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: PREDICTING PINUS MONOPHYLLA FOREST COVER IN THE BAJA CALIFORNIA DESERT BY REMOTE SENSING
Review round: 3
Reviewer: 1

Output:
Basic reporting: Okay.
Experimental design: The stratified estimators of overall accuracy, areas, and standard errors must be reported in sufficient detail that the reader understand how they were calculated and can replicate the analyses.  This is a non-trivial issue and requires that the revised paper be reviewed before acceptance.
Validity of the findings: Okay,
Additional comments: GENERAL COMMENTS:
Do not submit papers without both line AND page numbers.

The authors have used the stratified estimators correctly, but they need to include the estimators (the formulae) so the reader understands how the estimates were calculated.  Readers should not have to search the literature for information that is crucial for understanding the current study. How was overall accuracy estimated?  How were the area estimate and its standard error calculated?  What is W_i in Table 4?

As per previous versions of this paper, the first dictionary definitions of terms such as “high”, “low”, “over”, “under”, etc, refer to height, altitude, or vertical position, whereas the first dictionary definitions of terms such as “large”, “small”, “greater”, “less”, etc, refer to size or amount.  Despite widespread use to the contrary in the applied literature, perhaps the latter terms can be used in scientific papers to refer to size or amount.  Technical writing consultants strongly recommend using terms with only one meaning or definition, or if a term with multiple definitions is necessary, then the use the first definition.  Further, use of “high” to mean “large” is not well-defined.  What are the rules for this usage?  For example, would you characterize a large stone as “high”?  Lines 44, 242, elsewhere.  The authors stated in response to the last round of review that they had corrected this problem.

In statistics, the term “multivariate” refers to multiple dependent or response variables.  What were the multiple response variables?  Do not confuse “multivariate regression” meaning multiple dependent variables with multiple linear regression meaning multiple independent variables.  Further, the term “multiple” is only used for linear regression whereas here it is logistic (not logistical) regression.  Lines 261, 274, Table 4 caption, elsewhere.

SPECIFIC COMMENTS:
Line 63:  How can a tree be distributed?  Is it not the species that is distributed?

Line 37:  Should “valuation” be “validation”?

Lines 40, 235:  What does the number to the right of +/1 sign indicate?  Standard error?  Half-width of the confidence interval?

Line 77:  Correct the typographical error:  “the  The.”

Line 77:  First, the sensors are not used; rather it is the band values.  Second, band values cannot be used to “analyze vegetation” because they only characterize the intensity of reflected light.    Rather, they can be used to “predict” vegetation attributes.

Line 167:  At best, the classification can be used to “predict” types of land cover, and then only with error or uncertainty.

For Table 3 (error matrix), place “Reference” as a horizontal heading across the top.


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: PREDICTING PINUS MONOPHYLLA FOREST COVER IN THE BAJA CALIFORNIA DESERT BY REMOTE SENSING
Review round: 3
Reviewer: 2

Output:
Basic reporting: No more comments.
Experimental design: No more comments.
Validity of the findings: No more comments.
Additional comments: Thank you for making the necessary corrections.  I will now recommend to the editor that your manuscript be accepted as it is.  Cheers!


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: DENSITY AND POPULATION VIABILITY OF COASTAL MARTEN: A RARE AND GEOGRAPHICALLY ISOLATED SMALL CARNIVORE
Review round: 1
Reviewer: 1

Output:
Basic reporting: Generally looks fine to me (thanks, authors—written clearly is most places).

It might be helpful to include a layout of the trapping grid used for collaring, which I’ll discuss below.

L139—suggest “local convex hull (LoCoH)” and then using acronym rather than vice versa.

I suggest CRI rather than CrI as the acronym for Credible Intervals. In some places (e.g., L 249), you use plus/minus to denote a range—for clarity/ consistency, I would just stick with presenting CI or CRI for estimates rather than SE, and present means and range (rather than SD [? Not described]) when summarizing raw data.

L256: the t-stat and p-value suggest no difference, but I think also presenting estimates of territory size by region with CI would give the reader a little more information.

L290: The juxtaposition of the first two sentences in this paragraph is awkward. I think your point is that the observed anthropogenic mortalities, rather than evidence of a large population, instead suggest that the smaller population is at risk.

L301: Can you reword this? “Additional resolution” reads a little awkwardly.

L305: Rather than disproportionate, suggest saying greater or larger. Not sure why “nesting birds in plowed fields” needs to be explicitly included in this sentence.

Generally, the discussion seems a little less fully formed than other sections of the manuscript. I’ll revisit this in section three, but want to note it here because some issues with interpretation may simply be issues with the clarity and structuring of the writing.

From looking at the code and the text, it’s not clear to me how density is being estimated or when the masking is taking place: is D estimated as N-hat/Area with or without the masking of specific cells, or as the mean of the estimated point process intensity, or?

The data is set up in a standard flat format, which is fine and easier to store: for transparency, I might just add a comment to the code file indicating that the input data needs to be manipulated prior to model fitting.

Table 1: The input value for m here doesn’t seem to have any connection to the studies you cite—typo?

Table 4: Could you present p0 parameters as p0[male] and p0[female]? It’s not immediately clear which sex is which as presented.

Fig 1: Could you add an additional inset showing the distribution of cameras/traps? They don’t show up well here.

Fig 2: Instead of Mortality = x (which seems deterministic), how about Average Mortality = x?
Experimental design: I guess I interpret this part of the review as pertaining to methods/implementation. This is a clever design for answering the questions of interest, and the sampling effort (and the data collected) seem sufficient.

Several questions about how density was estimated.  Throughout, I suggest describing this as a spatial mark-resight study rather than spatial mark-recapture (the same acronym is fine) because the model incorporates unmarked and marked detections.

1)	A more detailed description of how unmarked observations and telemetry observations were integrated within the text is necessary for a reader to figure out what was performed without digging into code. Royle et al. use telemetry to get a better sense of habitat use (e.g., habitat/environment based changes in lam0 related to third order resource selection), while Sollmann et al. use telemetry exclusively to derive sigma (as performed here). The description of how of unmarked detections were integrated is similarly opaque (but seems to follow the likelihood described by Chandler and Royle in the 2013 AoAS paper). Please include some fundamental parts of the likelihood pertaining to these components of the model.

2)	Could you provide more detail regarding the spatial configuration of the live-trapping effort in relation to the camera trapping effort? One assumption of SMR models is that the spatial distribution of marked and unmarked individuals is essentially the same, but it’s tough to evaluate this without a sense of where the live-traps were placed. My sense is that this assumption is being violated (it seems like marked detections far outweigh unmarked detections, and that marked animals are much more exposed to sampling than unmarked animals), and it can lead to bias/poor coverage (see recent paper in Journal of Applied Ecology by Jesse Whittington et al. regarding “Generalized Spatial Mark-Resight” for a description of the issues and models to deal with them).

3)	I’m generally all for integration of disparate data sources to improve estimate precision. But one risk of integrating different data sources to estimate a shared parameter is that if the parameter is not ‘shared’ between datasets, you’re going to get a (precisely) biased estimate (There’s a paper “Balancing precision and risk” by Tabitha Graves et al. [2012] in Plos One that describes this nicely). I have some misgivings about integrating the telemetry and detection data in this case because I’d expect that baiting at cameras might be altering animal space use. Previous studies have suggested that incorporating telemetry data from a few individuals has basically no effect on estimates of density, but in this case, most of the data used to estimate sigma are derived from telemetry data: if ‘telemetry sigma’ is actually smaller than ‘trap sigma’ (which is what I'd surmise), shrinkage in estimates of the shared parameter might lead to overestimating marten density. Although Viorel Popescu’s 2014 paper with fishers implies that there probably is no consequence of combining these data types, I guess I would feel more comfortable with integrating the telemetry data if you could provide some evaluation of their consistency or sensitivity to their consistency. Maybe the easiest way to evaluate sensitivity is to see whether estimates change very much if the telemetry data are removed.

4)	The observation likelihood is off. Y is treated and described as a Poisson RV, but you seem to be imposing restraints to make it behave like a Binomial RV wherever possible (e.g., you’re placing a natural limit on Y based upon the number of days a camera operated because defining Y as the number of days in which an individual was detected [the exact # successes in K trials that defines the Binomial distribution], and modeling variability in the intercept using a logit function). My guess is that you’re forcing this as a Poisson observation model to allow the unmarked data to be integrated following Chandler and Royle 2013—but that observation model isn’t necessary to integrate the unmarked data. I’d use a Binomial/Bernoulli observation model instead: the unmarked component of the model should look a little more like the what is described by Chandler and Clark 2014 (Methods in Ecology and Evolution 5[12]) or David Ramsey et al. 2015 in the Journal of Wildlife Management (79[3]). For consistency with the literature, use p[i,j,k] and p0 rather than lamda and lam0 when using a Binomial/Bernoulli observation model.

5)	Because the stations are baited, I think that incorporating a behavioral response to initial capture (probably a trap-specific behavioral response) using an indicator covariate is probably important.  This is typically modeled using a Bernoulli encounter model. The Bernoulli likelihood will take a little longer to run, particularly with an imhomogenous point process model—here's a description of a tip that might help speed things up (https://groups.google.com/forum/#!topic/spatialcapturerecapture/v4KA8rSuX7Y). One caveat: in my limited experience working with unmarked Spatial Count type models, estimating a behavioral response has been tricky, and it may be impossible without additional information. I think the marked animals should provide sufficient info to allow a behavioral response to be modeled, but if you can’t, I think presenting your results as conservative estimates of population size is probably ok.

6)	The chains used to generate MCMC samples seem short—in particular, the burn-in of 500 iterations seems insufficient. Are you sure that you are sampling from the stationary posterior distribution? The Geweke diagnostic might be useful for checking this.

7)	Please provide a little more clarity regarding masking out habitat.  As far as I can tell, you fit the inhomogenous point-process model without masking out anything, but masked out non-habitat when predicting? I think it is reasonable to mask out sand-dunes when predicting density into the other region (it doesn’t look like the camera transect is really set up to capture the effect of forest cover on marten density all that effectively), but as noted above, it’s a little difficult to figure out just how abundance and density estimates presented are is being derived here (it seems like it’s derived from mu[g]).  As noted below, if estimates reflect masking habitat out after the fact, comparison with other studies is a little trickier.

Territory mapping: My sense is that demonstrating what you did within a graphic (perhaps adding onto to Fig. 3) might make interpretation easier. There seems to be disagreement within the text over what the territory mapping is estimating (carrying capacity, or actual population size). I’m not really convinced that this is a great method for doing either, and I don't see this as a necessary part of the paper, but maybe there's a compelling reason for keeping it that I'm missing. Regardless of how you prefer to interpret these predictions, if you keep this part, I think some discussion of the assumptions being made about marten space use and some justification for these assumptions is probably warranted.

PVA: generally seems fine, although I’m not qualified to review this with any technical depth. A couple minor questions regarding clarity/implementation. Why treat human-caused deaths as a Poisson RV, if only to later argue that anthropogenic mortality is not stochastic (Line 300)?

Given that the Poisson is skewed, maybe extinction at higher expected values is really being driven by sporadic but extreme mortality events? The modeled variation in anthropogenic mortality exceeds the range of observed harvest…is there sufficient empirical data to inform an alternative generating distribution for this variable? Could you add a little justification for choosing lambda values of 1,2,3 (e.g., we select these values to explore sensitivity to limited increases, or we assume that baseline mortality is higher because roadkill may go unreported, etc.)?

Could you provide a more detailed justification for assuming these population as lacking immigration in the methods (on L312 you note barriers, distance, etc., but can these things be quantified and presented in the methods)?

Finally, I think might be useful to incorporate uncertainty into the PVA projections (I think confidence intervals could be derived from non-parametric bootstrapping).
Validity of the findings: I guess this section pertains to presentation/interpretation of the results.

L269: As presented in the methods, the territory mapping was used to estimate marten carrying capacity rather than abundance; here it is treated as an additional technique for estimating population size.

L278 & L285: I’d say 2-3 annual mortalities on average instead of 2-3 mortalities.

L299-315:  Maybe this point belongs under basic reporting, but the focus here is unclear. The take-home of the PVA is that relatively low levels of anthropogenic mortality put these populations at risk. I’m not sure why juvenile recruitment is being mentioned here as another potential factor, and then summarily dismissed. I'd suggest focusing upon your own results a little more closely throughout the discussion.

L316-329: Two comments. First, I’m not sure that density estimates based on masking out non-suitable habitat are really comparable to density estimates reported by other studies. You’re reporting density per sq. km of suitable habitat; other studies typically report density per sq. km of land. I’d at least note that this is likely to amplify your estimates relative to other systems.

Secondly, do you think you could expand upon upon some of your predictions and alternatives here? An alternative is that rather than the distinct vegetation in this system mediating marten co-existence with other animal species, the animal community in the system is distinct (as you mention, year-round passerine birds). Or perhaps sympatric predators are less abundant in this system—martens in Newfoundland readily use beetle-kill and clearcuts that provide little cover, but sympatric predators are relatively rare (Hearn et al. 2010, Journal of Wildlife Management 74[4]). Presumably, the cameras provide some information about other carnivores in the study area?

L330-L335: I suggest avoiding any discussion of trying to manage inland forests to resemble coastal forests.

335-338: This is really the main finding of the study: this is an important but vulnerable marten population. I suggest that rather than ending with this sentence, you shift it earlier into the discussion and talk a little bit about how maintaining habitat and limiting mortality might be accomplished.
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: DENSITY AND POPULATION VIABILITY OF COASTAL MARTEN: A RARE AND GEOGRAPHICALLY ISOLATED SMALL CARNIVORE
Review round: 1
Reviewer: 2

Output:
Basic reporting: This is a well-written article. the authors used up-to-date references. I suggest that Buskirk et al (2012) in Aubry et al.'s book, be cited to support statements in lines 314-315.
Experimental design: This is a well-designed scientific research with a proper inductive review of the problem. There is a bit of confusion regarding the habitat preferences of the Humboldt marten. The introduction indicates that the species is found in late-seral stages - and such stages are present in federal parks where the habitats are protected. However, there were no marten surveys in these parks.  The martens are apparently found in 70-yr-old forests (study area). So it is incorrect to conclude that the species is a late-seral specialist (line 64). So the authors need to explain the discrepancy - either the species is wrongly believed to be a late-seral species, or the martens may use younger forests (as in the study area) - in the latter case, th presence of martens in young forests may be due to the fact that there is no other habitat at regional level or the food items are very abundant and the species is more flexible in its choice of habitats.
Methods are properly detailed. However, lease indicate the models and manufacturers of remote cameras.
Why do they authors refere to "territory" instead of "home range"?
Validity of the findings: The conclusions follow the data.  The findings are significant and may play an important role in the conservation of the species
Additional comments: Good work. the marten-habitat relationship needs to be better described and explained in the introduction. Please consider the following:

Line 58, martens instead of marten.
Line 93 - The Oregon Dunes consist of...
Line 131 - 5 min instead of 5 minutes
Line 133 - hrs instead of hours.
Line 184 - within one (or 1) hour - no hyphen.
Lines 252 and 275 -  >40% forest cover - please specify the cover (age and structure).
General note - your argument that, 'because of human-caused mortalities and limited habitat, the future of marten population may be jeopardized' relates to the level of resiliency of the species, a concept that has been developed by Banci and Proulx (1999- Mammal Trapping published by Alpha Wildlife Publications).


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: DENSITY AND POPULATION VIABILITY OF COASTAL MARTEN: A RARE AND GEOGRAPHICALLY ISOLATED SMALL CARNIVORE
Review round: 2
Reviewer: 1

Output:
Basic reporting: The one minor issue is that it looks like sigma and maybe some other greek symbols are being altered, which makes following some of the formulas difficult. For example, I can't quite figure out what's happening on line 187.
Experimental design: Thanks for the work put in here to alter some of my previous concerns. I just want to frame the following by noting that these are pretty advanced models that can be difficult to implement, I appreciate the effort the authors are putting into this, and I don't want to hang things up for no reason. With that said, two comments/questions:

1) Regarding the marking process (y.trap): you're sure that baseline encounter probability is constant? There's no trap-happiness or trap-shyness associated with actual trapping (as was implemented for the camera resighting)?

2) More substantively, the resighting process. A) In looking at the code and what I can make of the formulas in the text, you have a resighting process that consists of i) marked individuals that can always be identified, and ii) unmarked individuals that cannot be distinguished, but not iii) marked individuals that cannot be distinguished, correct? (Whittington et al. dealt with all three, but if there is no iii, the general structure here looks fine).

B) This is going to a big blob of text for which I apologize; I don't intend to be pedantic, but want to make sure you are comfortable with how you are modeling this and make sure that the model is valid, so:

There are basically two ways to model the unmarked component. In the first, your unmarked data are basically counts of detections during specific intervals, where each latent encounter history is Poisson distributed (an individual can be detected multiple times). The station-specific detection total per interval or overall can be treated as the sum of these latent individual Poisson variables (or you could marginalize over the latent encounter histories). Something like:

lambdaresight[i,j,k] <- lam0.resight[i,j,k]*exp(-d.resight2[i,j]/(2*sigma2[Sex2]))*z*(1 - marked[i]))
log(lam0.resight[i,j,k]) <- delta0 + delta1*Sex[i] + delta2*Baiting[j,k]
countu[i,j,k] ~ dpois(lambdaresight[i,j,k]
nU[j,k]~dsum(countu[1, j, k], countu[2, j, k].....etc.)

Alternatively, you might just look at presence-absence by station (i.e., there's >0 detections or not), in which case the likelihood looks a little different: the underlying encounter model for an individual follows the bernoulli model you have here, with the recorded presence-absences at a station = 1-(1-punmarked[i, j, k])^Nunmarked. Something like:

p_unmarked[i,j,k] <- lam0.resight[i,j,k]*exp(-d.resight2[i,j]/(2*sigma2[Sex2]))*z*(1 - marked[i]))
logit(lam0.resight[i,j,k]) <- delta0 + delta1*Sex[i] + delta2*Baiting[j,k]
Ptrap[j, k]<-1-prod(1-p_unmarked[,j,k])
yu[j, k]<-dbern(Ptrap[j, k])

As far as I can tell, you are treating the total # of unmarked marten pictures as arising from the sum of latent Bernoulli encounter histories. This is potentially problematic, because it implies that x marten detections = x martens were detected. A little more detail regarding how the unmarked data are defined (an image? an image sequence? >0 images during a day?) would be useful, and should dictate which formulation you use.

The data file suggests there is never >1 unmarked detection during an interval. Depending upon how the unmarked data are defined, this might mean that your formulation works okay, although you might wish to note that your formulation is not going to be correct in many circumstances.

I don't want to eat up a ton of space getting in the weeds here: I'll sign this, and if anything does not make sense or could use clarity, please reach out and let me know.

John Clare
University of Wisconsin
jclare2*at*wisc.edu
Validity of the findings: No issues.
Additional comments: The authors should be commended for putting a lot of work into revising the submission, and more generally, for attempting to tackle the underlying study problem with a high level of technical rigor. This is nice work, and I appreciate the thorough response to previous 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: DENSITY AND POPULATION VIABILITY OF COASTAL MARTEN: A RARE AND GEOGRAPHICALLY ISOLATED SMALL CARNIVORE
Review round: 2
Reviewer: 2

Output:
Basic reporting: Clear and unambiguous.
Experimental design: The text benefited from the comments expressed by Referee # 1 in the first review.
Validity of the findings: Very important findings.
Additional comments: I have  a few comments only.
1. Considering that trapping may impact significantly on the population survival, I recommend that all forms of trapping be eliminated within and outside the area of concern. Accommodating trappers on the outside (so you capture more male juveniles than females) can still impact on the marten population in your study area. Martens have the ability to find baits set far away and these baits on the outside could cause displacement of some animals. Trap sets outside the study area could still impact on the population survival. Since we are talking about survival of a species, measures should be taken to avoid all deaths. You may not be able to stop vehicles, but you can remove trapping.

2. The reference "Banci and Proulx 1999" is missing in Literature Cited:
Banci, V., and G. Proulx. 1999. Resiliency of furbearers to trapping in Canada. Pages 175-203 in G. Proulx, editor, Mammal trapping, Alpha Wildlife Publications, Sherwood Park, Alberta.

3. Figure 1, legend = The verb tenses need to be reviewed. For example, you used the past tense in "the study area was bonded..." and the present tense for "This area has extensive fragmentation...".  I suggest the authors harmonize the verbs, and use the proper tenses. For example, the study area is bonded (and it still is!), but the area had extensive fragmentation (at time of study).

4. Figure 2, legend. I think that lines 535-541 should be included in Methods, i.e., line 152.

5. Line 544 - Home ranges or territories?


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: HERBARIUM SPECIMENS CAN REVEAL IMPACTS OF CLIMATE CHANGE ON PLANT PHENOLOGY; A REVIEW OF METHODS AND APPLICATIONS
Review round: 1
Reviewer: 1

Output:
Basic reporting: English writing needs improvement to make the writing concise. Please remove redundant information. More detailed comments were provided after general comments.
Experimental design: No comment
Validity of the findings: No comment
Additional comments: This study summarized the approaches and applications of using herbarium specimens to analyze the changes in flowering phenology in the last decades. This is valuable work. The general and detailed comments are provided as below.

General comments:
(1) The authors need to briefly introduce how the phenology data (such as mean flowering day of year or first flowering day of year) are obtained from the herbarium specimens. Are they the dates when herbarium specimens were collected? This is important information for readers who are unfamiliar with this type of data.

(2) Many studies have shown that the inferences from herbarium specimen data are comparable to findings from field observations. What are the advantages and disadvantages of using herbarium specimens than field observations, especially in the future when field observations are being recorded more? Do herbarium specimens provide any extra data than field observations? Please briefly discuss it.

Detailed comments:
L55: “temperature regressed on year” does not represent the changes in phenology. Please rephrase this sentence.
L56: “but other approaches may be suitable in some cases” Please clearly point out what are “other approaches”, and “some cases”.
L64-66: the last sentence in the abstract is loosely related to the approach reviewed by this study. Please revise it to focus on the important role of herbarium specimens in studying the changing rate of phenology under continued warming.

L69: please provide the reference for Carl Linnaeus’s study of phenology.
L71: please provide the original reference for “Charles Morren who introduced the term around 1850”
L84: 2017 -> 2015?
L82-84: Please explain why herbarium specimens may be useful for these different cases.
L94: “model set”? Do you mean “procedure”?
L97: correlations of what? Change of what? Please specify.
L104: “or some combination of these with multiple regression models”. Please explain or delete.
L105. This could be more concise. For example, “whether flowering day was earlier in warmer years, whether flowering day got earlier over years.”
L119: Is there any reason herbarium specimens were not used in tropical region? I don’t think the availability of herbarium specimens data is one reason.
L122: provide -> provided
L130: This is redundant: “we only selected studies that met the all three eligibility criteria”. Because you just referred “Studied were eligible for this review if they met three main criteria”
L164: some significant trends? Vague expression. Please specify.
L354: discusses -> discussed


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: HERBARIUM SPECIMENS CAN REVEAL IMPACTS OF CLIMATE CHANGE ON PLANT PHENOLOGY; A REVIEW OF METHODS AND APPLICATIONS
Review round: 1
Reviewer: 2

Output:
Basic reporting: .
Experimental design: .
Validity of the findings: .
Additional comments: This is a well-written and well-organized review of the plant phenology.  This paper will serve as a useful introduction to the field for researchers who want to start conducting research in the field, and effectively lays out the basic types of analysis in this field.  Over the past few months,  there have been several important papers in this field that make this paper seem somewhat dated.  First, Willis had an article in TREE that outlined how herbarium specimens could be used in climate change, now that millions of specimens are available on-line. Second, Pearse had an article in Nature Ecology and Evolution describing a new statistical technique for combining peak flowering dates from herbarium specimens with first flowering observations in the field. And third, Daru had an article in New Phytologist about the biases of herbarium specimens. This article needs to be revised in light of these three recent articles.
The article describes the use of monthly average temperature data to compare to with flowering times.  However, many researchers in the field prefer to use growing degree data. That said, a review article by Basler demonstrated that both types of analysis yield almost identical results.
In the article, the authors suggest that mean flowering date is better than  first flowering date because first flowering date is more variable. However, the reason that first flowering dates are problematic is that they are affected by many sampling issues, especially changing population size over time. Populations that decline over time will have later first flowering dates even with the mean is the same.
A key concluding point is that the herbarium specimens could be used for other phenological characters, such as leaf out times. The authors seem to be unaware of the two 2014 papers that do exactly that  by Zohner and Renner in Ecology Letters and by Everill and others Am J Bot.
Finally, a key point made by the Willis paper which needs to be emphasized is that this field is ready to undergo a huge expansion now that millions of herbarium specimens are becoming available on-line.
If the authors can revise their paper with these points in mind, this paper could become a useful contribution.


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: OLIGOTROPHIC WETLAND SEDIMENTS SUSCEPTIBLE TO SHIFTS IN MICROBIOMES AND MERCURY CYCLING WITH DISSOLVED ORGANIC MATTER ADDITION
Review round: 1
Reviewer: 1

Output:
Basic reporting: This is a nicely written clear account of a factoral experiment to determine the impact of plant leachates on methylmercury production in a freshwater wetland.

There are a few newer reviews that should be included in subsequent revisions.

Symbols on figures would be better a bit larger.
Experimental design: The subject is entirely appropriate for PeerJ.

The methods need some work.  While many of the methods included in the supplimental materials should stay there, there is quite a bit of details required in the main paper to make the methods clear.  I have added what I think is needed in comments on the text file.
Validity of the findings: I can not comment on the statistical analysis.

The data is robust.

I think that there needs to be some work on the implications of the use of 16S methods to determine the microbes present vs. the fact that just because they are present, doesn't mean they actually methylate.  More details in comments in the text file.
Additional comments: Nice paper.  I look forward to seeing the revised manuscript if deemed appropriate by the editors.


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: OLIGOTROPHIC WETLAND SEDIMENTS SUSCEPTIBLE TO SHIFTS IN MICROBIOMES AND MERCURY CYCLING WITH DISSOLVED ORGANIC MATTER ADDITION
Review round: 1
Reviewer: 2

Output:
Basic reporting: This is a well-written manuscripts on the impacts of DOM to mercury methylation in vegetated and unvegetated microcosms.
Experimental design: Experimental design was well done. Statistical tests were generally correct and sound.
Validity of the findings: The findings on the effects of leachate on microbial community structure is the most important finding different from previous study.
Additional comments: Line 53: citation by publication time or alphabetic order of first author?
Line 67-68: need to know where is St Louis River, there is another one Florida.
Line 188 and Line 191: “at XXXXXX”?
Line 227: why was SUVA>7 removed?
Line 249-250: you may use Spearman Rank correlation if data were not normally distributed.
Line 271: should be ug/g wt  sediment.
Line 279-280: leachate did  not stimulate MeHg in vegetated sediment but did increase MeHg in oligotrophic unvegetated environment. Why?
Line 292-303 This is a multi-discipline study. Maybe not all the readers understand all aspects of the technical work. I would like to see for example, which group of methylators require sulfate and not require sulfate. Giving the name of the microbial group is not sufficient.
Line 388: it seems this is contradictory to Line 279-280 if I don’t read it wrong.
Fig 1: +/- may be expressed as ±


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: NO TEARS IN HEAVEN: DID THE MEDIA CREATE THE PSEUDO-PHENOMENON “ALTITUDE-ADJUSTED LACHRYMOSITY SYNDROME (AALS)”?
Review round: 1
Reviewer: 1

Output:
Basic reporting: It's fine.
Experimental design: It's fine.
Validity of the findings: Legit
Additional comments: “Tears in heaven” by Wicks & Lancashire takes a closer look at “AALS”.
The paper is interesting and quirky. It will be sure to draw media attention.
The style of the paper is tongue in cheek throughout. This is most noticeable at the end of the conclusions: “Therefore this study may be considered a precursor to
a more robust experimental design.”. Sure. Also, table 3. This is not necessarily a problem, as most of the comparable literature is dry as dust and not conducive to anyone actually reading it. In that sense, this was quite refreshing.

Assuming that the authors are actually serious, here is my review.

Strengths:
*Most people ask turkers to do too much, specifically for too long. There is only so much a turker will do. The authors to not make this mistake, as they keep their survey at much less than 5 minutes (which I consider to be the max a Turker will do without resorting to cheating).
*The authors provide a plausible mechanism as to why the phenomenon might have gained traction. It is fairly obvious what is going on. People watch more movies that tend to elicit crying (dramas and family movies) on planes (probably due to the available selection) and they are exposed to more movies on a single trip than during an entire year on the ground, with selective remembering and confirmation bias doing the rest.
*The authors are willing to report a “non-result”. This is very important and should be supported.
*The paper is well written. This is rare enough to note it here.

Major concerns:
1.	Are the authors fighting a strawman? Most of the people cited in the background are directors and movie people. I was entirely unaware of an impending epidemic of AALS, didn’t even know it is a thing. I fly a lot, but have never seen anyone cry on a plane (of course, I have seen many people watch movies on planes, including myself). As the authors state themselves, there are no academic studies on this. Their own pubmed search came up empty. Then again, it is important to dispel myths and urban legends before they gain much traction. Then again, why does it matter what a couple of neckbeards in their basement posting on the internet believe about who cries on planes? The authors would be well advised to google the “Mandela effect”. Thousands (millions?) of people online are willing to believe that it is more likely that the Illuminati changed the timeline of history rather than questioning the perfect veracity of their memory.
2.	As the authors do report a non-result, adequate power is critical. I strongly advise the authors to elaborate and clarify their power analysis. I must confess that I do not understand it. As far as I can tell, no suitable power analysis was performed. This is particularly important as what the authors report relies on the pilot data, which might misrepresent the true effect size. This is true both for the section on power, as well as anywhere else power is mentioned in the manuscript, e.g. when talking about the Learning curve analysis. I did not find this compelling. Please clarify/elaborate. Moreover, 1,000 participants sounds like a lot, but it really isn’t. In this context, it is important to note that Turkers are not actually real people in this sense. There are all kinds of problems with Turker samples, see for instance https://osf.io/cv2bn/

Minor concerns:
1.	I was surprised that turkers fly so much. And saw a movie on the plane – so were presumably flying long distance. Is this plausible, given that they work for minimum wage on the internet (less than other jobs in the gig economy, e.g. Uber drivers)? In other words: Do turkers fly (this much)? A priori, I would have expected Turkers to be the least like sample to do so, and thus the least suitable to address this study. Maybe I misunderstood what the authors report, but I don’t think so.
2.	Please clarify the modeling of the crying behavior. The text (and the model) implies that crying was binary (cried or not), but the table suggests otherwise.
3.	219: (Saheli) is Saheli 2017, no?
4.	264: Learning curve analysis? This comes out of nowhere. Elaborate.
5.	In general, put a space before an opening parenthesis. They seem to be missing throughout. Which makes me suspect the authors did this on purpose.
6.	Title suggestion: Shouldn’t it be “no tears in heaven”?
7.     The authors keep talking about their deep net. But this doesn't really seem to be well motivated at all. Or integrated into the rest of the manuscripts. All results are in terms of the logistical regression. What happened to the deep net? Why mention it at all, if it is not used?


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: NO TEARS IN HEAVEN: DID THE MEDIA CREATE THE PSEUDO-PHENOMENON “ALTITUDE-ADJUSTED LACHRYMOSITY SYNDROME (AALS)”?
Review round: 1
Reviewer: 2

Output:
Basic reporting: The review of relevant literature was thorough and well-organized. The authors situated the current research well within the "era of fake news," clearly articulated the importance of evaluating claims that have become commonplace in the popular media. I have no substantive suggestions for changes. My minor critiques are as follows:

•	There appears to be a missing citation on line 77.
•	I do not have experience using Mechanical Turk. In the shared data file, could “RespondentID” numbers be used to identify specific users of M-Turk, or are these ID numbers generated by the researchers? I just want to be sure that the data have been adequately anonymized.
Experimental design: I request that the authors add a statement to the paper confirming whether they have reported all measures, conditions, data exclusions, and how they determined their sample sizes. The authors should, of course, add any additional text to ensure the statement is accurate. This is the standard reviewer disclosure request endorsed by the Center for Open Science [see http://osf.io/project/hadz3]. I include it in every review.
Validity of the findings: Although I had a good laugh while reading Table 3, I question whether its content has a solid empirical foundation and whether it adds substantive value to this paper. I will leave it to the handling editor to decide.
Additional comments: This manuscript was a pleasure to read. I literally laughed out loud at a few points. Laughter while reviewing can be a death knell for a manuscript, but it was not in this case. The authors provided valuable (and scientifically sound) myth busting and did so in an engaging manner that will be appealing to the readership of PeerJ. My critiques are minimal and should be easily addressed.


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

Input:
Title: NO TEARS IN HEAVEN: DID THE MEDIA CREATE THE PSEUDO-PHENOMENON “ALTITUDE-ADJUSTED LACHRYMOSITY SYNDROME (AALS)”?
Review round: 2
Reviewer: 1

Output:
Basic reporting: Good
Experimental design: Good
Validity of the findings: Good
Additional comments: Thanks for addressing my concerns and taking my suggestions seriously. I think the manuscript is actually improved. So... good job?


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: NO TEARS IN HEAVEN: DID THE MEDIA CREATE THE PSEUDO-PHENOMENON “ALTITUDE-ADJUSTED LACHRYMOSITY SYNDROME (AALS)”?
Review round: 2
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: I am satisfied that all of my concerns have been addressed. Kudos on a fun and interesting myth-busting exercise.


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: REFERENCE GENE SELECTION FOR QRT-PCR ASSAYS IN STELLERA CHAMAEJASME SUBJECTED TO ABIOTIC STRESSES AND HORMONE TREATMENTS BASED ON TRANSCRIPTOME DATASETS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The English language should be improved to ensure that the readers can clearly understand your text. Some examples where the language could be improved are highlighted in the annotated PDF file. The current phrasing makes comprehension difficult. Typing errors should also be corrected.
Experimental design: The section of materials and methods raises several doubts that should be clarified, namely:
1-	The authors should include in the text a justification for choosing these particular 10 candidate genes (RGs).
2-	No justification is given for the use of the concentration of 300mM for salt treatment nor the percentage of 20% of PEG for the drought treatment. Have the authors done some previous studies that show that these concentrations are adequate to induce the stresses?
3-	In the case of plants obtained from seeds in which the variability will certainly be high, three biological replicates may not be sufficient to guarantee a good sampling, four replicates should be the minimum. Please explain why you did not use a greater number of plants in each treatment.
4-	As the authors point out gene expression is dependent on the organ or tissue. So why was the study done on “complete seedlings” instead of leaves, roots and stems separately?
5-	Did the authors used any negative controls for de qRT-PCRs? It should be mentioned in the text.
6-	Did the authors check for DNA contamination in the RNA samples? It should be mentioned in the text.
7-	It is not clear which cDNA was used to confirm primers specificity (lines 135- 140). Please explain.
8-	It is not clear which cDNA samples were used to determine primers efficiencies (lines 144- 152). Please explain.
Validity of the findings: The sections of results and discussion raises several doubts that should be clarified, namely:

1- In lines 197-198 the authors say:” Instead, GAPDH2 showed the lowest expression level….”. This in not in accordance with Figure 1. Please check.

2-	It is not clear how the comprehensive stability analysis of RGs was made. Please clarify which methodology / tool used.

3- Please check other comments/suggestions in the annotated PDF file.
Additional comments: It should be emphasized the importance of the previous selection of RGs because only in this way we can guarantee the reliability and robustness of the of expression studies and RNA-seq data analysis.
However, in its current form, the manuscript shows several flaws. Still, the authors are encouraged to respond and to resolve the issues raised.


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: REFERENCE GENE SELECTION FOR QRT-PCR ASSAYS IN STELLERA CHAMAEJASME SUBJECTED TO ABIOTIC STRESSES AND HORMONE TREATMENTS BASED ON TRANSCRIPTOME DATASETS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript needs language editing.

L93-L95: when introducing GI, its role in salt stress resistance (see, e.g., www.ncbi.nlm.nih.gov/pubmed/19542296) should also be mentioned

Lines 302-309 describe in detail why 18S is not a suitable RG. I think this is obvious from Figures 4, 5 and 6 and does not have to be included in the discussion.

L312: tissue-specific - for which tissue?

Line 318: The reference for the SOS pathway is not correct. And I wonder whether the authors wanted to quote www.ncbi.nlm.nih.gov/pubmed/23322040 for the effects of ABA on GI expression instead of www.ncbi.nlm.nih.gov/pubmed/23656866.

Format of References:italicize species names, do not capitalize titles
Experimental design: The paper fits the Aims and Scope of PeerJ, and I see no problems with the experimental design and statistical analysis. However, I wonder why not more candidates for RGs were examined. Besides, why was mon1 selected as a housekeeping gene? It encodes a protein that, among other functions, regulates programmed cell death (https://www.ncbi.nlm.nih.gov/pubmed/27799422).
Validity of the findings: The choice of 10 potential RGs led to the identification of suitably stable RG combinations for the six experimental conditions under analysis. However, as shown in Figures 5 and 6, only one RG combination was suited for more than one condition (drought/cold). This raises the question whether the analysis of more potential RGs would have yielded a combination that worked for more conditions.
Additional comments: The text has to be corrected by a native speaker.


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: INTERACTION OF A DINOFLAGELLATE NEUROTOXIN WITH VOLTAGE-ACTIVATED ION CHANNELS IN A MARINE DIATOM
Review round: 1
Reviewer: 1

Output:
Basic reporting: The basic reporting of this paper was expertly done. The writing was clear and unambiguous. The raw data was shared in the supplemental materials section, literature cited was current and provided good context. The structure of the article was great, with professional looking figures.
Experimental design: On the whole, the manuscript does a good job describing the methods and presenting their research questions. That said, I have minor issues with some parts of the methodology.

1. Was the diatom culture axenic?

2. Line 143 - it is unclear what is meant by "exponential growth phase is determined by cell counts (10^5) with a..." does this mean that the authors counted 10^5 cells? That was the final concentration? This needs to be clarified.

3. On Line 175 - "The perfusion was then stopped and a bolus addition of ASW...." what volume were these bolus additions added in?
Validity of the findings: The findings on the whole were presented well and the conclusions reached were well thought out. Minor issues:

1. Just a comment that it would have been nice to show the impact of the PbTx3 toxin on long term growth of the diatom culture. While you don't see huge differences in terms of hyperexcitability, there are differences in the action potential. It would have been nice to see if that indeed translated into differences in growth rates of the cells.

2. Interesting finding that the action potential inhibition was accompanied by an apparent shift in the ion selectivity that favors Ca2+ influx. The influx of Ca2+ into a cell is a typical stress response that has been observed in phytoplankton previously (see refs in Bidle 2015). Without additional physiological information (staining for intracellular Ca2+ or just diatom growth) it is hard to know what the long-term impacts are, but Ca2+ signaling has been suggested to play a role in programmed cell death, so it could be that this is a significant response of the cell, but with no information for how the cell survives exposure it is hard to draw conclusions. Inclusion of some discussion of Ca2+ signaling in phytoplankton could be added to the discussion.

3. The final statement on Line 329 - 331, seems a bit heavy handed. In reality one toxin was tested in these experiments, while the authors state that it is the toxin most prevalent, certainly diatoms could react to the other forms of the PbTx toxin or other waterbourne chemical cues.
Additional comments: Nice paper, it is nice to see people trying to look for the mechanisms of action in response to toxin or secondary metabolite exposure.


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: INTERACTION OF A DINOFLAGELLATE NEUROTOXIN WITH VOLTAGE-ACTIVATED ION CHANNELS IN A MARINE DIATOM
Review round: 1
Reviewer: 2

Output:
Basic reporting: Well-written manuscript with clear, unambiguous and professional English.  Literature review is adequate, but see general comments with respect to breadth of discussion.

Note comments on raw data format in general comments.

Study is self-contained, but linkages between electrophysiology and bioinformatics could be strengthened.
Experimental design: Research question is well defined and falls within aims and scope of the journal.  Knowledge gap clearly identified in introduction.

There is a mismatch between the motivating hypothesis and the study details (see general comments).  Additional methodological details needed for replication of results.
Validity of the findings: The findings seem to be valid, but more experimental details are needed to properly assess bioinformatic findings (see general comments).
Additional comments: Overview

In the introduction, the authors motivate their study with the hypothesis that toxin production by species like Karenia brevis may function as allelopathic compounds that inhibit growth in potential competitors.  This is a compelling hypothesis.  While much work has been completed in elucidating the effects of neurotoxins on ion channel function, little progress has been made in establishing the competitive advantages that the toxins confer to the algal species producing them.

The experimental approaches in this study were two-fold:  1) electrophysiological measurements on the effect of brevetoxin on channel function; and 2) bioinformatic analysis comparing the amino-acid structure of brevetoxin binding sites of voltage-gated channels from diatoms, other phytoplankton species, bacteria and “animals”.  While I found the study very interesting, I did not think it answered the question set up in the introduction.  Specifically, in the experimental treatment, a single (and high; 1 µm) concentration of brevetoxin was applied to the cells.  A better experimental design would have been to use a range of concentrations, including concentrations that would have been closer to environmental levels (30 - 80 nm; line 327).  It seems that a simpler approach would have been to grow the cells in the presence/absence of brevetoxin to establish allelopathy.

Nevertheless, I found the study very interesting, in particular the combination of physiological measurements with a bioinformatic approach.  The effect of the toxin on the channel function is novel.  The similarity/dissimilarity of VGCs across different taxa has been an active area of research, including the relatively recent conclusion of independent evolution of the bacterial and the eukaryotic cation channels (e.g., McCusker et al. 2012).  Thus, the presence of bacterial channels in the diatoms is interesting, although the current manuscript does not indicate whether they are expressed (see comments on bioinformatics).

I had some concerns about the electrophysiological methods.  Given the unusual structure of the diatom, the presence of large vacuoles and the likelihood of recordings from multiple channels, the materials and methods need to include more details to allow a better assessment on what is being recorded, data filtering and analysis.

Discussion – much of the discussion is too speculative and needs to be revised.  Specifically, the comparisons with the physiology of vertebrate and invertebrate Na+/Ca++ channels needs to be much more specific – throughout the discussion there are overgeneralizations mentioning “animal” channels, which may be only applicable to certain species/channels and an oversimplification of the these channels, and thus not represent the diversity of VGCs in vertebrates and invertebrates.

The TTX story may provide an interesting framework for interpretation of the current results.  Using site-directed mutagenesis, it has been possible to gain insights into how conformational changes caused by single amino acid mutations affect the TTX binding site.  While brevetoxin may not have been studied as extensively, brevetoxin resistance has been characterized for some channels, and references to this literature are incomplete (e.g., Dechraoui MY, Wacksman JJ, Ramsdell JS., 2008).

Bioinformatic analysis

Provide more details on the searches performed including the specific databases in NCBI that were searched.  Depending on the database, it is quite possible that only partial sequences were available for some species.  Include a description of the criteria used (such as reciprocal blasts) to vet the sequences that were retrieved using the blast searches.  Search results should include length of the sequences retrieved, whether proteins are full length, top hits, e-values.

No information is given whether the searches were limited to genomic data with predicted protein sequences, or if they also included mRNA (transcribed) sequences or even mass spec analyses of the actual proteins (model species). Thus, the table should include information on the source of the predicted proteins, and the text provide an assessment of the databases searched and sequencing technology used, since the proteins are often predicted from incomplete information.  Furthermore, the NaV1 sequence is particularly difficult to assemble from short sequence reads or to obtain using a PCR-based approach, due to regions of low complexity and splice variants.  It is difficult to evaluate the quality of the bioinformatics results without additional information.

One issue is whether the absence of a NaV1 gene is due to incomplete sequence data or the true absence of the gene in the organism.  This can only be addressed in species with genomes that have been completely sequenced, assembled and supported by extensive transcriptomic data to confirm transcription.  The complete genomes of two diatoms have been published (Phaeodactylum tricornutum and Thalassiosira pseudonana) – these genomes could be searched to determine which genes would be expected in the databases.  Thus, Fig. 4A should include the VGCs found in P. tricornutum as well. Are there more than 1VGC gene present in these diatoms?  Table 1S would be more informative if it included information on e-values and top hits (bacterial vs. NaV1 vs. NaV2).  Given the general audience of PeerJ, provide information on the phylogenetic relatedness between the study organism and these two diatoms.

Raw data check

The data are included with the manuscript.  However, the electrophysiological recordings are in “.abf” format (Axon Instruments?), which I could not read.  Could these files be converted to “.cvs” format (or another format that is broadly accessible)?  This would make them more broadly available.

Table S1 caption – provide a more detailed description of the data (see comments on bioinformatics section).

Table S1 – For many sequences the authors list the publication associated with the sequence, which I think is important.  However, it may be useful to add the source of the sequences (which is only given in the absence of a publication). This would allow the reader to go directly to the appropriate website (e.g., NCBI) and retrieve the sequence.  However, while the NCBI sequences were easy to find, I could not locate the sequences on “imicrobe”.  Specifically, my searches indicated that the “imicrobe.us” website could not be found.

Figure S2 – needs to be checked for errors.  At least two species are identified as CCMP127. Furthermore, it would be helpful to make it easier to cross-reference between this figure and Table S1 and Fig. 4, consider using a numbering system that is common to table and figure.  This numbering system could be used to cross-reference with the sequences aligned in Figure 4B, C and D, which is not possible in the current format.

Specific comments
Line 221 – remove “in”

Line 291 – “animal models” – be more specific here, which animal models?  Throughout the discussion avoid generalizing to “animal” – the diversity of ion channels is very large, and there are many taxonomic differences in gene duplication and function.  Comparisons should specify the model species and the specific genes.  NaV channels are characterized by the DEKA motif (which lends them their specificity), which is not true for the diatom channel, raising the question whether it should be considered a true Na+ channel – it seems like it is a Ca++ channel, that is also permeable to Na+ ions.

Lines 297-300 – the authors indicate that the response observed in their diatom is unique, yet seems to be similar to the squid (which is a standard animal model).  This section is unclear: how is the diatom’s response similar/unique, and how does the squid compare with other “animal models”.

Paragraph starting with line 332 – is too speculative.  Needs to be rewritten after revision of the bioinformatics section.  It seems to be premature to speculate on the evolution of the channels given the diversity in amino acid sequences shown in Figure 4.  A lot is known about the evolution of VGC channels in invertebrates and vertebrates, and channel function – but this is not reflected in this paragraph.  Furthermore, the wealth of information available on vertebrates and invertebrates stands in contrast to the limited understanding of VGC function in bacteria and unicellular organisms like the diatoms.

Paragraph starting with line 354 – the conclusion of the lack of a 4 domain VGC is not supported by the current result section (see figure 4C and D with sequences shown for O. sinensis).  Note comments on bioinformatics.  This paragraph also seems to be contradictive – if the EEEE filter is Ca++ specific (bacterial channel), and the DEEE filter is a general cation channel, what is the basis for identifying the predicted diatom DDDD motif as being a selective Na+ channel?


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: INTERACTION OF A DINOFLAGELLATE NEUROTOXIN WITH VOLTAGE-ACTIVATED ION CHANNELS IN A MARINE DIATOM
Review round: 1
Reviewer: 3

Output:
Basic reporting: Kitchen et al studied the impact of the Karenia breve neurotoxin (Brevetoxin) on marine phytoplankton as they hypothesize that these neurotoxins may also affects the sodium and calcium VGCs in marine phytoplankton like in animals. This is an obvious hypothesis to test, but not much was found in the literature that brevetoxins acting as allelopathic subtances, see Cembella 2003 and others.
However, the MS is clear and well written and the experimental set-up follow a logical structure and is well conducted. The combination of electrophysiology to analyse the VGC performance and the molecular genetic analyses of the potential VGC structure and function in phytoplankton such as the diatom Odontella presents a new level of effect analyses.
I wonder if the MS would benefit when the authors would put the insensitivity of diatoms and other phytoplankton species towards PbTx-3 into the focus and uses the results presented here to discuss a potential evolutionary step by changing the 4-domain channel losing the PbTx binding side and may using a single domain channel.. As the literature, so far as I know, was suggesting rather insensitivity of phytoplankton towards PbTx I was not expecting effects, but the results presented here serving with a nice dataset explaining why they are not sensitive. Different structure of the 4 domain channel and additional the one domain type. Anyway, just my thoughts and if I got it right, I think it should be explained more schematic so it will be easier to follow.
Introduction and background: The first paragraph of the introduction presents a good motivation for the model but I am wondering if not more recent publications can be used. For instance the increased frequency and duration has valid references from ~2000 and I think that there are more recent ones, particular from the group of Van Dolah and others.
Line 70-77: There is a new van Dolah paper out (J. Phycol. 53, 1325–1339 (2017)) about some new findings according the biosynthetic pathways and related PKS genes.
L80: “…it takes only nM concentrations of these potent toxins”…..Please be aware that this might be not much for an animal accumulating toxins over time, but in the water column, it is a lot. I have no information that any phytotoxin was measured in such high concentration in water. For the allelopathy hypothesis the effect should be in pM range I guess. The part could be rewritten.
L82-86: These sentences are a bit misleading as they suggesting/indicating that brevetoxins (…”these algal secondary metabolites..”) show allelopathic effects. Maybe it would be better to restructure the whole paragraph and put this general idea as the starting point and ask if PbTx can have similar functions…..with the following part (L91-96) you may support the hypothesis.
L91-96: These sentences are the most important ones to support the hypothesis of the MS. I would appreciated to get here more details of the organisms and effects.

Results: L287/L334: The chromalveolates were not a natural group and therefore the RAS-group (Rhizaria, Alveolates, Stramelopiles) are a better descriptor.
Figures are okay.  I may got confused while reading the MS about the model to explain the insensitivity. I do not know how, but maybe the Figure 4 can be used to point out how the sequence differences in the four domain channel and the one domain channel support the conclusion.
Experimental design: So far I can comment on it, the methods are described with sufficient detail and informations. I cannot comment on the electrophysiology.
Validity of the findings: I appreciate the conclusion and the model which may help to explain why some phytoplankton species are insensitive to PbTx. As mention above, in my opinion that should be stronger highlighted.
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: GMPR: A ROBUST NORMALIZATION METHOD FOR ZERO-INFLATED COUNT DATA WITH APPLICATION TO MICROBIOME SEQUENCING DATA
Review round: 1
Reviewer: 1

Output:
Basic reporting: The paper by Chen et al. presents a novel method for normalizing micribiome read data for downstream analysis. The GMPR method seems like a good approach for normalization, and shows improved performance compared to current normalization methods. The paper is well written and provides good support for its claims.

Following are some comments which I feel can make the manuscript more clear and compelling, as well as explain better the reasons for the improved performance shown by GMPR:

1. While the GMPR method is presented with good details in the methods section, I am not convinced the reason for it performing better than the other methods it is compared to (RLE/TMM) is due to the higher sensitivity of these other methods to zeros in the data. As can be seen in figure 3, all methods (including GMPR) seem to degrade similarly as the fraction of 0 increases from 60% to 80%. I think it would benefit the paper to try and explain better the intuitive reason for the improved performance of GMPR.

2. Some observations are over/understated in the manuscript. specifically
- line 141-142 "the performance of TMM and RLE decreases significantly as the number of perturbed OTUs increases" - significantly is a bit too strong - it is a small change
- line 161-162 - "As shown in Figure 5A, although all approaches have slightly elevated FDRs relative to the nominal levels, the ".... slightly elevated is an understatement (a 5-fold underestimate in the FDR level for edgeR-GMPR and edgeR-TMM), please remove the "slightly"

3. Figure 4 and table 2 do not contribute a lot (since similar data is presented in figure 3 and figure 6 respectively). Maybe worth moving to supplementary file.

4. Some of the simulation details in the results section can be moved to the methods section instead (and then mentioned briefly in the results) in order to simplify the results section

5. The source code is available in the github address supplied. However, an additional file ("GMPR_0.1.3.tar.gz") is mentioned in the github readme file but is not there? where can it be obtained?

6. The paper is well written. Some small typos exist, such as:
methods section:
- c_ik and c_ki are interchanged sometimes (i.e. step1 and step2 use c_ik whereas definition and r_ij definition use c_ki
- Definition of S_i - can you describe with what S_i is used for (I assume it is the estimated number of reads in the sample, used for the normalization by division?)
- definition of r_ij has a multiplication over all j=1..n, which is not needed, as it is later performed in the S_i calculation
- formula for S_i calculation using r_ij - add ,i=1...n at end of formula (simiar to previous S_i calculation described to RLE).

results section:
line 125 - "trends to decrease" could be "decreases in most cases"
line 169 "sequencing of the stool samples" could be "sequencing of stool samples"
line 169 "These real datasets are retrieved from qiita database" could be "These experimental datasets were retrieved from the qiita database"
line 170 "with a sample size larger than 50" could be "with a sample size larger than 50 each
line 172 " from other body sites." change to " from other sample types"
line 215 "has achieved" change to "achieves"
line 232-233 "by showing its better performance" - change to "by showing it performs better"
line 243 " its use may not be limited to these applications." - change to " its use is not limited to these applications."

7. A few references can be added to the introduction when discussing compositionality effect (such as "Analysis of composition of microbiomes: a novel method for studying microbial composition" - Mandal et al. 2015, "Balance Trees Reveal Microbial Niche Differentiation" - Morton et al. 2017
Additionally, can you supply a reference to the statement in lines 50-51 "Many normalization methods have been developed for sequencing data generally, and for RNA-Seq data in particular..."

Box1 - maybe worth adding the reference for each method if possible.
Experimental design: The authors validate the performance of GMPS and compare to state of the art methods using both simulations and real datasets. A few issues which may help make the results and interpretation more robust:

8. For the real dataset used for the analysis shown in figure 6, were all scaling methods normalized somehow (i.e. sum/mean of all samples identical in all methods tested)? Otherwise, a normalization method that just divides all samples by a large number will obtain the lowest variance.
9. Can error bars be added to figures 3 and 4?
10. Can the performance of TSS be shown in figure 5? Or is there a technical reason preventing doing this?
11. For the real datasets mentioned in Table 1, were all samples from each study used? Some studies contain both fecal and non-fecal samples. Other studies contain fecal samples from multiple hosts (i.e. human and canine in study 3). Using all samples from each study may be problematic as the assumption of low variance may not hold for different hosts/sample types in the same study.
12. For the performance of the various methods shown in figure 6, can you also provide (maybe in the supplementary) an example of the distribution of the variance values for each method (such as a histogram of variance values) for some experiment from Table1? This can complement the comparison summary shown in figure 6 and enable seeing the difference between the methods.
Validity of the findings: 13. In lines 207-208 "Under this condition, certain bacteria will grow in the ambient temperature and we thus expect a low agreement between replicates after four-day ambient temperature storage." - if growth happens similarly in all replicates of a given sample, would expect high ICCs? If so, maybe low ICCs are due to non-identical growth in the replicates maybe due to sporadic events? Or maybe ICC is between day 0 and day 4 (in that case need better explanation as i did not understand it this way).
Also same phrasing in lines 214-215 "since reproducibility decreases as certain bacteria grow as time elapses" - again is it due to growth which does not happen in all replicates?

14. In the conclusions section line 248 discusses usage with unweighted distance metrics. Is it possible to rarify after GMPR? will it improve performance over just rarefaction?

15. line 47-49 state "An ideal normalization method should thus capture the invariant part of the count distribution and be robust to outliers and differential features. The latter property is important to reduce the false positives due to compositionality." : Since going from the real bacterial abundances to the reads/sample is not a 1-1 function, the assumption used for inferring the abundances from the reads/sample (i.e. many biological relevant datasets have a large invariant part) should be clearly stated.
Additional comments: A few additional comments:
lines 34-35 " or more severely, result in falsely discovered features." - This can only happen when the library size is a dependent - so maybe combine with next sentence "Normalization is especially critical when the library size is a confounding factor that correlates with the variable of interest"

16. line 41-44 "First, it is not robust to outlier counts. Outliers have frequently been observed in sequencing samples due to technical artifacts such as preferential amplification by PCR (Aird et al., 2011). Several outliers could bias the library size estimates significantly." - what are outlier counts? how do they bias the library size estimates?

17. Lines 44-47 - why is the compositional effect enhanced when there is a small number of features ("...and the total number of features is relatively small...") - do you mean number of differentially abundant features?

18. line 62 - "One popular strategy to circumvent the zero inflation problem" - can you explain what the zero inflation problem is (i.e. why is having a large number of zeros problematic)?


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: GMPR: A ROBUST NORMALIZATION METHOD FOR ZERO-INFLATED COUNT DATA WITH APPLICATION TO MICROBIOME SEQUENCING DATA
Review round: 1
Reviewer: 2

Output:
Basic reporting: The authors developed a new normalization method for microbiome amplicon data, which was extended from RLE. The usage of this method was demonstrated with both simulated and real data sets. It is good to see the statistic community is picking up the problem and start to solve the challenge in microbiome data set.
Experimental design: The current result looks good; however, there are several key issues that need to be addressed. Without these, I would be very skeptical about the general robustness and usefulness of GMPR method in microbiome:

1. In the simulation, the percentage of OTUs perturbed ranged from 0% - 32%. The authors should provide cases where over half of the OTUs are perturbed, because the authors tried to argue one of the advantage of GMPR, compared to other methods, is that it is robust even majority of the features are subject to change.

2. Besides stool microbiome data, the authors should demonstrate the usefulness of GMPR on skin and oral data, because skin and oral microbial community are much less diverse and thus has a bigger compositionality problem than stool data.

3. It is surprising that the authors didn't compare their method to rarefaction. As the most used normalization method, rarefaction has been shown to be applied for any type of analysis including quantitative or qualitative alpha/beta diversity, differential abundance, etc. The disadvantage of rarefaction is the loss of power due to the discard of reads when rarefying from high-read to low-read depths. The authors should include rarefaction for their benchmark results.

4. It looks like GMPR method could also be applied as a normalization method for quantitative beta diversity calculation (eg weighted UniFrac distance). The authors should show the benchmark results on this type of analysis as beta diversity is one of the most used techniques in microbiome data.
Validity of the findings: The data and analyses looks sound.
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: GMPR: A ROBUST NORMALIZATION METHOD FOR ZERO-INFLATED COUNT DATA WITH APPLICATION TO MICROBIOME SEQUENCING DATA
Review round: 2
Reviewer: 1

Output:
Basic reporting: The manuscript convincingly presents the novel GMPR method for count normalization. GMPR seems to improve sensitivity and specificity compared to current methods in a large range of simulations and real sample types, and will help obtain better results in microbiome analysis.
The authors have addressed previous comments in a satisfactory manner.

A few small points:
1. In figures 3 and 4 for large perturbation, do the authors have an insight as to why TSS performance is increasing with the increase in proportion of perturbed OTUs (whereas as all other methods decrease)? If so, it would be useful to mention/explain in the corresponding results section.

2. When discussing figure 5, maybe worth explaining shortly why the observed FDR is higher than the nominal FDR even with the "balanced" scenario (If it is truly balanced, one would expect no compositional effect and hence full FDR control).

3. In general, can the authors comment on the optimal OTU filtering method to use prior to using GMPR? I would expect there is a balance between obtaining the ratios from low frequency OTUs (where discretization would play a large role - i.e. 2 reads in one sample and 1 read in another sample for the same OTU would be very noisy in estimating the fold change of the OTU between the two samples compared to 200 reads vs. 100 reads), whereas on the other hand keeping more OTUs would result in a larger number of ratios (and hence maybe a better estimation of the median). In the COMBO dataset, the authors filtered OTUs with <10 reads. Would this be the recommended filtering method? Or is the method not sensitive to the exact filtering?

4. Maybe worth adding in the introduction (where the COMBO dataset is first mentioned) a brief description of what the COMBO dataset is (i.e. human fecal etc.) for clarity to the reader without needing to read the reference?

4. typos:
line 153: missing space "zero inflated"
line 230: level should be levels
Experimental design: No additional comments
Validity of the findings: No additional comments
Additional comments: No additional comments


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

Input:
Title: GMPR: A ROBUST NORMALIZATION METHOD FOR ZERO-INFLATED COUNT DATA WITH APPLICATION TO MICROBIOME SEQUENCING DATA
Review round: 2
Reviewer: 2

Output:
Basic reporting: The authors improved the manuscript substantially  and addressed all the comments. One figure I request the authors to add: besides showing the nonparametric ranks for inter-sample variability (fig 6&7), the actual value of the variances should be shown as well to see how much better or how different in terms of inter-sample variability among those normalization methods.
Experimental design: good
Validity of the findings: good
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: GMPR: A ROBUST NORMALIZATION METHOD FOR ZERO-INFLATED COUNT DATA WITH APPLICATION TO MICROBIOME SEQUENCING DATA
Review round: 3
Reviewer: 1

Output:
Basic reporting: The authors have answered all points in a satisfactory manner.
I believe this paper will help future microbiome analysis, and GMPR seems an excellent method as a first step normalization prior to downstream analysis.
Experimental design: NA
Validity of the findings: NA
Additional comments: NA


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

Input:
Title: EFFECTS OF MENTAL HEALTH INTERVENTIONS FOR STUDENTS IN HIGHER EDUCATION ARE SUSTAINABLE OVER TIME: A SYSTEMATIC REVIEW AND META-ANALYSIS OF RANDOMIZED CONTROLLED TRIALS
Review round: 1
Reviewer: 1

Output:
Basic reporting: In general the language is clear and professional throughout. However, I have some comments and suggestions for improvements:
- In the abstract, change the heading Conclusion to Discussion.
- Line 58: To state that a thing is common or has high prevalence without specifying how common or high is annoying.
- Line 66: Is it really higher risk groups and not groups with higher risk?
- Merge sentences lines 92-93
- Check heading of Table 2 and Figure 3.
- The layout of Tables could be improved by not using marked lines for every row and column. Also the authors could consider using background coloring of e.g. every other row.

Introduction
While the introduction gives the context to mental ill health – literature being well referenced and relevant – no corresponding context is given to positive mental health. There is no theoretical conceptualization of positive mental health, which would give the rationale for including (or not) certain outcomes as measures of positive mental health. Just because there are records of studies in the literature and methods to make effects of intervention sustainability across studies “statistically comparable” using standardized units, it doesn´t necessarily make them meaningful to include in a meta-analysis. Thus, if the authors want to keep positive mental health they should provide the relevant context and conceptualization that justify the outcomes included in the analyses and why they think they are meaningful to pool. If they do this my guess is that it will become evident that the scope of the study is better limited to mental ill health and related endpoints meaningful in a meta-analysis.
Experimental design: The research is original and within the aims and scope of the journal. However, the research question (s) could be better defined. It is unclear what is meant by mental health and mental ill health, for example. Also I do not like the part of the aim that addresses the implementation quality. While implementation quality is (!) important and should be brought to attention I do not think this is the way to do it. The reason is that RCT:s usually do not report implementation components which could lead to a bias in an assessment of such quality. Further, it could be stated more clearly how the present systematic review and meta-analysis differs from the previous ones (line 87). The authors refer to three previous reviews (Conley et al 2015, 2016, 2017) and it would have been easy to describe each of them more in detail. The present description makes it difficult to know what specifically their review adds. Since the referred reviews of Conley et al are recently published this becomes really important because it is the part where the novelty of the study should be stated clearly.

The methods are described with sufficient detail and information to replicate. An exception though, is found on line 106. Since there are multiple guidelines the authors should specify which were used.
Validity of the findings: The study deals with an important topic and it is evident that the authors have done an ambitions job trying to evaluate intervention sustainability of over time. That being said there are several limitations with the study, some of which are addressed by the authors in the discussion and some that I would like to stress further or add even. I have a major concern about collapsing so many types of outcomes into a single concept particularly for positive mental health. The studies included in the review or meta-analysis should be as homogeneous as possible. Now they introduce a potential bias that can be large. The high-to-moderate heterogeneity is a consequence of the broad outcome categories and an important limitation of the study. Collapsing outcomes also lead to other problems, like having to decide on a hierarchical order for positive outcomes - that in my mind do not make sense. Is academic performance a better indicator of positive mental health than well-being, for example? Effect sizes have to be excluded when studies report in more than one domain, which is negative because they fulfill the inclusion criteria but the effect size for another outcome is used.

In the fourth limitation of the study it is mentioned that 30% of the original studies were assessed as being of weak quality with selection bias as the most commonly identified weakness and what may have come out of this limitation. It would have been interesting to have the study quality distributed among the two major outcome categories, ill-health and positive. This would have helped the reader to evaluate the effects. A description of what type of quality impairments that was most common for each outcome concept and would also provide a larger picture. Lastly, I am skeptical about including the studies of weak quality in the meta-analysis.
Additional comments: No additional comments


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

Input:
Title: EFFECTS OF MENTAL HEALTH INTERVENTIONS FOR STUDENTS IN HIGHER EDUCATION ARE SUSTAINABLE OVER TIME: A SYSTEMATIC REVIEW AND META-ANALYSIS OF RANDOMIZED CONTROLLED TRIALS
Review round: 1
Reviewer: 2

Output:
Basic reporting: (1) The paper is well written and easy to follow. The language throughout the paper is mostly clear and unambiguous. There are a few small suggestions for clarification, which I have included in the sections below as they seem more appropriate for clarifying issues around design and validity of findings rather than issues with grammar or writing style.

(2) The authors have provided a substantial and entirely relevant background for issues of student mental health, which leads well to the need for a study such as this.

(3) Except for a few small issues with formatting of the paper (e.g., full-stops in headings, table & figure headers, table formatting), the paper is formatted consistently. These formatting issues should be addressed, but they are minor.

(4) Raw data has been shared.
Experimental design: (1) This research is certainly original in its aims, well designed, and within scope of PeerJ.

(2) The research aims are provided and they give good structure to the paper overall. However, some (simple, but important) attention is needed to clarify these research aims.
- In the abstract, it is not clear whether the second last sentence (lines 27-29) is referring to the first aim, or describing a second aim, or prefacing the aim in the last sentence. Some small adjustments to the sentence will clarify this confusion, eg: if it is prefacing the aim in the last sentence, then the full-stop in line 27 could be replaced by a comma.
- A new (third?) aim is presented in lines 101-102, but is not mentioned in your abstract. The section in the results that addresses this aim is lacking detail: almost as though it is a secondary and less important element of the paper. I suggest either including this aim in the abstract (and providing more detail in the relevant results section) or removing this aim from the paper.
- Line 97: I recommend providing an example of what you mean by "too little information is often provided on the process of program delivery" - eg, what sort of information is generally missing? how would including that information benefit the evaluation or outcome? Clarifying this will help strengthen the argument for your method and identifying the gap in the literature that you are addressing.

(4) The research approach does very well to navigate the often-unclearly-defined areas of student mental health and mental ill-health. This is particularly noted in the comprehensive and in-depth method section, which I found easy to follow and in sufficient detail to allow for replication.
Two small points of clarification would further strengthen the description of the study's methodology:
- Line 42: It is not clear what you mean by "individual outcomes" in this sentence, as "individual outcomes" suggests outcomes for individual people, but the rest of the sentence describes outcomes for specific symptoms across the dataset. Perhaps a more accurate phrase than "individual outcomes is "specific symptoms of mental illness"?
- Also on line 42-43, the phrase "most considerable sustainability of symptoms reduction was evident" is awkwardly phrased. Consider adding "the" to the beginning of the phrase (ie "the most considerable..") and replacing "symptoms reduction was" with either "symptom-reduction was" or "symptom-reductions were".
One point of clarification would strengthen the results section:
- Lines 354-355 presents a substantial problem with the structure of the results and setup of (one part of) the papers' methodology (this problem can be easily resolved): if there is a "lack of data on individual positive mental health and academic performance outcomes", then why is this section heading "interventions promoting mental health and academic performance"? I recommend changing the heading to better represent the analysis taking place, and either: justify why you have up to this point focused your argument on positive mental health and academic performance without then analysing those outcomes, or, change the focus of your setup in the introduction to better account for an analytical focus on experiences such as active coping, self-esteem, and self-efficacy.
Validity of the findings: (1) The effect sizes reported in this paper are small (except for the effect size for active coping). This is fine, but rather than claiming the effect sizes are "substantial", I recommend that the authors acknowledge throughout their paper that the effect sizes are "small but significant" or "small but meaningful", as appropriate.  This will prevent any misinterpretation of the actual patterns reported in the paper by novice / uninitiated readers.

(2) The data were shared with PeerJ. Data were handled in appropriate and reasonable ways. Findings are statistically sound, with the exception of my first point in this section.

(3) The concluding paragraph reflects the general findings in a realistic and thoughtful manner. The sentence addressing policy-makers and student health providers (lines 467-368) is not particularly helpful, and might be better focused on the different contexts and group differences (eg, medical students, group differences for intervention types, etc).
- The conclusion in the abstract is not as helpful as the overall conclusion. For example, Lines 52-54: "Interventions targeting university students … should be considered by student health policy-makers and providers": Considering that you have not investigated the attention paid to interventions by policy makers (and considering that  many student health policymakers and providers are already invested in or searching for effective interventions), this concluding statement is not particularly helpful or meaningful for readers. It also does not do justice to the importance of your findings (that interventions have a small but real sustained effect!!) or relate back to your aims (investigating how sustainability varies for different types of interventions, in different contexts, with different cohorts, etc). I recommend considering a stronger conclusion in this abstract that speaks to the potential benefits of specific intervention types, and how these might vary in different contexts.
Additional comments: Well done on conducting such an innovative and important study! I was thoroughly interested and engaged in your paper, and I look forward to seeing it in print. I hope that you find my comments and suggestions useful for refining an already high-quality paper. My suggestions are all minor and (should you agree with them) they will not take much work to address.


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: PLASMIDSEEKER: IDENTIFICATION OF KNOWN PLASMIDS FROM BACTERIAL WHOLE GENOME SEQUENCING READS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The authors present a novel tool, PlasmidSeeker, which examines the co-occurence of k-mers between a query sequence, bacterial host and a plasmid database. This is done directly from raw reads, thus giving higher sensitivity but also saves the user for the major computational task of doing assembly.
Experimental design: As described by the authors, a method based solely on k-mers requires a database that is highly similar to the reference sequences. Here the sensitivity and specificity is tested with artificial sequence, mutated with SNP’s in different amounts. Plasmids are however also known to be extremely plastic, meaning that they quite quickly exchange their genomic information by switching out entire gene islands, as described by M. Couturier et al. (Couturier et al. 1988). Which is part of the reason why PlasmidFinder is based on replicons, as these are the constant parts of the plasmid (Carattoli et al. 2014). Another benchmark is thus needed, where entire islands of genes are changed.

Besides the mapping of k-mers to a reference database, the authors also examine the copy-number difference between chromosomal k-mers and plasmid k-mers, where these are assumed to be different. The copy number of plasmids may be influenced by the library preparation used, and might therefore have impact on the detection and be worth mentioning (Turner n.d.).
Overall, PlasmidSeeker seems to have great potential, and might help in outbreak investigations to gain a deeper insight on plasmid spread.

Carattoli, Alessandra et al. 2014. “In Silico Detection and Typing of Plasmids Using PlasmidFinder and Plasmid Multilocus Sequence Typing.” Antimicrobial Agents and Chemotherapy 58(7):3895–3903. Retrieved February 8, 2018 (http://www.ncbi.nlm.nih.gov/pubmed/24777092).
Couturier, M., F. Bex, P. L. Bergquist, and W. K. Maas. 1988. “Identification and Classification of Bacterial Plasmids.” Microbiological Reviews 52(3):375–95. Retrieved February 8, 2018 (http://www.ncbi.nlm.nih.gov/pubmed/3054468).
Turner, Paul E. n.d. “Phenotypic Plasticity in Bacterial Plasmids.” Retrieved February 8, 2018 (https://www.ncbi.nlm.nih.gov/pmc/articles/PMC1470877/pdf/15166133.pdf).
Validity of the findings: No comment
Additional comments: No additional comments


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

Input:
Title: PLASMIDSEEKER: IDENTIFICATION OF KNOWN PLASMIDS FROM BACTERIAL WHOLE GENOME SEQUENCING READS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The text is clearly written and provides sufficient background information and references.

A Makefile (or similar process file) could be referenced such that the reader could easily recreate the analysis in the paper,
Experimental design: The design seems reasonable, and the necessary parameter validation steps appear to have been performed.

The purpose of the tool is well defined and targets an important research question i.e. robustly identifying plasmid sequences in WGS data.

I would ask why 80bp was used for read simulation? A more realistic length would match that of MiSeq data i.e. 250-300bp. Does read length have any effect on k-mer frequencies and therefore the accuracy of results?
Validity of the findings: The results are well presented and the discussion and conclusions seem fair.
Additional comments: Line 86: claims that a reference genome from the same genus would be sufficient. This might be quite genus specific, there can be quite a high level of genome diversity in some genera. I don't think any evidence has been presented to support this?

Line 133: can the "in house script" be made available? Maybe through github or in supplementary. It would help the reader reproduce the analyses

A general comment, always write the species name in full the first time, and then subsequently abbreviate. E.g. Escherichia coli written in full at line 114, 189 and 211. Also check other species names.