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

Input:
Title: A BRIEF INTRODUCTION TO MIXED EFFECTS MODELLING AND MULTI-MODEL INFERENCE IN ECOLOGY
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comments
Experimental design: no comments
Validity of the findings: no comments
Additional comments: I have reviewed an earlier version of this MS. The authors have addressed my comments and it seems they did so for others' comments. I have noticed that one of the other referees raised a point about missing data, which I did not comment on. Actually, missing data on mixed models are still underdeveloped and an emerging research topic. There are a couple of papers that directly discuss missing data in mixed model contexts, but which are not currently cited in the MS but relevant.

Nakagawa, S. (2015) Missing data: mechanisms, methods and messages In: Ecological Statistics: contemporary theory and application (eds. Fox, G. A., Negrete-Yankelevich, S. & Sosa, V. J.). Oxford University Press, Oxford. pp. 81-105

Noble, D. W. A. & Nakagawa, S. (submitted) Planned missing data design: stronger inferences increased research efficiency and improved animal welfare in ecology and evolution. bioRxiv

https://www.biorxiv.org/content/early/2018/01/11/247064

The latter one includes an interesting example of how planned missing data design can be used in a repeated measurement design (which is modelled by mixed models). I thought the authors may be interested. No need to cite these but the authors would like to note that missing data on mixed models are topics under development.


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

Input:
Title: A BRIEF INTRODUCTION TO MIXED EFFECTS MODELLING AND MULTI-MODEL INFERENCE IN ECOLOGY
Review round: 2
Reviewer: 2

Output:
Basic reporting: Language and presentation are appropriate
Experimental design: Not applicable
Validity of the findings: Not applicable
Additional comments: In this paper, which I reviewed previously, Harrison et al. provide an overview of considerations associated with (generalised) linear (mixed) modelling in ecological datasets. Overall the paper has much improved from the previous version, and will likely make a valuable contribution to the literature. I feel that a few of my previous comments still apply to the new version, so I hope the details below clarify my concerns for the authors:

1.	Regarding the simulation analysis, I accept the authors’ response about choosing not to run more models. However, I am still concerned about the mixing of NHST and IT philosophies in the interpretation. Specifically, there is heavy reliance on interpreting results as “Type I error” – strictly speaking one cannot (or perhaps, should not) falsely reject a true null hypothesis with an information theory approach, because one is not doing null hypothesis significance testing. Of course, I agree with the authors that it is important to consider how often one might draw a false conclusion about whether a given variable is an important predictor of a response. However, it is important not to assess models built under IT using NHST. A better approach would be for the authors to use the inference strategies they advocate elsewhere in the paper, such as testing model assumptions, reporting R2, and basing interpretation on the presence and size of effects in the final model (see also my comment below on RI) – would these metrics collectively lead a researcher to erroneously conclude that they had settled on an appropriately parameterised final model that suggests strong effects? Similarly, the sentence at L944-945 presents a very frequentist viewpoint on model selection, which is inappropriate in a discussion of information theoretic approaches to model selection.

2.	Regarding the use of delta-6 or 95% summed weights, I felt that the authors response to my previous comment missed my point somewhat, which is that delta values and summed weights represent two (albeit slightly) different approaches.  If one wants to “guarantee” 95% weight, then they should use 95% summed weight.  For example, in the paper cited by the authors, model “M4” required delta-6.5 to encompass the best EKLD model 95% of the time (Richards, 2008, p223). While “at least delta-6” may be a good general guideline, this is not the same as “guaranteeing 95% weight”. See also Burnham and Anderson, 2002, p78, for explanation of how delta values represent relative evidence.

3.	New material has been added on the specification of random factors: I believe the lme4 specification “Clutch Mass ~ Foraging Rate + (1|Woodland) + (1|Female ID)” should achieve the same goal as the model on L402 (should this be M5?), if all female IDs are unique. Ambiguity can arise if the females are labelled (say) 1 – 10 in woodland 1, and 1 – 10 in woodland 2: are there 10 females, each breeding at two sites, or 20 females? Labelling females as 1 – 20 (if the latter) alleviates the ambiguity between crossed and nested random factors, and it would be worthwhile explaining this. See for example lme4.r-forge.r-project.org/book/Ch2.pdf

4.	Considering the revised section 5 (p34), I think the authors are overly dismissive of “relative importance” statistics. Unfortunately, the vernacular definition of “importance” differs somewhat from the technical definition; “relative importance” (sum of weights) informs which parameters are likely to occur in the best model, not their effect sizes. Indeed, IT-based model selection determines two things: the probability that variables should be present in the model (taking model selection uncertainty into account) and, if variables are included, what their effect sizes are. RI can assist inference around the former. I accept that there is discussion about the effectiveness and interpretation of RI in the literature (e.g. Giam and Olden, 2016; Galipaud et al., 2017), but I am concerned that the tone of section 5 might suggest to readers that they should ignore RI altogether. My view is that inference in an information theoretic framework should take into account (or at least, report!) all measures of quantitative evidence about the models, including RI and parameter estimates. For example, a predictor with RI of 1 and a small effect size may or may not be biologically “important”, while a low RI would likely indicate poor support, even if an associated effect is large. These statistics are additional tools for inference.

5.	A note on the suggested model specifications (p5, p6, p8): it is great these are provided, as knowing how to specify a model in R can be very useful to new users. These models are set within a discussion that considers the differences among models, so it would be helpful to see how the model outputs change depending on the model specifications. This could be easily obtained using a “built in” dataset in R, and presented as supplementary material with a brief commentary on how to interpret each output. For example, the output from M1 and M2 could be narrated in terms of the interpretation of output values associated with “group”. The same approach could be applied to M3 and M4. As an aside, a more complete discussion of for the use of random slopes would be provided if the authors explain the circumstances under which one would prefer model M4 over a model specified as “glmer(successful.breed ~ 1 + (body.mass|sample.site)”, which is sufficiently similar to model M2 that I think it is worth noting (see also e.g. Gelman and Hill, 2007, p259).

6.	A note on whether removing models from the set makes interpretation of the Akaike weights “difficult” (L1011): as pointed out by Burnham and Anderson (2002, p75), adding and removing models from a set requires weights be recalculated.  From a practical perspective, it is straightforward to calculate the weights of any model set by manually making the list of models for further analysis with MuMIn, or by using ‘get.models’ (MuMIn) on an existing ‘dredge’ object – see the MuMIn documentation for more info. In fact, wi values can even be manually recalculated relatively easily too (using the formula in Burnham and Anderson, 2002, p75). Explicitly specifying the model set is what the authors are indirectly recommending when they suggest that one should consider whether the “all-subsets selection” approach is appropriate, and so mentioning these methods for re-calculating weights would overcome the “difficulty” and provide readers the flexibility of choosing their own model set.

Minor comments

L105 “best practice”, in light of the title change, best to change this phrase here too?
L369 “checking the assumptions of the LMM or GLMM is an essential step” – given the high level of detail and instruction provided elsewhere in the paper, I felt like this statement needs a sentence or two also providing suggestions for some of the methods/packages that could be used.
L641 note that it is also possible for data to be under-dispersed (less variance than expected by chance, i.e. more uniform than chance).
L719 isn’t a Gaussian GLMM a LMM?
L769 a dataset cannot be “made up of missing data” – suggest rephrasing
L839-840 “there is no ‘null’” – I see the authors’ point, although one occasionally sees the intercept-only model referred to as the ‘null model’ – suggest rephrasing.
L1062 “data dredging” and “fishing” are no longer major components of the paper, and could therefore be removed from the Conclusions?
The paper contains a lot of abbreviations – some of which are widely used, and others less so. I suggest the authors consider providing a glossary of abbreviations. Furthermore, many abbreviations that are used only once or twice are probably unnecessary, and the paper would be more readable if the terms were spelt out e.g., “GLS” (L633), “IT-AIC” (L775) “ASS” (L897 and 898).

Literature cited in this review

Burnham, K.P., Anderson, D.R. (2002) Model selection and multimodel inference: a practical information-theoretic approach. Berlin, Springer.
Galipaud, M., Gillingham, M.A.F., Dechaume-Moncharmont, F.-X. (2017) A farewell to the sum of Akaike weights: The benefits of alternative metrics for variable importance estimations in model selection.  Methods in Ecology and Evolution, 8, 1668-1678.
Gelman, A., Hill, J. (2007) Data analysis using regression and multileval/hierarchical models. Cambridge, Cambridge University Press.
Giam, X., Olden, J.D. (2016) Quantifying variable importance in a multimodel inference framework.  Methods in Ecology and Evolution, 7, 388-397.
Richards, S.A. (2008) Dealing with overdispersed count data in applied ecology.  Journal of Applied Ecology, 45, 218-227.


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

Input:
Title: A BRIEF INTRODUCTION TO MIXED EFFECTS MODELLING AND MULTI-MODEL INFERENCE IN ECOLOGY
Review round: 2
Reviewer: 3

Output:
Basic reporting: all okay to good.
Experimental design: doesn't really apply with the exception of the simulation which is okay, but doesn't really much and conflates mode selection with testing (see my comments to the authors)
Validity of the findings: doesn't apply
Additional comments: General comments

This manuscript greatly improved as compared to the last version, and I appreciate the authors' efforts to deal with my comments and recommendations. However, I still see need for improvement and refinement. More specifically I see four major points (in my view issue two and four are the most crucial ones):

* First, I still feel that the manuscript's two major topics, GLMM and MMI, are not really connected, neither regarding statistical theory nor in the manuscript itself, and that the manuscript would benefit from being split into two. Moreover, I even see dangers in presenting both approaches in the same manuscript. In fact, as the authors themselves (correctly) state, the number of estimated parameters (degrees of freedom) in GLMM are generally unknown (L 883-884). This, in turn poses the question of how to even determine an information criterion such as AIC or BIC which penalizes for model complexity. The authors do not elaborate on this question, beyond briefly mentioning the issue. In their cover letter the authors state that they want to present the entire 'analysis pipeline'; but to me it seems that this particular pipeline (i.e., GLMM in combination with MMI) does not rest on a solid theoretical basis (and the fact that the two methods are frequently combined in applied statistics in ecology and behaviour doesn't alleviate the problem). So maybe better not presenting as being logically following one another, perpetuating common practice but not promoting best practice.

* Second, I still see need for refinement regarding the sections about random slopes (particularly L 379-402). Although the authors have considerably improved the manuscript regarding this point, the current manuscript still cuts the issue too short. The key point is that the authors seem to mix random slopes and correlations among random intercepts and slopes. In fact, the maximal model proposed by Barr et al. (2013. J Memory Lang, 68, 255–278) represents a model comprising random intercepts, all possible random slopes and also all correlations among them. The authors of the current manuscript are correct in stating that (nearly) perfect correlations are indicative of a model being too complex for the data at hand. However, the situation is not an all-or-nothing. In fact, when the correlations cannot be reasonably estimated, it might still be possible to fit a model including random intercepts and all random slopes but not the correlations among them (see Bates et al. 2015. Journal of Statistical Software, 67, 1-48). This is also the approach somewhat proposed by Barr et al. (2013) and Bates et al. (Parsimonious Mixed Models. http://arxiv.org/abs/1506.04967v1): begin with the most complex model but simplify it, beginning with the exclusion of correlations among random intercepts and slopes when it appears too complex.
There is one additional point I feel the authors must make: it should not be a matter of taste whether random slopes are considered. Instead, based on the available literature Schielzeth & Forstmeier (2009. Behav Ecol, 20, 416-420), Barr et al. (2013), and Aarts et al. (2015. BMC Neurosci, 16, 94) it simply seems needed to account for random slopes to achieve the nominal type I error rate (and correspondingly unbiased standard errors and confidence intervals); and when all or several random slopes are neglected because the model would get too complex to fit it, then one has to face a perhaps highly elevated type I error risk.
Also at other occasions (e.g., L 172-187), the authors still leave the impression that decisions regarding whether to include random slopes are a matter of 'taste' or the aims of the study, but in my view Schielzeth & Forstmeier (2009), Barr et al. (2013), and Aarts et al. (2015) made convincing cases that these have to be included to prevent type I errors.

* Third, I feel concern about the section headed 'Stepwise Selection, Likelihood Ratio Tests and P values' (716-750). In my few this conflates a couple of issues in an inappropriate and confusing way. First, NHST is one of the three major statistical 'philosophies' (together with Bayesian and information theory based inference) used to draw inference about a model and/or individual predictors. Stepwise procedures, in turn, are a specialized technique which had been (and unfortunately still is) used as a means of model simplification; stepwise can be based on NHST, but also on an information criterion like AIC or other criteria (e.g., an F value). As such NHST has nothing to do with stepwise procedures, and the far, far majority of uses of NHST have nothing to do with stepwise selection. As the authors correctly state, both have come under heavy criticism, but for very different reasons. NHST is criticised since decades for the many weaknesses and pitfalls the approach has; stepwise has been criticised for a couple of particular weaknesses (e.g., Whittingham et al. 2006. Journal of Animal Ecology 75, 1182–1189) among which is an extremely inflated type I error probability (Mundry & Nunn. 2009. Am. Nat., 173, 120-123).
Here are a couple of clarifications which seem needed:
- NHST, when not coupled with stepwise and used appropriately in the sense of Forstmeier & Schielzeth (2011. Behav. Ecol. Sociobiol., 65, 47–55) does not lead to overestimated effect sizes or an inflated type I error rate.
- the null model sensu Forstmeier & Schielzeth (2011) is not one that differs from the full model by a single predictor, but by a set of predictors and the comparison between the two reveals a global test of their combined effect (appropriately accounting for multiple testing which otherwise would be an issue in case one would base inference on the significance of the individual terms in the model without conducting a full-null model comparison).
- Mundry (2011) did not argue in favour or model simplification.
- Murthaugh (2009) found that stepwise and all subsets approaches revealed largely comparable results (wrt their predictive performance and number variables selected) and regardless of whether stepwise was based on an F-test or information criteria. As such the article does not really compare NHST with other philosophies but compares model selection techniques.

* My last major concern is about the fact that the authors lack clarity and rigour regarding the issue of mixing model selection with significance testing. In fact, Burnham & Anderson (2002) have repeatedly pointed out that mixing the two philosophies is a no-go (and Mundry 2011 showed that it leads to drastically inflated type I error rates). For instance, when applied appropriately, there is no such thing as a type I error when using model selection based on an information criterion (such as AIC) because in the context of such an analysis one simply must not use any tests (see Burnham & Anderson (2002), e.g., P 202-203). In the view of the authors of the current manuscript, however, such an option seems to exist (see, e.g., L 805-807; 850-852; 855-859; caption of Fig. 4). Its worth emphasizing here that the term 'test', as I used it here, also encompasses checks of whether confidence intervals comprise the zero (and that bias in P-values gets along with parallel biases in standard errors (being too small) and effect sizes (being too large)).

Apart from that, I am still not very convinced by the simulation (L 813-836), since it conflates a couple of issues, namely (i) combining model selection with significance testing (see also my previous comment), (ii) conducting pair-wise comparisons without a global test of the effect of a factor, and (iii) neglecting the full-null model model comparison). Each of these have been addressed more thoroughly and clearly in other papers (i: Burnham & Anderson 2002; Mundry 2011; ii: all stats books covering ANOVA; iii: Forstmeier & Schielzeth 2011), and I feel this section does not contribute much to the existing literature nor to the clarity of the manuscript. On the other hand, the authors should make clearer statements about not combining model selection and significance testing (in a wider sense, i.e., encompassing also inspection of whether confidence intervals encompass zero; see also my previous comment).

Specific comments

L 33: Pretty abrupt transition from one topic to another.

L 67-68: inference 'about'.

L 69-72: I felt these examples are confusing: if the fixed effect varies or is manipulated at the clutch level, how can pseudo-replication happen on the chick level (it happens on the clutch level if each comprises several chicks, each measured once). And 'if fixed effects vary at the level of the chick': between or within chick? In case of the former the authors are correct that non-independence occurs among clutches or mothers'; but in case of the latter it also happens on the chick level.

L 145: 'hierarchically' implies that certain effects get priority when being estimated; but to my knowledge all effects are modelled/estimated simultaneously.

L 165-167: in my view random slopes need to be included to keep type I error rate at the nominal level of 0.05 and obtain unbiased standard errors and confidence intervals.

L 179-182: it seems worth mentioning that this model comprises the random intercept, the random slope and also the correlation between the two.

L 183: Schielzeth & Forstmeier (2009) *show* that...

L 274-279: I don't get the point here. Certainly, the random effects structure needs to be set up appropriately; but as Barr et al. (2013. J Memory Lang, 68, 255–278) showed, P-values for individual effects should best be based on likelihood ratio tests comparing the full with respective reduced models. This, in turn, doesn't rely on determination of residual degrees of freedom.

L 285-287: *general* linear models make the assumptions of normality and homogeneity of residuals (in my view, 'linear models' is a generic term encompassing also Generalized Linear Models such a Poisson or logistic models).

L 287: lower case 'normality'.

L 308-318: my intuition tells me that those not being already familiar with the link function wouldn't get this section.

L 372-376: but this applies in general (not only to GLMM).

L 374: 'Crossed factors *allow to* accurately estimate...'.

L 566: Zuur et al *give*.

L 586: 'estimates *of* …'.

L 658-659: to my knowledge, Wald-/t-tests are not applicable for random effects (and maybe not even F-tests).

L 694: 'often' or 'always'.

L 779: 'reference*s*'.

L 788: '...details on *how* AIC...'.

L 792-795: comparing the full with a null model is not an alternative to NHST, but simply NHST applied appropriately (avoiding type I errors due to multiple testing)..

L 805-807: but this applies only when one selects the best model and then tests it, something which should never be done as repeatedly and strongly stated by Burnham and Anderson (2002).

L 817: 'ASS' not formally introduced.

L 818: I guess you the authors mean 'different' rather than 'separate'.

L 817-819: I don't see any difference: what the function dredge of the package MuMIn does is exactly dredging in the sense of fitting all possible subsets of models...

L 849-852: as Burnham and Anderson (2002) have pointed out repeatedly one should not use the term 'significant' in the context of an AIC-based analysis (e.g., P 84, 203), and I feel the authors should adhere to this rule.

L 855-860: another example of the authors mixing model selection and significance testing. According to Burnham and Anderson (2002) such exercise must not be done (see previous comment), and Mundry (2011) clearly showed how such practice leads to drastically inflated type I error rate.

L 859: which 'conditions'?

L 930: 'included' in what? The AIC-best model?

L 936: I'd use 'similar' rather than 'equal'.

Figure 1, caption: reference to (B) is missing. The fact that the overall intercept is 0 is irrelevant here.

Figure 2, caption: I'm not sure if I would speak of a biased estimate when its average seems pretty much perfectly matching the simulated value (I'd speak of 'bias' then the average deviates from the simulated value).


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

Input:
Title: A BRIEF INTRODUCTION TO MIXED EFFECTS MODELLING AND MULTI-MODEL INFERENCE IN ECOLOGY
Review round: 3
Reviewer: 1

Output:
Basic reporting: None
Experimental design: None
Validity of the findings: None
Additional comments: I have read the MS again and the point-by-point replies of all the comments. I support the authors in terms of this paper being published as one. This will be an extremely useful paper for ecologists like myself and my students.


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

Input:
Title: A BRIEF INTRODUCTION TO MIXED EFFECTS MODELLING AND MULTI-MODEL INFERENCE IN ECOLOGY
Review round: 3
Reviewer: 2

Output:
Basic reporting: Appropriate.
Experimental design: N/A
Validity of the findings: N/A
Additional comments: This is a paper that I reviewed previously. I thank the authors for their efforts in responding to my comments; all matters raised in my previous review are now addressed to my satisfaction. The current paper presents a nice overview of issues associated with fitting and drawing inference from GLMMs, which readers will find useful.


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

Input:
Title: A BRIEF INTRODUCTION TO MIXED EFFECTS MODELLING AND MULTI-MODEL INFERENCE IN ECOLOGY
Review round: 3
Reviewer: 3

Output:
Basic reporting: as before
Experimental design: as before
Validity of the findings: as before
Additional comments: General comments

I had reviewed this manuscript already twice, and I have to say, that the authors largely dealt satisfactorily with my previous comments.

However, I still see some issues regarding the random slopes question. First, random slopes are applicable for covariates and factors (qualitative predictors) and the question which to include and the consequences of neglected random slopes are equally relevant in either case. The para about random slopes (L 415-438), however, leaves the wrong impression as if random slopes are only applicable for covariates. This needs to be fixed. Furthermore, the para still somewhat leaves the impression that the inclusion of random slopes is a matter of taste but after having carefully read the papers Barr et al. 2013 and Aarts et al. (2015. BMC Neurosci, 16, 94), I have to say it is not, but simply a must.

The other issue I still see is use of the term 'model selection' (L 763-981). What the authors leave complete open is the question of what is the purpose of it? I think this is an important question since there is really so much confusion about 'model selection' that I meanwhile came to the conclusion that the title of Burnham's and Anderson's book was badly chosen (the book itself I like lot). In fact, one sees so many papers that utilize model selection to identify a 'best' or 'minimum adequate model' and then test it (and just yesterday some colleagues of mine got a manuscript rejected because they were *not* doing this)... But this is just what statisticians refer to as a 'fishing expedition'. So without some explicit clarifications regarding the purposes of 'model selection' (and the 'no-goes' in this context) I feel the manuscript is incomplete and likely to contribute to misunderstandings prevailing.

Specific comments

L 44: remove 'best practice'?

L 102-103: I'd reserve the acronym GLM for Generalized (i.e., non-Gaussian) Linear Models.

L 194-195: body mass is not 'moved into' but 'added to' the random effects structure (since its fixed effect is kept in the model).

L 196: '… the correlation between the two *and also the fixed effect of body mass*'.

L 201: I'd cite also Barr et al. 2013 and Aarts et al. (2015. BMC Neurosci, 16, 94).

L 293-302: another example would be a model with a miss-specified random slopes structure (i.e., missing random slopes).

L 299-302: according to Barr et al. (2013) a fixed effect is most reliably tested comparing the fit of the full model with that of a reduced model lacking the fixed effect (but being otherwise identical) using a likelihood ratio test. In such a case, the question of residual degrees of freedom is obsolete.

L 319: I'd say such transformations 'aim at' (not 'ensure') the variance being homogeneous.

L 329: 'include*, for instance,* Poisson-distributed counts' (counts can form many other distributions).

L 331: 'or' rather than 'and'.

L 409: 'factors' rather than 'groups'.

L 408-412: the whole concept of 'variance' (in the way its is used in Gaussian models) isn't really applicable in most non-Gaussian models – so I'd replace 'interaction variance' by 'interactive effects' throughout this section.

L 415: random slopes are equally relevant and applicable in case factors (i.e., qualitative predictors). This is an important point which must not be missed! And the entire para must be adjusted accordingly.

L 418: they to not 'allow' but 'force' the fixed effect to 'have a common slope across all experimental units'.

L 421 & 323: Schielzeth & Forstmeier (2009) and Barr et al (2013) (and also Aarts et al. 2015) found clear and convincing evidence for these statements made; as such I find the term 'argue' misleading as it implies these just being opinions (which one could share or not).

L 434: this *likely' inflates Type I error rate.

L 435-438: this is too imprecise. A model can comprise, random intercepts, random slopes, and the correlations among them (but it can also comprise only random intercepts, only random slopes, or only random intercepts and slopes). The model the authors speak about here comprises all the three (i.e., random intercepts, random slopes, and the correlations among them) and only in such a model these correlations can be inspected. And in case of perfect correlations one could still fit a model comprising random intercepts and random slopes but not the correlations among them.

L 439-443: I'd also refer to the papers by Barr et al. and Aarts et al..

L 473: 'predictors' rather than 'data'?

L 596 & 599: I think one usually plots residuals versus fitted values.

L 660: delete 'coefficient'.

L 670: 'compl*e*mentary'.

L 720, 721 & 722: I'd write 'response variable' rather than 'data'.

L 726: delete 'test' ('test statistic' has a very specific meaning; but what is meant here is more generic).

L 747: 'it is *often* not possible'.

L 773-776: when just two models are compared, one lacking a term, this is isn't model selection but simply a way of getting a P-value for the term in question. Also, I would refer to the simpler model as a 'null model' (in the view of many researchers a 'null model' is an intercept only or intercept plus random effects model).

L 932: 'invalid results' in what sense?

L 967: 'uncertainty *in* the'.

L 990: 'unit*s*'.


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: EVALUATION OF THE GLYCEMIC EFFECT OF CERATONIA SILIQUA PODS (CAROB) ON A STREPTOZOTOCIN-NICOTINAMIDE INDUCED DIABETIC RAT MODEL
Review round: 1
Reviewer: 1

Output:
Basic reporting: There are some minor details that should be reviewed:
- FeSO4•7H2O subscript (P.11 L. 139)
- IC50  defined at the first use
- Uniform fonts and font sizes should be used. Please, review references and legends.
Experimental design: No Comment
Validity of the findings: Point 1. Please explain why the authors chose the doses for the treatments (500 mg kg-1 carob and 1000 mg kg-1 carob) in the induction of type 2 diabetic animal model? This point should be includes in materials and methods, would not be interesting a dose course?
Point 2. The authors describe the Free radical scavenging capacity and Ferric reducing antioxidant power as markers antioxidant activity In fact, Free radical scavenging capacity and FRAP can be used with this goal. However, it is not the only methodology, for exemple Lipid peroxidation (MDA levels) is well know used for antioxidante activity. Why the authors opted for DPPH and FRAP?
Point 3. ‘’...Although in vivo acute oral toxicity findings indicated a rise in ALP and urea of male rats as well as creatinine of female rats, the hsitological sections of liver of male and female rats showed normal architecture of hepatocytes... ‘’ What the authors think about this?
Point 4. HOMA-S and HOMA-IR showed a non-significant difference. Please
please includes a discussion for these results.
 Point 5. The study shows in vitro antioxidant activity in assay with synthetic radical (DPPH), that does not mimic physiological conditions. But in the discussion section the authors atributed the exvivo protection to the remaining β-cell from destruction owing to its antioxidant activity. What the authors think about this? Also, authors concludes that Carob pods possess antioxidant effects by inhibiting α-amylase and α-glucosidase. In my point of view the authors should explain this conclusion.
 Point 6. Authors concludes that ‘’Carob pods are non-toxic’’, it will be better: did not cause acute systemic toxicity. The conclusion section should be rewritten.
Additional comments: This manuscript describes the antioxidante and antihyperglycemic activity of the methanolic extract of Carob in nicotinamide-streptozotocin-induced diabetic rat’s model, and provide data to support that these activities. Overall the author provide a good body of work however, I have some suggestions that I believe would greatly improve this work.


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: EVALUATION OF THE GLYCEMIC EFFECT OF CERATONIA SILIQUA PODS (CAROB) ON A STREPTOZOTOCIN-NICOTINAMIDE INDUCED DIABETIC RAT MODEL
Review round: 1
Reviewer: 2

Output:
Basic reporting: - The tables is confused, please correct the number of tables and describe the parameters, not used abbreviations;

- Besides the effect on the α-amylase and α-glucosidase activity, what other enzymes or metabolic pathways could the compound be regulating? Stimulating the metabolism of carbohydrates in the liver, for example? Why? Please explain.
Experimental design: - The authors should include a figure of experimental design, to make clear the aim of the study;
-On which are carob concentrations based?
-Please, explain in the materials and methods why the used of nicotinamide to induce diabetes.
-Please add in all results (tables and figures) the experimental number.
Validity of the findings: No comments.
Additional comments: The study "Evaluation of the glycemic effect of Ceratonia siliqua pods (Carob) on nicotinamide-streptozotocin-induced diabetic rats model (#25216)" is designed well, the results are nicely summarized, and the findings are impressive and appropriate. This is a very nice article that needs only minor revision.


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: EVALUATION OF THE GLYCEMIC EFFECT OF CERATONIA SILIQUA PODS (CAROB) ON A STREPTOZOTOCIN-NICOTINAMIDE INDUCED DIABETIC RAT MODEL
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: This manuscript describes the antioxidante and antihyperglycemic activity of the methanolic extract of Carob in nicotinamide-streptozotocin-induced diabetic rat’s model, and provide data to support that these activities.


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: EVALUATION OF THE GLYCEMIC EFFECT OF CERATONIA SILIQUA PODS (CAROB) ON A STREPTOZOTOCIN-NICOTINAMIDE INDUCED DIABETIC RAT MODEL
Review round: 2
Reviewer: 2

Output:
Basic reporting: No comments.
Experimental design: In the experimental design figure, I suggest used different colors in the parameters, for example: the pharmacological assays one color, toxicological and chemical another color.
Validity of the findings: No 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: THE COMPLETE CHLOROPLAST GENOME OF COLOBANTHUS APETALUS (LABILL.) DRUCE: GENOME ORGANIZATION AND COMPARISON WITH RELATED SPECIES
Review round: 1
Reviewer: 1

Output:
Basic reporting: A well-constructed and detailed report of an apparently unremarkable plastid genome from a rather more remarkable plant. The English is clear and easy to follow with only minor and occasional grammatical errors.
Experimental design: The sequencing, assembly and repeat analysis appear to have been carried out thoroughly and I see no obvious issues that need further work. The phylogenetic analysis is not fully described (how was the ML analysis done, exactly?) and brings very little to the paper; the relationship to C. quitensis was never in any doubt, and the other Caryophyllaceae were dealt with better in Kang et al 2017. I would recommend removing this part of the manuscript. The authors could perhaps instead attempt an analysis of RNA editing sites, based on sequence conservation, even in the absence of transcript data. In addition, no attempt appears to have been made to look for any differences in the Colobanthus genome(s) that might play a role in adaptation to the relative extreme conditions under which the plants grow.
Validity of the findings: I have some minor comments on some of the annotations. The authors mention 'five conserved hypothetical chloroplast ORF (open reading frame) of currently unknown functions (ycf1, ycf2, ycf3, ycf4, ycf68)'. This is a very outdated view of these genes' functions. Ycf3 and Ycf4 are known to be assembly factors for Photosystem I and Ycf1 is claimed to be an inner membrane component of a protein import channel (although this is disputed). The ycf68 ORF probably doesn't encode a protein at all (Raubeson et al BMC Genomics 2007).

'...there were genes (ycf1 and accD) for which great acceleration in the rate of
sequence and/or structure evolution in C. apetalus and C. quitensis was observed'. No evidence for acceleration is provided in the manuscript; just because these gene are more divergent than others does not mean that their rate of change has accelerated. They may have always accumulated mutations more rapidly than other genes (indeed this is known to be the case in other lineages).

ClpP is a multisubunit complex, of which the plastid-encoded subunit is just one, so the plastid gene should really be labelled clpP1.
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: THE COMPLETE CHLOROPLAST GENOME OF COLOBANTHUS APETALUS (LABILL.) DRUCE: GENOME ORGANIZATION AND COMPARISON WITH RELATED SPECIES
Review round: 1
Reviewer: 2

Output:
Basic reporting: The authors present the complete sequence of the chloroplast genome of Colobanthus apetalus and its comparison with already published chloroplast genome of the Antarctic species Colobanthus quitensis.
Grammar and style are not acceptable, they shall be improved substantially. The authors need to consult a native English speaker. the text is often too lengthy, should be shortened.
The article is well structured with appropriate references. The chloroplast sequence of Colobanthus apetalus has been already published in GenBank.
Experimental design: 1.	The method of genome assembly is not well described. The authors state:

       The obtained high quality short reads were trimmed and then mapped to the reference cp
115 genome of Colobanthus quitensis (NC_028080) using Geneious v.R7 software (Drummond et al
116 2009) with default medium-low sensitivity settings. Contigs were formed by the mapped regions
117 (coverage > 5 reads) located between uncovered gaps. All contigs were mapped using
118 customized settings (minimum sequence overlap of 60 bp and 99 % overlap identity) with 30
119 iterations steps. Next, elongated sequences were de novo assembled to create a circular
120 chloroplast genome.

Which parameters of trimming were used? How was the de novo assembly performed? Were the mapped reads retrieved from the mapping file? Why were there “uncovered gaps” - the corresponding sequence data were missing?
As the reliable sequence is the prerequisite of the following analyses, all the steps leading to the final assembly should be properly clarified.

2.	Synonymous and non-synonymous substitution rates
There are well elaborated ways how to analyze Ka/Ks ratio, for example DnaSp (Librado and Rozas, 2009). The authors simply counted nt and aa substitutions, which is least informative and incorrect. The analyses based on e.g. DnaSp or PAML shall be applied.

3.	The two Colobanthus species are sister taxa in the phylogenetic tree. The addition of just a single species to the phylogenetic tree published by Kang et al. 2017 does not add very much to our knowledge. The Ka/Ks analysis of the cp proteins across the Caryophyllaceae family would be more contributing.
Validity of the findings: This topic of the manuscript is interesting but it represents only incremental contribution.
There are serious methodical problems described above, which affect the results.

In addition, the authors determined SSR regions. Mononucleotide repeats prevailed.  The homopolymer size often varies within the same individual. Did authors observe any evidence for heteroplasmy in their data? This aspect shall be mentioned in Discussion
Additional comments: The authors should clarify the method of genome assembly and perform new analyzes of the Ka/Ks ratios. Sequencing of chloroplast genomes in additional Colobanthus species would improve the impact of this project very much.


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

Input:
Title: THE COMPLETE CHLOROPLAST GENOME OF COLOBANTHUS APETALUS (LABILL.) DRUCE: GENOME ORGANIZATION AND COMPARISON WITH RELATED SPECIES
Review round: 2
Reviewer: 1

Output:
Basic reporting: There are still some typos and grammatical errors in the text, especially in the newly added sections, but overall the text is clear and easy to understand.
Experimental design: The experimental design is fine as far as it goes - the addition of more genomes might allow more interesting biology to be explored.
Validity of the findings: I believe the findings are valid.
Additional comments: All of the reviewers' criticisms of the initial submission have been satisfactorily addressed, apart from the desire to extend the project to other related genomes.


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

Input:
Title: THE COMPLETE CHLOROPLAST GENOME OF COLOBANTHUS APETALUS (LABILL.) DRUCE: GENOME ORGANIZATION AND COMPARISON WITH RELATED SPECIES
Review round: 2
Reviewer: 2

Output:
Basic reporting: The revised version of the manuscript was improved, but not substantially. The presented knowledge is incremental. More chloroplast genomes related to Colobanthus are necessary to sequence to achieve the improvement of the phylogenetic tree of Caryophyllaceae.
Experimental design: The calculations based on Ka and Ks were corrected
Validity of the findings: No important conclusions are drawn.
Additional comments: The addition of a single chloroplast genome of the sister species of the previously sequenced and published Colobanthus  quitensis does not contribute to our understanding of phylogeny or adaptation in Caryophyllaceae. Please, sequence more plastid genomes, e.g. of Spergula to broaden our knowledge of the evolution in Caryophyllaceae.


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: GIANT WORMS CHEZ MOI! HAMMERHEAD FLATWORMS (PLATYHELMINTHES, GEOPLANIDAE, BIPALIUM SPP., DIVERSIBIPALIUM SPP.) IN METROPOLITAN FRANCE AND OVERSEAS FRENCH TERRITORIES
Review round: 1
Reviewer: 1

Output:
Basic reporting: English is acceptable (but it is not my mother language). Literature is not suficiently and adequately explored. Article structure is deficient. Relevant results are hiddend by not original data.
Experimental design: Manuscript meets Aims and Scope of the Journal. Research question is well stated. Methods are not fully with sufficient detail.
Validity of the findings: Impact and novelty are obscured by many secondary informative information obtained from anecdotal observations and from literature, sometimes both sources are mixed and confounded with each other. Data are partially robust. Conclusion is not fully supported by the results.
Additional comments: In my enthusiasm for providing a quick review, I did not check my first revision for grammar errrors. Since my review is going to be published, I would ask you to accept the checked version of my review (below). If necessesary, I can send to you a version with corrections highlighted.

Best,
Fernando Carbayo.

1. 1. Basic reporting
English is acceptable (but it is not my mother language). Literature is not suficiently and adequately explored. Article structure is deficient. Relevant results are hiddend by not original data.
2. 2. Experimental design
Manuscript meets Aims and Scope of the Journal. Research question is well stated. Methods are not fully with sufficient detail.
3. 3. Validity of the findings
Impact and novelty are obscured by many secondary informative information obtained from anectodal observations and from literature, sometimes both sources are mixed and confounded with each other. Data are partially robust. Conclusion is not fully supported by the results.

In this manuscript the authors provide a number of new records of exotic bipaliine species introduced into France and overseas French territories. Part of the records were gathered with the collaboration of citizens during the last four years. Identification of the specimens from up to five species was conducted through examination of pictures of the specimens and COI gene fragment sequences, and compared against DNA sequences from GenBank. Since I am not expert in the molecular methods my comments on this point should be considered anecdotal.
Regarding the general aspects of the manuscript, I noticed main deficiencies as follows: (a) part of the headings and subheadings are out of place, (b) statements in Results are not based on evidences, (c) methods on which behavioural aspects (predation, reproduction) reported in Results and Discussion are not presented, and (d) behavioural aspects bring no novelty and are anecdotal. The whole manuscripts needs a profound revision and many sections should be deleted:

MATERIAL AND METHODS (M&M)
It is not stated how the descriptions of the species were done. It is not presented how behavioural and reproductive observations were conducted (although they should be deleted since they are out of the scope of the manuscript).

RESULTS
Description of B. kewense (lines 225-237) is a practically a copy-pasted version of Winsor’s (1983) description (as acknowledged by the authors). This is wrong. In this context, the purpose of the description is to provide evidence that the examined specimens do belong to  kewense. Authors should have described their own specimens, and eventually conclude that the description matches that of B. kewense. The same is valid for the remaining known species.
“Predation of earthworms”, and “Morphological evidences of reproduction by scissiparity” of B. kewense (lines 242-249) are out of the scope of the work and Methods followed by the authors for obtaining associated data are not provided. These two subheadings should be deleted (out of scope).
Line 264: This statement has no support from the data and M&M (How did authors obtained these results? Did they offer non-earthworm prey?). These lines should be deleted.
After having read the description of B. kewense, I am not sure whether the description of external aspect of Bipalium multilineatum (lines 269-288) is original or it is a version of a  description found elsewhere. Only descriptions based on collected specimens are valid for identification purposes. This should be stated unequivocally in M&M and the Results presented accordingly.
Lines 289-293 are not “Morphology” but comparative discussion and should be placed in a separate subheading. The same for every “Morphology” section of all species.
Source of the description of Bipalium vagum (lines 310-322) is uncertain. At least body dimensions are from the holotype found in Jones & Sterrer (2005) not from the specimens (or pictures) collected by the authors; this is wrong (see comment for B. kewense). It seems that the remaining description is based on the observation of the French specimens colelcted by the authors.
“Remarks” (lines 345-348; 363). Authors state that “The COI barcode of this specimen is clearly different from all other known sequences” and from this difference they conclude that it represents a different species. As presente, this is a weak argument. For instance, see the two terminals of B. venosum on Fig. 2; they are clearly different, but also considered to belong to just one species. The statement should be rewritten.

DISCUSSION
Supporting references should be given (lines 390-393).
Subheadings “Possible specific identity of the “black” and “blue” species”, and “A note about taxonomy of Diversibipalium” should be moved to the “Remarks” of either species.
Subheading “Predation in Bipaliines” (lines 408-431) should be deleted. The statements presented are purposeless and not derived from the M&M nor from Results.
Lines 438-444: It is concluded that “clearly, B. kewense is an invasive species”. Further in the same paragraph the authors declare to have examined the literature and citizen-science information to show that B. kewense is not confined to indoors but it may also be found outdoors. From having recorded B. kewense outdoors, authors conclude that this species is invasive. The meaning of is term, however, is not free from univocal meaning. What does it mean invasive for the authors? For a discussion, see Coulatti & MacIsaac (A neutral terminology to define ‘invasive’ species. Diversity and Distributions, (2004) 10, 135–141). Most records shown do no report the environs: indoors, outdoors, in natural habitats, natural forest areas, planted forests? There are indeed no reports on possible detrimental effects on the native fauna or rural activities (earthworm farms, grasslands...) apart from the two references provided (Winsor, 1983a, 1888b) in which it is reported that B. kewense is “a minor pest in earthworm farms”. To the best of my knowledge, this species has not been found in natural habitats outside its original distributional range area. The title of the manuscript is revealing in showing it: “flatworms [...] in metropolitan France [...]”. By reading the manuscript, I do not see reason for considering the species as invasive, independently from the habitats it is found. In the same rationale, the House Sparrow Passer domesticus could also be considered an invasive species. Author should make it clear what does ‘invasive’ mean, as suggested above.
It is unclear whether distributional data presented on lines 445-454 and Fig. 38 are the same shown in Fig. 1.

CONCLUSIONS
Some conclusions are not supported by the Results.
Last sentence is a belief (as they said) since no data are provided.

I would make additional minor comments to the manuscript, but at this stage, the text should best be rewritten. Nevertheless, I made minor suggestion in the PDF version of the manuscript. I recomend Major revision.

Fernando Carbayo


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: GIANT WORMS CHEZ MOI! HAMMERHEAD FLATWORMS (PLATYHELMINTHES, GEOPLANIDAE, BIPALIUM SPP., DIVERSIBIPALIUM SPP.) IN METROPOLITAN FRANCE AND OVERSEAS FRENCH TERRITORIES
Review round: 1
Reviewer: 2

Output:
Basic reporting: OK
Experimental design: OK
Validity of the findings: OK
Additional comments: General comments
This is a very interesting and well-presented study on a neglected group of invasive species. The figures are highly informative, particularly the photos of the specimens.
The professional English is generally good.
The use of citizen science is a very appropriate and original method to obtain detailed information on the distribution of these animals.
In addition to identification through external features the authors appropriately use DNA barcoding.

Specific comments
I have made annotations on the pdf of the manuscript, suggesting a rather limited number of changes in the text of the manuscript, as well as posing a few queries. I will not detail these remarks here, except the one concerning the use of French in the title of the manuscript.
I do strongly suggest that the authors strike the first four words (plus exclamation mark) from the title. The major reason is the use of the French ‘’Chez moi!’’. As I understand French, I can see that it is funny. However, most of the world population does not understand French and thus these words would not mean anything to the majority of the world population in general and of scientists in particular. Second, use of the word ‘’giant’’ to describe Hammerhead worms may be too much. Yes, for triclads they are big but usually people associate the word ‘’giant’’ with a different scale (elephants, blue whales). So, using ‘’giant’’ in the title may put people to stand on the wrong foot.


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: GIANT WORMS CHEZ MOI! HAMMERHEAD FLATWORMS (PLATYHELMINTHES, GEOPLANIDAE, BIPALIUM SPP., DIVERSIBIPALIUM SPP.) IN METROPOLITAN FRANCE AND OVERSEAS FRENCH TERRITORIES
Review round: 1
Reviewer: 3

Output:
Basic reporting: Overall, the article is clear and the English is correct. Relevant references are listed and the context is sufficient. Structure might be slightly improved. Results are interesting and useful for future studies.

Please check attached pdf for further comments.
Experimental design: The article contains original primary research including new reports of invasive hammerhead worms, new COI sequences and their analysis. Furthermore, two putative new Bipaliinae species found in France and Mayotte are reported.

Overall, the experimental design is correct.

Please check attached pdf for further comments.
Validity of the findings: Please check attached pdf for comments.
Additional comments: Please check attached pdf for 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: GIANT WORMS CHEZ MOI! HAMMERHEAD FLATWORMS (PLATYHELMINTHES, GEOPLANIDAE, BIPALIUM SPP., DIVERSIBIPALIUM SPP.) IN METROPOLITAN FRANCE AND OVERSEAS FRENCH TERRITORIES
Review round: 2
Reviewer: 1

Output:
Basic reporting: This new version of the manuscript meets PeerJ standards with regard to organization of the the text. Unnecessary or out-of-scope sections (reproduction, predation) have properly been deleted. Species descriptions and comparison of the descriptions against those known species are robust. A reflections on the invasiveness of the species is properly stated.  Authors are right in their criticism to the example I had provided on the invasiveness of House Sparrows in the first review. They also discuss what 'invasive' means and conclude that the species presented in the manuscript are at least potentially invasive. I made minor comments and corrections on the PDF version of the manuscript. I suggest publication with minor changes (see PDF archive).
Experimental design: Adequate.
Validity of the findings: Adequate. Data are robust. Conclusion is supported by the results.
Additional comments: See above.


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

Input:
Title: GIANT WORMS CHEZ MOI! HAMMERHEAD FLATWORMS (PLATYHELMINTHES, GEOPLANIDAE, BIPALIUM SPP., DIVERSIBIPALIUM SPP.) IN METROPOLITAN FRANCE AND OVERSEAS FRENCH TERRITORIES
Review round: 2
Reviewer: 2

Output:
Basic reporting: OK
Experimental design: OK
Validity of the findings: OK
Additional comments: This revised version is a great improvement of the first draft of this manuscript, as the authors responded well to  the detailed comments of the reviewers and completely restructured their manuscript.

However, I still feel that in their descriptions of B. kewense,  B. multilineatum, and B. vagum they still fail to make fully clear whether the descriptions refer to the specimens collected (as it should) or represent a general description of the species.  The confusion already starts with the first sentence of the description, which concludes that the animals correspond to the published morphological descriptions of the species. This conclusion should come at the end, i.e. after the description of the French animals. Generally, a (taxonomic) description is followed by a Discussion section in which it is explained to what extent the animals described correspond to a certain species and how they differ from other, closely related and/or similar-looking species. So, I suggest that the authors rename their heading ‘’Differentiation from other species’’ as ‘’Discussion’’ and start this with the first sentence of the current  description of Morphology and Colour Pattern.


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: GIANT WORMS CHEZ MOI! HAMMERHEAD FLATWORMS (PLATYHELMINTHES, GEOPLANIDAE, BIPALIUM SPP., DIVERSIBIPALIUM SPP.) IN METROPOLITAN FRANCE AND OVERSEAS FRENCH TERRITORIES
Review round: 2
Reviewer: 3

Output:
Basic reporting: The authors of the paper "Giant chez moi! Hammerhead flatworms (Platyhelminthes, Geoplanidae, Bipalium spp., Diversibipalium spp.) in metropolitan France and overseas French territories have satisfactorily answered the review comments and done many of the suggested improvements.

I only have very minor improvements to suggest:
> Line 73: Peninsular (instead of Peninsula).
> Line 181: I think that 'belong' should be 'belonging'.
> Line 462: winter (lower case).
> Line 205: one parenthesis is opened but not closed.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: No additional comments


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

Input:
Title: MOLECULAR RESPONSE OF CANOLA TO SALT STRESS: INSIGHTS ON TOLERANCE MECHANISMS
Review round: 1
Reviewer: 1

Output:
Basic reporting: 1. Line 30, can rephrase to "suggests what researchers should focus on in future studies".
2. Line 45, "are taken up" to "take up" or "absorb".
3. Line 46, "are" to "is"; "compound" to "compounds".
4. Line 56, delete the 2nd "is"; Line 57, delete the "is".
5. Line 64-66, references are needed here.
6. Line 81-87, the Survey Methodology section is not needed.
7. Line 115-116, the sentence "Transcription factors directly change the expression level of many genes" is unclear.
8. Line 127-132, the SDS PAGE principle is not necessary; it is just a basic analytic technique.
9. Line 161, for a literature review, "seems that" sounds unsure, can be rephrased to it is proposed that.
10. Line 165, the 1st sentence can be deleted.
11. Line 199-200 can be deleted. The basic molecular biology concept is not necessary here.
12. Line 211-212, the sentence is unclear.
13. Line 220, "less" than what?
14. Line 221, "undergoes" to "undergo".
15. Line 227, "post-translational" to "post-transcriptional".
16. Line 254-255, this sentence is not needed.
17. Line 272-278, references are needed.
18. Line 294, "future" to "subsequent".
19. Line 310-312, this sentence is unclear. a number of  or  the number of?
20. Line 322, what "these protein" represents? (Sub-group A was mentioned).
21. Line 338, "membranous" to "membrane".
Experimental design: no comment
Validity of the findings: no comment
Additional comments: No additional comments


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

Input:
Title: MOLECULAR RESPONSE OF CANOLA TO SALT STRESS: INSIGHTS ON TOLERANCE MECHANISMS
Review round: 1
Reviewer: 2

Output:
Basic reporting: English is clear and professional.
Experimental design: Experiment design looks good  and research is under scope of the journal
Validity of the findings: Experiments are well designed.
Additional comments: i recommend acceptance of the article for publication.


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

Input:
Title: MOLECULAR RESPONSE OF CANOLA TO SALT STRESS: INSIGHTS ON TOLERANCE MECHANISMS
Review round: 1
Reviewer: 3

Output:
Basic reporting: In this review, the authors focused on studies of the molecular response of canola to salinity to unravel the different pieces of the salt response puzzle. The paper includes a comprehensive review of the latest studies, particularly of proteomic and transcriptomic analysis, which will be helpful for understanding the mechanisms of salt tolerance and cultivating the salt tolerant canola varieties. However, this manuscript still has some content need to be modified or explanted.
Experimental design: The experimental design is reasonable。
Validity of the findings: no comment
Additional comments: 1.	Line 468-470: the authors introduced that the report examines the results of proteomic, transcriptomic, genetic engineering, QTL mapping, and genetic studies to put together current understanding of canola salt response. However, there is no description of QTL mapping in the text, and there is less explanation in transcriptome. Could you please make an explanation?
2.	line 479-486: in this paragraph, the author introduced many methods, and told us that the progress of these methods will remarkably help to elucidate the unknown or less-known aspects, whether the author can explain in detail how they can be applied in future studies.
3.	In the paragraph of ‘Dynamic Changes of Canola Transcriptome and Proteome. This section describes the transcriptome dynamic change rarely, only discussed in proteomics level. Could you please add some content about dynamic changes of canola transcriptome?
4. line142 ‘root and leaves’ was changed to ‘roots and leaves’.
5. line250 ‘root and leaves’ was changed to ‘roots and leaves’.


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: IDENTIFYING POTENTIALLY MARKER SYMPTOMS OF ATTENTION-DEFICIT/HYPERACTIVITY DISORDER
Review round: 1
Reviewer: 1

Output:
Basic reporting: This study is well written, with clear and proper language throughout the manuscript. In both the introduction and the discussion sections the authors cite the relevant literature to properly frame the research problem and the study’s conclusions. The structure of the paper conforms to PeerJ’s standards, with the exception of the “Discussion” heading in the abstract, which does not begin on a new paragraph. All the figures and tables are relevant, of high quality, and are properly labeled and described. The authors supplied the raw data and the items in the file are properly labeled and coded.
Experimental design: The current study consists of an original primary research that falls within the scope of the PeerJ journal. The research question is well defined and relevant. The authors clearly state how this research fills a gap in the available literature. The research was performed to a high technical and ethical standard. The methods were described with sufficient detail to allow for replication, except for the parallel analyses, as commented on point #1.
Validity of the findings: The rationale and benefit to the literature was clearly stated by the authors. The data collected was robust and the analyses performed were appropriate to the research question. The conclusions were well stated, linked to the original research question and limited to the obtained results (with the exception of those commented on point #7).
Additional comments: The present work aims to replicate some relevant findings from the attention deficit hyperactivity disorder (ADHD) literature with a Spanish-speaking Chilean sample. Specifically, the study is concerned with assessing the discriminative power and relative severity of the symptoms of ADHD, as measured by the inattention and hyperactivity scales of the Child and Adolescent Behavior Inventory (CABI). The authors argue that considering the different psychometric properties of the item scores, as opposed to the current criteria outlined in the fifth edition of the Diagnostic and Statistical Manual of Mental Disorders (DSM-5) where all indicators of the disorder are given equal weight, might enhance the accuracy of the ADHD diagnosis. To this end, the authors employ Samejima’s graded response item response model to evaluate the discriminative power and relative severity of the ADHD symptoms, and provide evidence that indeed the properties of the item scores have substantial variation, in particular for the inattention scale. Finally, the authors suggest that the diagnosis process of ADHD could be improved by weighting the severity of each symptom, and by considering the possibility of using the most informative symptoms as markers.

All of my concerns about the paper are very minor and easy for the authors to address. I will list them next.

1)	In the data analysis subsection line 155 the authors state that they used parallel analysis to evaluate the unidimensionality of the scales used in this study. However, they don’t give enough information regarding how they implemented the method to allow for replication. In this regard, the authors should inform of: a) the software/code they used; b) the criteria used to summarize the random eigenvalues (e.g., the mean, the 95th percentile, etc.); and c) the procedure used to generate the random variates (e.g., random column permutations of the empirical data, data generated from a multivariate distribution, etc.). Further, I believe that the information regarding the use of exploratory factor analysis to obtain the parallel analysis eigenvalues is erroneous, as the random eigenvalues have a mean of 1, which indicates that these are the eigenvalues from the full correlation matrix (i.e., the principal component eigenvalues).

2)	In lines 165 and 166-167 the authors propose a Type I error rate of 0.01. Why 0.01 and not the standard 0.05?

3)	In line 165 the authors should specify what they consider as RMSEA values close to zero, including the appropriate references.

4)	As all the discrimination parameters shown in Table 1 are greater than 1.70, they all fall in the ‘very high’ range; in line 202 it says that they were ‘high’ or ‘very high’.

5)	According to Table 1, the most discriminative item for the HI subscale was item 5 (it says item 6 in line 207). Additionally, in the table it says that the ‘a’ parameter was 3.62, while in line 207 it says 3.78. Also, the second and third most discriminative items have practically the same parameter estimate (2.96 and 2.94) so it may make more sense to mention them both in line 208.

6)	The values of 1.13 and 1.84 given in lines 230 and 233 do not match the position of the lines in Figure 4. For example, for the most severe item a score of 4 touches the horizontal axis at a value higher than 2.

7)	Although the assertion in lines 297 to 299 is supported by the literature (e.g., Haslam et al., 2006; Marcus & Barry, 2011), it cannot be derived from the analyses of the current study. To do that, the authors would need to perform a formal taxometric analysis. So, I suggest that the authors change the wording on this sentence to reflect that this is their view based on the literature and not on the results of the current study.


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

Input:
Title: IDENTIFYING POTENTIALLY MARKER SYMPTOMS OF ATTENTION-DEFICIT/HYPERACTIVITY DISORDER
Review round: 1
Reviewer: 2

Output:
Basic reporting: The quality of this study is good, with clear and professional English.
Experimental design: All is good, except for the method, as commented on point #1.
Validity of the findings: The findings were generally valid. My main concern here relates to the data collected was based on parental rating. I raise my comment on point #2.
Additional comments: The purpose of this study was to replicate the results of previous research by evaluating the discriminative capacity and relative severity of ADHD symptoms. The result suggests that the diagnosis process of ADHD could be improve by weighting the severity of the symptom and even to assess the possibility of defining ADHD marker symptoms.
My main concerns about this paper are list below:

1) You chose 6-15 years old students as your sample, which includes children, preadolescent children, and adolescent. The age range is wide and might affect the result. Have you consider this issue and use the adequate statistical method to eliminate age difference?

2) The psychometric properties of the items were based on parental rating, as you mentioned it in the research limitation. I believe that teacher’s rating might be an important data in your study. Since you didn’t collect these data, I would suggest authors can provide the reason.

3) Base on literature and background knowledge author provide in introduction. I would suggest author can provide hypothesis in the introduction. And see if the result meet your expectation or not.


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

Input:
Title: IDENTIFYING POTENTIALLY MARKER SYMPTOMS OF ATTENTION-DEFICIT/HYPERACTIVITY DISORDER
Review round: 2
Reviewer: 1

Output:
Basic reporting: The basic reporting in this article meets the standards of PeerJ.
Experimental design: The research design of this study meets the standards of PeerJ.
Validity of the findings: The validity of the findings derived from this study meets the standards of PeerJ.
Additional comments: The authors have satisfied all my concerns. I therefore recommend this article for publication.


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

Input:
Title: IDENTIFYING POTENTIALLY MARKER SYMPTOMS OF ATTENTION-DEFICIT/HYPERACTIVITY DISORDER
Review round: 2
Reviewer: 2

Output:
Basic reporting: No Comments.
Experimental design: The authors have appropriately addressed previous concerns that were pointed out.
Validity of the findings: The authors have appropriately addressed previous concerns that were pointed out.
Additional comments: The authors have completely addressed the questions provided by the reviewer and have completely revised the manuscript. The reviewer considers this manuscript now is in good shape and has no further questions/concerns on this manuscript. Congratulations to the authors for their hard work and the effort they have made.


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: INFLUENCE OF APREPITANT ON THE PHARMACODYNAMICS AND PHARMACOKINETICS OF GLICLAZIDE IN RATS AND RABBITS
Review round: 1
Reviewer: 1

Output:
Basic reporting: Clear language has been used. Appropriate literature has been cited. The figures and tables have been professionally presented. The results section links well with the "hypothesis" of the paper.

Overall, the manuscript is written in good English and flows well. However, there are minor grammatical errors that can be easily rectified. For example, results section in the abstract- doe needs to be changed to dose. Results section- “these results confirming that …”, needs to be “these results confirm that …”. Discussion section, “The biphasic blood glucose reduction was note* observed in rabbits …”

In the introduction section, the line “In general, the overall … high risk individuals” seems to be out of place.
Experimental design: Original research, well defined research question, appropriate use of animal models and statistics
Validity of the findings: 1.	It is possible that the effect of concomitant administration of gliclazide and aprepitant on blood glucose level and insulin level (in normal rats, diabetic rats, and normal rabbits- tables 1, 2, and 3) is simply an additive effect, especially for the single dose treatment. Aprepitant alone seems to have a modest effect on blood glucose levels (and a strong effect on insulin levels- please show the data in the manuscript figures). Granted that the authors provide strong evidence suggesting the pharmacodynamics of gliclazide has been influenced (table 4), I would describe the effects of concomitant administration on insulin levels (figure 3) and serum gliclazide levels (figure 4) as modest changes. It would be optimal if the authors can convince the readers that these modest changes in insulin level and serum gliclazide levels indeed lead to increased glucose levels via pharmacodynamic interactions and not an additive effect.
2.	The results section seems rushed. The authors must describe the results in detail using words rather than just referring to the tables and/or figures. It might also be useful to split the results section into smaller chunks using sub-headers such has pharmacodynamics, pharmacokinetics, etc.
3.	In the results section, the authors say “These results confirming that the blood glucose reduction with gliclazide treatment was relatively higher in diabetic condition compared to normal condition”.  Even though they have used the word ‘relatively’ in the sentence, it is not appropriate to make such comparisons without statistical evidence.
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: INFLUENCE OF APREPITANT ON THE PHARMACODYNAMICS AND PHARMACOKINETICS OF GLICLAZIDE IN RATS AND RABBITS
Review round: 1
Reviewer: 2

Output:
Basic reporting: In this manuscript author tried to show the influence of aprepitant on pharmacodynamics (PD) and pharmacokinetics (PK) of gliclazide in rats and rabbits by analyzing glucose, insulin and drug bioavailability in blood samples of drug (gliclazide, gliclazide+ aprepitant) treated and non-treated rats and rabbits. It is a simple and straightforward study with valid reason and good idea (across species). Author also admitted couple of limitations, I appreciate that. However, I have couple of queries for this manuscript.

1.	Author claimed/concluded that aprepitant significantly influenced the pharmacodynamic activity of gliclazide by CYP3A4 inhibition in animal models, while there was no data shown to the relevant claim. If author wants to claim aprepitant's inhibitory role on  CYP3A4, either expressions levels of CYP3A4 or interaction studies of CYP3A4 with drug, correlating the PD and PK values should be shown.

2.	Tables showing the values of normal and diabetic animals can be shown side by side or in the form of scatter plot. It would be much easier for reader to analyze.

3.	Grammar/typing errors in line number 50 and 53
Experimental design: no comment
Validity of the findings: no comment
Additional comments: No additional comments


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

Input:
Title: INFLUENCE OF APREPITANT ON THE PHARMACODYNAMICS AND PHARMACOKINETICS OF GLICLAZIDE IN RATS AND RABBITS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors have revised the manuscript to overcome all grammatical and flow problems.
Experimental design: Look good.
Validity of the findings: The addition about the "additive effect" makes the manuscript scientifically sound.
Additional comments: The authors have addressed all of the reviewer 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: INFLUENCE OF APREPITANT ON THE PHARMACODYNAMICS AND PHARMACOKINETICS OF GLICLAZIDE IN RATS AND RABBITS
Review round: 2
Reviewer: 2

Output:
Basic reporting: Authors addressed all my concerns that i raised for this manuscript.
I recommend this manuscript for publication in peerJ journal.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: No additional comments


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

Input:
Title: LARGE MAMMAL BURROWS IN LATE MIOCENE CALCIC PALEOSOLS FROM CENTRAL ARGENTINA: PALEOENVIRONMENT, TAPHONOMY AND PRODUCERS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript is well written, the English grammar is, in some cases, rather old-fashioned so I have edited it with track change to bring it more into line with modern scientific reporting.

The literature review is exhaustive and up to date.

The article is structured according to current convention for scientific reports. The raw data is in the manuscript as well as supplementary information

The analysis and interpretation of the burrow structures  is sound and is a good example of how morphometric landmarks analysis can be successfully applied to field outcrops.
Experimental design: The research topic is within the scope of Peer J as it is based on empirical data collected in the field- analysed and synthesised with a modern statistical approach to prove the origin and preservation mode of these enigmatic tubular structures interpreted as mammalian burrow casts. The authors go in to discuss the palaeoenvironmental significance of these structures which is a definite advance in our knowledge to date.

The methods are fully and succinctly explained
Validity of the findings: The interpretations are based on comparison of the study set with other ancient burrow casts as well as modern fossorial mammals, The presence of bone fossils in the casts is as an indicator of the possible burrower is treated with the proper circumspection.

The two sedimentary facies are involved in infilling of the burrows is novel and useful information to be tested on similar occurrences elsewhere. The sedimentological interpretations are sound and backed up with the relevant references.

Linking the occurrence of burrow casts to rapid environmental change is not new, but there is always scope for such field based studies to back this up.
Additional comments: My detailed comments are in track change

Overall a very competent and informative study with something new to say about the infilling sequences and the environmental significance of vertebrate burrow casts in the fossil record.

I would like to see the outcrop area plotted on the map
I would also like to see a longitudinal profile of a generalised burrow cast showing the thickness relationships of the two facies and the onlapping with the burrow walls both down burrow and across burrow


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: LARGE MAMMAL BURROWS IN LATE MIOCENE CALCIC PALEOSOLS FROM CENTRAL ARGENTINA: PALEOENVIRONMENT, TAPHONOMY AND PRODUCERS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The English grammar used through the manuscript is clear and professional. However, as I am not a native English speaker my grammar corrections are limited.
The introduction and background are well presented and completed with actualized literature. The figures are relevant, high quality, and well labeled, and the raw data is supplied.
Experimental design: The research is original, with primary data analysis.  Although, the structures were partially and briefly described (Genise et al., 2013), but a detailed description and analysis was missing. The research questions are clearly stated, relevant, and meaningful and followed throughout the manuscript.  The technical methods used to analyze the data are modern, proper and well described to replicate it.
Validity of the findings: The manuscript is a good example of how to deeply analyze a set burrows of assorted morphologies and sizes. The evaluation of its likely producers is exhaustive and the analysis of the taphonomy of the burrows to finally infer its paleoecological and paleoenvironmental meaning its also very well performed.
Additional comments: I found one minor aspect to be consider through the manuscript. The authors talk continuously about the features of the “burrow fills”, as referring to the main burrow structure. I understand that the burrow fill is one of the features of the burrow itself, even though that is what is mostly observable. The sharp contact between the host rock and the burrow fill is actually the fossil burrow. In some cases could result valid the use of burrow fill as referring to the whole structure (Line 189), but in others it doesn’t (line 19-21). Please consider revising its use in the whole manuscript.
For example, in line 19-21 “Geometric morphometric analysis of transverse cross-sections support the distinction of subcircular and elliptical (horizontally flattened) fills.” What is subcircular or elliptical is the burrow itself and not the burrow fill.
Line 189. “Description of large burrow fills”. Could result correct if you are describing the burrow fill, But, if is used as synonym of burrow and you are describing other attributes of burrows, as the burrow architecture, it results tricky.


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: LARGE MAMMAL BURROWS IN LATE MIOCENE CALCIC PALEOSOLS FROM CENTRAL ARGENTINA: PALEOENVIRONMENT, TAPHONOMY AND PRODUCERS
Review round: 1
Reviewer: 3

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: This is an interesting and professionally designed study that significantly contributes to the evolutionary paleoecology of fossorial behavior, and, of course, is a very detailed and comprehensive study of the Argentinean occurrence. The ms well matches the requirements of PeerJ in all relevant aspects. I do not see potential to improve the paper except for minor formal mistakes or inconsistencies (see marked pdf).
I am just wondering how long it may have taken to completely fill especially the large-sized burrows. Is there any chance to constrain the duration of this process? If there was much time it is remarkable that there seems almost no evidence for reoccupation and restructuring of the primary burrows.
Well done!

Sebastian Voigt, 2018-04-07


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: IMPACT OF INPUT DATA (IN)ACCURACY ON OVERESTIMATION OF VISIBLE AREA IN DIGITAL VIEWSHED MODELS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript was reasonably well organized, but I struggled with some of the writings.

1.1. This paper clearly provides its purposes (Lines 92-95). But, the scope of the work presented in this paper is narrower than the purposes. In the introduction, the aim was to evaluate the effects of input data accuracy, terrain configuration, and a number of visual obstacles, as well as the height of forests. However, this paper only deals with the input data accuracy and height of obstacles. Please describe this purpose more concisely, or supplement it with other results.

1.2. All dataset names are always used throughout after they are defined (Lines 115-122) in order to keep consistency and to help interpretation. Several different representations of the datasets (e.g., lines 169 and 202) can give a confusion when interpreting related figures and tables.

1.3. OFFSETA is a term in specific GIS software (Line 136). Please provide a brief explanation of the process instead of just proving the OFFSETA parameter in the Viewshed tool.

1.4. When the authors compare spatial differences among the datasets (Lines 188-197), using a table or a graph may assist readers to easily understand the result.

1.5. Thank you for providing the raw data. But, if the locations of random observer points are also supplied in raw data, it would be very helpful to understand analysis results.

1.6. Minor suggestions:
1) Line 174, “ca” might be “are”.
Experimental design: The authors well explained each individual step of the analysis. However, the explanation of the sampling may be improved upon, and some additional descriptions are necessary.

2.1. 104 sample locations were chosen using stratified random sampling with three categories of the proportion of forest and three categories of the standard deviation of elevations. Thus, I think the number of samples might be a multiple of 9 to contain the same number of samples in each category. Please explain why you selected this number of samples.

2.2. Related to the sampling again, sample locations are highly clustered in the northern part. Are there any reasons for this clustering?

2.3. The authors should provide a data source for the calculation of elevation differences (i.e., the standard deviation of elevation) and forested proportion. Especially, the elevation differences can vary considerably according to a source dataset.

2.4. I do not understand the meaning of the last sentence in 2.1 Sampling locations. I thought the authors do not choose adjacent samples, but I saw some adjacent map pages in the raw data.

2.5. The authors compared spatial differences among the results of viewshed analyses from different datasets. However, the term of spatial difference is not familiar to me. Please include a detailed process for the spatial difference calculation.
Validity of the findings: The authors found that visible areas are overestimated in a small-scale dataset and heights of obstacles have a minor effect on a viewshed analysis.

3.1. However, the overestimation might result from a smaller variance (or a standard deviation) of elevations in small-scale datasets than large-scale datasets. Because the authors also knew the effect of an elevation variance on the size of a visible area, I think they used the stratified random sampling. Therefore, a useful addition may be investigating the relationship, if it exists, between the sizes of visible areas and the variances of elevations among the different datasets.

3.2. The authors also classified the sample according to the proportion of forests. But, they did not examine different impacts of obstacle heights on the sizes of visible areas according to forest proportions. I think it also would be worth to be investigated.
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: IMPACT OF INPUT DATA (IN)ACCURACY ON OVERESTIMATION OF VISIBLE AREA IN DIGITAL VIEWSHED MODELS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript is written clearly, with few errors. It is well-organized and logically structured. The figures are helpful and well-done. The background and motivation are solid, and references are appropriate, There are others that could be included, but I don't think it's essential.

It is not clear if the raw data are shared - the editor can confirm this.

The paper provides an aim, but not any specific hypotheses - see below for more comments about this. It could be strengthened with a couple of specific questions that the results already incorporate.

One correction: in Table 1 the terms 'large scale' and 'small scale' have reversed meaning to that of conventional cartographic usage. 1:5000 is large scale, as the fraction 1/5000 is relatively large, while 1:500,000 is small scale, as 1/500,000 is relatively small.
Experimental design: The design is rigorous and enables the authors to address several aspects of their research aims. However, not all could be considered with this experimental design.

Starting on line 92: "the aim of our study was to evaluate the effects that input data accuracy, terrain configuration, number of visual obstacles such as forests and buildings, and the quality of expertly assigned obstacle height (particularly of forests) have on the results of simple binary viewshed analysis." In fact, the study is able to effectively demonstrate that DSMs constructed by 'adding' volumes for forested and built up areas result in overestimation of the iewshed area. It is not possible for this investigation to determine specific contributions of data accuracy, spatial resolution, or forest/land modeling. The paper aim could be modified to more carefully reflect what the analysis is able to accomplish.

In addition, I have two points about methodology that were not clear to me:
i. Were observer points offset from the ground elevation or the surface model elevation? That is, if an observation point was in a forest, would the observer be placed 1.8 meters above the ground or above the (25m) canopy surface?

ii. Explain the manner in which spatial differences between viewsheds were measured and then tested (line 154-155)

The knowledge gap the paper fills is real, and the paper is able to make a contribution.
Validity of the findings: This data-heavy paper uses appropriate methods and the findings are solid. Given the importance of accuracy, it would be helpful to discuss the accuracy of the vectorized forests and buildings layers - presumably errors in these features could contribute to the big differences in viewshed visible area identified in the paper.

Conclusions follow logically and are connected to parallel findings in the literature. The rationale for why viewsheds are overestimated so much by the non-lidar DSM is not a strong point, though. More discussion on 'why', even if it's speculation, would improve the paper.
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: INTOLERANCE OF UNCERTAINTY AND CONDITIONED PLACE PREFERENCE IN OPIOID ADDICTION
Review round: 1
Reviewer: 1

Output:
Basic reporting: Basically well done.  Some comments are provided in the feedback below
Experimental design: Basically fine. Some clarifications on the statistics and data computation are needed
Validity of the findings: Some discussion as to the validity of the model are needed
Additional comments: The paper by Radell et al is well-written and attempts to adopt a preclinical paradigm to the study of personality variables in substance use disorder. In general the paper is well laid out and well presented.  Some points of clarification are below.
My main comment is on the use of this novel paradigm in humans.  Although it is interesting to adapt a preclinical model for study in humans, further discussion of the parallels between the preclinical model and human model is needed.  Further, some discussion of the validity of this model is needed.  For example, in the current model, the final phase involves exploration of the two rooms with a reward contingency in place. In the animal model, the final exploration phase is in the absence of any reward.  This is important because the authors talk about ‘preference’, but is it really a preference if a reward is available? What are some of the strengths and weaknesses of the differences between the preclinical and clinical model?
In the Methods section it would be helpful if the authors could provide a section describing the statistical analyses, with a rationale for the statistics chosen. This is important because the statistics were different for different parts of the study.  Is it not possible to analyze all the data with ANOVAs? In this section it is also necessary to describe the computation of all variables, such as in the final phase. What exactly was a ‘higher score’ (e.g. line 266) and how was this computed? Why did the authors analyze the tendency to switch between rooms, and how was this computed?
Throughout the paper the authors describe the patients as ‘addicted’.  Would it not be more accurate to simply state that they have opiate use disorder (OUD)? (or substance use disorder (SUD)?)
1)	Line 44: Please define a motivational hierarchy
2)	Line 57: a citation is needed
3)	The paragraph on line 72 beginning: ‘IU has also been associated…’. Is this paragraph necessary?
4)	Paragraph on line 82: Is there evidence for changes in reward sensitivity from non-imaging data?  That would seem more relevant to the present discussion, would it not?
5)	Line 183: ‘Questionnaires’ should read ‘Demographics and Personality Variables’ to match the header on the Table
6)	Line 196: there should be some mention as to what high IUS scores mean, so the reader can follow along easier with this logic.
7)	line 315: why does this behavior decrease from pre-training to post-training? Some interpretation is warranted. Also, why was this analysis done?  There is no rationale in the Methods
8)	Line 382: A citation is needed.
9)	Figures: Error bars should be included for all figures. Statistics should also be presented in the figure captions, with symbols on the figures representing the results of pairwise comparisons.
10)	Fig 2A: Is the difference between the groups in the poor room significant? They look to be.
11)	Fig 3A figure caption: Mention of IU is made, but there is nothing about IU in the figure.