:
- It is not clear if you used the same participants?
- I am not sure about the valiidity of FitBit, do you have references?
- Why did you use a dark room in the second study and not in the first one? This could consitute a bias. Surprisingly, the second study is very precisely described in its method compared to the first one.
- EEG please add the name of the reference and its placement.
- Why did you use PSychophysics for Study 2 and not study 1? What about the timing accuracy in both cases?
- Wy did the PVT changed?
- Why EEG was done eyes closed and not eyes open? What would have been different?
- I miss references related to each method point and its justification in the EEG paragraph. I also miss an explanation related to the lack of analyses on other frequency bands.
- Why did you use a sliding window for analyses? And not a global analyse? The EEG part is really unclear to me, particulalry in the justification of methods used.
- Statistical analyses: Which factors did you use in the ANOVA?
Validity of the findings: 3) Results:
- Be aware that you are not assessing sleep and correct for this, please.
- Please remove all part related to methods (normality etc) and place it in the appropriate section.
- Please be clear that EEG was completed before task and eyes closed!

4) Discussion
- First paragraph: if you refer to tiredness, please relate it to KSS results instead of alpha ones.
- The explanation line 493 is not clear and seem wrong to me. Please remove or adapt (slow wave and alpha).
- Please be more specific about the consistent findings in previous studies.
- Please remove the sentence line 507, this is not useful.
- The second "explanation" is not an explanation, this is an interpretation of you results. Please modify.
- The last pragraph is nto useful ad partly inappropriate, please remove.
Additional comments: The current paper report results from 2 studies related to the effects of sleep loss on attention.
The paper is globally clear but lack precision at several points. In addition, some methodological issues need to be discussed.
General comment in all the manuscript: Please be more specific when you can, also more precise and with references at each point. Also, please remove the term "sleep" and be clear that EEG was done before task completion and eyes closed.


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

Input:
Title: THE IMPACT OF SLEEP LOSS ON SUSTAINED AND TRANSIENT ATTENTION: AN EEG STUDY
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript appear to be clear and unambigouous in the writing. English (as it appears to me) is professional.
Literature references are complete, giving a sufficient scenario of the reach background of this reserach field.
The structure of the article conforms to an acceptable format of ‘standard sections’. Figures are surely relevant, but in my opinion, they should be reduced in number.
Hypotheses are weel tested and "answered".
Experimental design: Aims and scopes of the manuscript fall within the area of interest of the journal.
The manuscript clearly defines the research question, that results to be relevant and meaningful. As a consequence, the knowledge gap is univocally identified.
Methods are clearly described, so that replication is possible.

Nonetheless this, I have serious concerns related to the choice to use FitBit as a reliable measure of actigraphy. Actigraphy is a well-known and accepted measure in psychophysiology; it can provide a direct measure of motion and activity and a sufficiently reliable indirect measure of sleep.at the same time it is surely useful as a compliance index when deprivation studies arre carried out. FitBit in my opinion is absolutely not acceptable as a professional measure of sleep, and the authors did in study 2 (section 7.1).
As a consequence, I strongly suggest the AUthors, to delete all the section in which a commercial device is proposed as a professional technique.
Validity of the findings: Good level of impact and noveltu/originality of the findings.
Results are statistically sound and controlled so that findings can be generalized.
Conclusions well stated and linked to the original question.
Additional comments: In general it is my opinion that the present manuscript is of interest for the readers of the journal and that can be easily imporved and made acceptable 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: THE IMPACT OF SLEEP LOSS ON SUSTAINED AND TRANSIENT ATTENTION: AN EEG STUDY
Review round: 2
Reviewer: 1

Output:
Basic reporting: All comments have been adressed.
Experimental design: All comments have been adressed.
Validity of the findings: All comments have been adressed.
Additional comments: I would like to thank authors as they adressed all my comments. Regarding the sleep term, I feel that the reader will be aware of the limit of using actigraphy as an objective measure of sleep (maybe authors could just add a small sentence related to this) and I accept the modifications that have been done.


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

Input:
Title: THE IMPACT OF SLEEP LOSS ON SUSTAINED AND TRANSIENT ATTENTION: AN EEG STUDY
Review round: 2
Reviewer: 2

Output:
Basic reporting: The Authors managed all the concerns I raised in my previous reviewing. As a consequence tha manuscript can be published in its present form.
Experimental design: see point 1
Validity of the findings: see point 1
Additional comments: see point 1


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

Input:
Title: ORIGIN IDENTIFICATION OF MIGRATORY PESTS (EUROPEAN STARLING) USING GEOCHEMICAL FINGERPRINTING
Review round: 1
Reviewer: 1

Output:
Basic reporting: Generally clearly written, though some minor issues with sentence structure and grammar exist.
There are some places in the intro that could use a bit more explanation (see general comments section). For example, more could be presented about the known migration patterns and distances for starlings relative to the study region and site delineations. But overall the context is clear and the intro has a logical flow.
There are numerous examples where statements are made without any citation (see general comments section).
The figures are generally relevant and of high quality. However, I have a couple of suggestions for improvements (see general comments section for details). For example, Figure 1 would be a lot more informative with more information about underlying geology dictating the regional trace element landscape. And all three figures could use more clear indications of site locations to help orient us in spatial distribution.
The Zscored trace element data are present in the raw data file but I don’t see the original ICP-MS and ICP-OES data.
Experimental design: This manuscript certainly reflects original primary research within the scope of PeerJ. I think the research question is clear, well defined, and interesting/valuable. The rationale for need is generally pretty clear, though it seems as though the authors were simultaneously arguing that little is done with trace element fingerprinting in bones so we don’t know if it works (not really true as trace elements in bones have been use for some time now to look at geographic origin in a wide range of species) and also applying it with the assumption that it does work.
The methods could be a bit clearer. In particular, there is very little information about the regional geology that establishes the geospatial patterns in trace element profiles. It would be useful to see that on the figure and discussed in the “Study Area” section. It could even be used to make hypotheses about site separation that could be tested with the data presented.
Little information was presented about the birds sampled (size, sex, age etc.) that could be used to help interpret the patterns in the context of movement ecology.
Validity of the findings: I think the authors did a nice job interpreting their data, but there are several important assumptions made that I think need to be clearly identified and discussed (see general comments for details). My biggest issue is that it is really challenging to be certain of site identifications if you do not have all potential sources clearly characterized. The classification model is only as good as the data you put in. So if you only have a subset of the sites characterized, the model will do look to assign groups to those sites. You clearly showed that there can be significant variability on short spatial scales within your study region. So why couldn’t that same variability exist outside the study area such that there are other regions with similar geology to your study sites? Similarly, in L366-371 you argue that some birds could not be assigned to origin sites because they are from areas between the sampling locations and trace element signatures varied over small spatial scales. I feel like this line of reasoning is exactly why it is challenging to say whether the birds that had values distinct from your juvenile source locations were immigrants or not. They could just reflect local sites not sampled.
I’m also interested to know how stable are the geospatial trace element signals. The juveniles representing source locations were collected in one season and year, yet the adults were collected over more than a decade. How variable are the source signals seasonally/interannually relative to spatial across the different potential origin habitats?
The authors often discuss the results providing “high spatial resolution” over “small spatial scales” but these are very qualitative metrics without reference to the movement scales and habitat scales of the study system. Small scale is very different for a starling vs a wandering albatross. So unqualified statements like this are a bit empty. Similarly, statements like “The selected trace elements may provide the best marker for tracing the origins of starlings and similar birds.” (L375-376) are not really accurate. The elements selected are specific to your study region and underlying geology. They are not universally the best. A region with different underlying geology will likely require a different suite of elements to properly characterize those sites.
Additional comments: L2: No need to include an abbreviation for European staling if you don’t use it again in the abstract

L6 etc.:  Some issues with comma usage need to be addressed. E.g., No comma after contaminating food (L6). Include a comma after (Cabe 1993) (L28). Include a comma after parasites (L33). Comma after In 2003 (L52), and many more

L13-14: I’d suggest rephrasing to “…classified juveniles to their natal origin (minimum discrimination distance of 12 km) with 79% accuracy.”

L14-17: I’m a little confused here. Is this saying that 11% were local and 89% were not local, and of the 89%, 55% were from the northern portion of the valley or 55% of all birds were from the northern portion of the valley?

L18-20: How did you determine the spatial accuracy? You would need independent validation to determine that the birds actually came from those locations (e.g., tagging work coupled with trace element work). Also, how do you quantify “high degree” and “small geographic scales”? these are qualitative metrics relative to the organism and question at hand. Small geographic scales for a non-migrant mean very different things than small scales of a global migrant. This could use a bit more explanation, e.g., high degree of accuracy relative to typical migration distances etc.

L22: When were European starlings introduced? Is this a new threat or something that has been here for decades or centuries?

L24: Is the IUCN status of least concern the metric of consideration for it being one of the most successful non-native species?

L26-36: These five reasons seem to lack some key citation. This first example seems a bit vague, citing a government report on starlings. What do you mean by adaptive in nature? Is this all linked to being a generalist forager? Where is the evidence of them being resilient and adaptive to extreme and diverse habitat conditions (no citations here)? Some added citations clearly assessing their resilience and adaptation would be useful here. Similarly, there’s no citation at all for the broad claim that predators, parasites, and diseases are not sufficient to inhibit populations growth. There’s also no citation for the North American population size.

L37: You introduced an acronym EUST in the first sentence but then don’t appear to use it. Please be consistent here. I personally prefer spelling the name out. EUST does not seem to be standard and the abbreviation really doesn't save much space.

37-47: There is a lot of information here that seems like it should have citations. Where is the quantitative evidence that starlings cause significant financial loss to farmers in the region? Similarly, there is no citation for “large flocks destroy fruits…” Since this paper rests on the notion that these starlings are significant pests, the sources of this information should be documented.

L47-49: Are these figures for damage caused by European starlings? If so, state that. If not, then this sentence is a bit misleading and should be modified to reflect that.

L50: Propane cannons!?! I’ve never heard of those but it sounds crazy.

L54: Citation for this statement about industries supporting the program.

L57-59: Again, to make a claim that numbers of starlings are increasing, you need to have a citation that shows quantitative evidence.

L67-70: These techniques are definitively potential techniques, but they aren’t the only techniques. People use population genetics, tagging/tracking techniques etc. I suggest removing “the” from in front of potential methods to make it clear that these methods are the only options used. Similarly, the markers can be indicators of origin, but they aren’t always. Plenty of isotopes record information about things other than origin (diet, trophic dynamics, metabolism etc.) and there are plenty of times where isotopes and trace elements don’t clearly distinguish origins because the sites do not have different signatures. This is all just a case of phrasing (easy fix), but makes a big difference in the intent and interpretation of the statements.

L71: There is very little discussion about the known movement patterns of starlings. How far do they travel and over what time scales? Do they undergo daily migrations, seasonal migrations, ontogenetic migrations? Do they return to their natal origin repeatedly or do they leave and not return?

L74-75: Why not use both? Isotopes and trace elements record different mechanisms of variation, which can complement each other and improve accuracy.

L84: Conversely, the bone also integrates over the lifetime of the bird. So if the bird is several years old, the vast majority of the bone signal will reflect life outside the natal origin. How do you control for the relative input of signal in bones? The older the bird gets, the more diluted the natal signal.

L91-93: What was the metric for determining “the best”? Accuracy, precision, cost, time, relative ease?

L93-94: I think this section needs a lot more attention. The entire study hinges on solid geographic separation of source regions based on trace element profiles. So there should be a clear discussion of the patterns and drivers of distribution, the stability of the signals, the spatial scales of separation relative to starling migration patterns etc.

L104-115: I’m struggling a bit to figure out why this information is really critical for the study area description? This seems like an expansion of background info already presented in the intro, but not directly relevant to the methods of the study. More useful information here would be the shape of the valley and the distribution of habitats in relation to bird migration, discussion of the bedrock distribution and resulting geospatial trace element signals etc. These info are critical to evaluating the use of this fingerprinting technique for tracking movement patterns.

L120-121: This sentence is a bit awkward. Consider rephrasing to “We obtained fresh and frozen samples, with each bird representing a single sample.”

L124-125: This technique needs a citation.

L127: What does “shortly after”

L117-131: I’m a bit confused by this section. The topics jump back and forth between collecting adults and juveniles. I would recommend reorganizing this a bit. First the sentences about juveniles representing local source signals needs to be moved to the beginning of the paragraph before talking about how many were collected and where. I would then talk about collecting since they are being compared to the juvenile source signal. I’m a little confused about the difference between the adults collected by SCP since 2003 and the “problem birds” collected in the Valley in 2015. Where were the rest of the adults collected? What makes a bird a “problem bird”? What are the sample sizes from the SCP and what are the total sample sizes for juveniles and adults. How many regions did you sample and how did you define those regions (by habitat, by cardinal location in the valley, by distinct trace element signals)? I’d like this section to be a bit clearer and straight forward as to how many birds were collected, what life stages, what regions, and what years.

L121-123: How stable are the geospatial trace element signals. The juveniles representing source locations were collected in one season and year, yet the adults were collected over more than a decade. How confident are you in the accuracy of your source location signals? In aquatic systems, terrestrial bedrock provides the trace element signal in rivers, which get recorded in anadromous fishes. To look at natal origins, scientists have to ground truth the source signal to the season and year in which the fish occupied that habitat (e.g., characterize the source signal in 2015 and look at one year old fish in 2016 or two year old fish in 2017 etc.). The source signal will change not only as a function of bedrock type (very stable), but also temperature, precipitation, growth conditions of plants taking up the mineral signal etc. (much less stable). How variable are the source signals seasonally/interannually relative to spatial across the different potential origin habitats?

L134-137: I know I’ve been harping on adding citations, but I don’t think you need multiple citations for each step for standard protocols like drying to room temp or weighing or putting a sample in a Teflon tube. At best include the citations at the end of the sentence, but honestly I would just cite steps that are unique to this protocol since you already cited Norris et al. 2007.

L157-160: What about selection based on what elements help discriminate geographic regions? The Szep et al. 2009 paper cited as evidence of using the elements to look at migration was working Europe and western Africa. There is no reason to believe that those same elements should be the best choice for western Canada. You should be able to determine the predicted elemental composition based on bedrock maps of the region. This would be a much better justification for use.

L184: Trace Element Multivariate Analysis is really a component of the Statistical Analysis of Data and should be included in that subsection.

L193: How did you determine “site”? There was never really and discussion of what qualifies as a site beyond the southern fruit and northern dairy portions of the valley.

L223: Here and throughout, it would be useful to more clearly differentiate headings and subheadings. E.g.,
Results
Spatial separation of source population of starlings in the Okanagan Valley

L226: I don’t think the Results section should be the first time we are told that there are 10 potential juvenile source locations. There should be a much clearer discussion earlier in the methods about what those sites are and how they were determined.

L230-232: I don’t think a single sentence should be a stand-alone paragraph.

L258-259: This is nice.

L261: How do you define “immigrant”? Is it a distance away or simply that they don’t match the juvenile source signals? Could there be regions within the valley that were not characterized?

L278-280: This is not a proper sentence “Out of which…”

L286-287: First off, there’s no citation for this statement that results from your study were comparable to feather-based studies. Second, I’m not really sure what this means. The statement is a bit vague. In what ways were they comparable? The absolute distances, the distances relative to bird movement scales, the distances relative to geographic bedrock variation?

L287-293: Local/regional scales is very subjective and will depend on the species. That said, between continents seems larger than local to regional scales.

L295-297: Again, I’m a bit confused by this comparison. The exact distances are case specific. The spatial scale will depend on the geographic composition of bedrock, which is site specific, and whether or not that separation scale is useful will depend on the species. For example, one site might change bedrock type on the scale of kms and the other 100s of km. Similarly, for a bird that migrates 100s of km, separation at the scale of 10s of km might be great, but if the bird travels kms, then separation at the scale of 10s of km isn’t very helpful.

L301-304: I feel like there is plenty of evidence for this. These phrases make it sound like this was in question.

L305-307: I’m quite confused by this sentence. First, I’m trying to figure out what it adds to this discussion and second, I’m not sure what you mean by “phenotypic quality”.

L315-317: How old were the “juvenile” birds? The elemental signal in natal origin birds would reflect the diet of the adults feeding the them until they can feed on their own. When they are fed by the adults, their signal will reflect the spatial integration of the adult foraging range. How far to the adults travel to feed? In other words, how do the spatial scales of adult foraging compare to the spatial dimensions of the a priori sites selected? If adults forage in a radius beyond the local site level, then the “local signal” could actually reflect a much wider spatial scale that presented. Similarly, how long have the juveniles been feeding on their own, which would presumably reflect the more local signal without significant dispersal?

L325-328: 79% is not really an assessment of the degree of spatial separation or degree of differentiation, but rather an indication of reclassification accuracy.

L330-334: This information should be expanded upon. You could even turn this into hypotheses of site separation that you could test with your bird trace element profiles.

L336-342: This paragraph starts out saying the results can be compared to other studies, but then it doesn’t actually do that. I would suggest starting with an assessment of your results first, then talking about how your results compare to other studies, with specifics.

L346-348: The line “This implies that…” is repetitive of the sentences before.

L348-349: It would be helpful to have a clearer description of the known migration patterns in the intro to set up the context for interpreting the movement patterns determined from this study.

L353: How do you know that they were from Northern BC? I thought the evidence you had was just that the profiles didn’t match the juveniles you sampled.

L355-357: Why would a higher number of dairy farms lead to higher immigration? Are dairy farms more desirable than fruit farms?

L360: You've already spent much of the discussion talking about immigrants, so this definition here seems out of place.

L363-365: I don’t quite follow this line of reasoning. You clearly showed that there can be significant variability on short spatial scales within your study region. So why couldn’t that same variability exist outside the study area such that there are other regions with similar geology? There have to be maps of bedrock geology for the region which could be cross referenced with the signals from this study to make predictions about regions of similar trace element signal in areas within the migration range but outside the study area.

L366-371: I feel like this line of reasoning is exactly why it is challenging to say whether the birds that had values distinct from your juvenile source locations were immigrants or not. They could just reflect local sites not sampled.

L375-376: This is an odd statement. The elements selected are specific to your study region and underlying geology. They are not universally the best. A region with different underlying geology will likely require a different suite of elements to properly characterize those sites.

L377: Again, these are very qualitative metrics “small scale” and “high precision” without reference to the movement scales and habitat scales of the study system. Small scale is very different for a starling vs a wandering albatross. So unqualified statements like this are a bit empty.

Figure 1. Can you put the site names on the map to help orient us in the other Figures? The map would also be a lot more informative with more information about underlying geology dictating the regional trace element landscape. Outlining the spatial boundaries of the 10 collection sites and two major farming regions would also be helpful for context.

Figure 2. Can you order the names from North to South like in Fig 3 to again help orient to spatial distribution?

Figure 3: Can you adjust the color bar to provide a bit clearer distinction among the 10 sites. The all blue spectrum makes it really challenging to differentiate.