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: FALSE MEMORIES WHEN VIEWING OVERLAPPING SCENES
Review round: 1
Reviewer: 1

Output:
Basic reporting: Overall, this paper addresses an interesting question using a clever design. In particular, I commend the authors on designing this paradigm using unseen parts of old scenes, as I think this will be a useful paradigm for the field. Although I know that interest is not relevant for meeting the journal criteria, I do want to add that both the finding of high false alarms to unseen regions, and the finding that central regions of the original scenes were preferentially fixated even when they were not the center of the presented images, are very interesting and answer important questions.

My biggest concern is that the clarity of the manuscript needs to be improved throughout, as the paper is somewhat difficult to read in its current form.

First, different terms are used in different places to refer to the same concept (e.g., “study part” and “study phase”; “cut” and “crop"; scene “parts” versus “patches”), which makes it harder to extract the main points.

There are also more subtle instances, for example “We found that fixations were biased towards the center of the original larger photograph and that this bias was repeated during the second presentation in both identical and overlapping views.” The first presentation is never mentioned, so the reader has to infer from the end of the sentence that the first half of the sentence was referring to the first presentation. Solving these types of issues would result in a paper that is substantially easier to read.

Furthermore, the manuscript would benefit from careful editing for English usage, in both syntax and nonstandard word choices. For example of the latter, “panoramatic” is used rather than the term used by the panoramic study being discussed, “stimuli” is used as singular and plural in different places, and “cut” is used instead of “cropped” in most places.

My impression is that the authors provided generally sufficient background information. My only specific suggestion with respect to citations is to discuss Valuch, Becker, & Ansorge (2013), as their paper uses a very similar method.

The composition of the introduction and discussion could be improved. In particular, I felt that the transitions between points and paragraphs in the introduction often lacked logical flow, and it wasn’t clear to me why some points were being discussed, or what questions the authors were hoping to answer with their study. I would suggest writing a more targeted introduction to focus more on the points that are directly relevant to the present study—that is, what readers need to know to understand why the study was done, what questions it is aimed to answer, and what work others have done that are relevant for this question and methodology.

In the beginning of the discussion, it was not clear why Andermane and Bowers (2015) was discussed in such detail, particularly with respect to their delays. Was the point to show that other studies have found that memory decreases after a delay?

I found the figures to be excellent. My only suggestion for the figures is to make the points larger in figures 4 and 5, as they are very small currently.
Experimental design: The analytic approach seemed to be excellent based on the description in the method, but I feel it was not consistently well executed or described in the results. For the most part, the design was well thought out, with my only major hesitation being the memorability estimation (see section 3).

Furthermore, as in the rest of the manuscript, I strongly recommend the authors improve the clarity of writing in the method and results section.

Some of the areas that lack clarity do so in a way that hinders the ability to understand the method and analyses, for example:
1.	“The model contained two random factors (intercepts for participants and images), one fixed factor (patch type) and the response (correct yes/no) as dependent variables.” It is unclear in this case which variable is the outcome measure.
2.	“Vigilance patches” is used only once in the manuscript (in the results), and it is not clear what it means.

I think that using “central,” “lateral” and “contra-lateral” in place of “identical, overlapping, and novel” introduces unnecessary confusion that makes things harder for the reader. I realize this was likely done because the significant result pertained to fixations being central, but this can be stated in a more efficient way without the need for new terms.

Lastly, please clarify the Experiment 3 statement that “We did not limit dwell times to the patch areas, because their content could be arbitrary and people might better investigate their surrounding context.”
Validity of the findings: My most serious concerns pertain to the results sections; in particular, the lack of statistics to support conclusions that are drawn. I recommend that statistics be provided, or the conclusions be removed. Some instances:
1.	The main conclusion from Experiment 3 (e.g., “these results indicate a strong bias for the central patches“ and “The main finding from the eye-tracking experiment was preference for the central part of the original image”) does not appear to be supported by any statistical tests. It seems that the authors only provide means and standard deviations for this data. This is particularly concerning given that the discussion states that “the results are near the threshold level for significance”
2.	The authors used generalized linear mixed effects models with model comparison, but in some places, only presented the results of the comparisons, without providing the significance or direction of the independent variables (e.g., in the Fixation duration and saccade amplitude section of Exp 3, it is stated that adding trial type improved the model fit, but it is not stated which direction these effects occur or what conclusion we can draw from them).
3.	It is stated in the Exp 3 discussion that “the average duration of the second fixation was slightly longer”, however, this is not mentioned in the results or supported by statistics.
4.	In the general discussion, line 551, it is stated that “Patches with high false alarm rates either contained textures similar to seen parts or contained objects that were also present in the presented part”, however, this does not seem to be supported by any data.
5.	In the final conclusions section, it is stated that “they are highly prone to false alarm errors in distractors closely matching the style of the original stimulus,” however, it does not seem like that claim is supported, as distractors were looked at as a single entity, not analyzed by style match.

I would avoid discussing the directions of the nonsignificant effects at such length. For example, in Experiment 2 lines 324-331, only the first two nonsignificant correlations are explicitly referred to as such, whereas the rest of the nonsignificant correlations are referred to as if they were significant effects (“correlation was slightly negative”). I am concerned that this may mislead readers who are skimming and not reading the statistics, or more importantly, the general public who may read this paper without a knowledge of statistics.

It seems like there is an implicit assumption in the paper that neural nets are a good proxy for memorability, but they are a rough estimate of memorability at best (i.e., a correlation of .64). In particular, it is not known how well those neural networks estimate memorability in the present subset of stimuli. Because memorability was not directly assessed in this study, I highly recommend that the authors greatly temper their conclusions with respect to the null memorability correlations, and change all uses of “memorability” to “model-estimated memorability.” This issue is particularly concerning in the abstract, where it is not mentioned that the memorability measure is not actually memorability.
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: FALSE MEMORIES WHEN VIEWING OVERLAPPING SCENES
Review round: 1
Reviewer: 2

Output:
Basic reporting: The article presents important empirical data in clear and professional language. However, there is a significant alternative possible interpretation of a major findings of the study. The "false memory" for lures is not presented well in my opinion. The discussion of the Boundary Extension work is very relevant here and should be included in the Introduction as well as research on scene layout. You may want to consider Gottesman (2011), which I think is particularly relevant here, but in any case research on scene layout should be discussed in the introduction.
(Gottesman, C. V. (2011). Mental layout extrapolations prime spatial processing of scenes. Journal of Experimental Psychology: Human Perception and Performance, 37(2), 382–395. https://doi.org/10.1037/a0021434)

There are a few stylistic issues (as well as some lack of clarity in the design and procedure that will be addressed later).
Stylistic issue:
The discussion of Experiments 2 and 3 at the end of the introduction doesn't flow well and interrupt the flow of the paper. I recommend shortening it and making it more relevant given the overall introduction.
Minor points:
-Lines 182-186 are not presenting information in consistent way if it is "old 2- 25 patches from identical trials and 25 from..." should it not be "old 1- 25 patches from... and 25 patches from... and the same for "lure..."?
-Figure 4 's heading doesn't state "Experiment 1"
Experimental design: The overall theoretical frame work and design are good with some significant problems.
Most important, as mentioned above, there is a significant alternative theoretical framework that is mostly ignored in the article yet provides a very important alternate explanations for the results. The authors use "lures" which are patches or parts of the scenes that were not presented to the participant with the expressed purpose of having distractors that are supposedly matched for "content and style". However, there is a strong alternative view to this argument that should be presented upfront. These patches are not just similar images (indeed there is no clear evidence that they are in some way matched for content and style). They are actually parts of the actual scene from which the photographs were taken. Extensive Boundary Extension literature (which is only briefly mentioned in the discussion) suggest that people understand photographs of scenes (as well as drawings, and real physical partial views through apertures) as parts of bigger scenes. These patches are not just similar in gist or style, they are parts of the same scenes presented. In addition to the same textures and gist they also show parts of the layout of the views presented. The importance of layout, in particular, is ignored for the most part in the article and yet it is arguably a significant part of scene representation. Gottesman (2011) for example, showed that partial views of scenes primed distance judgments in areas of the scene that were not visible in the prime view. The results obtained in this study are strongly consistent with this view, particularly the strong FA rate for lures. There are other weaker indications like the tendency to focus on the central part of the scene (in Exp3), as if people can predict where the center is and therefore arguably, have some idea (though obviously not a perfect one) of what the "unavailable" parts show.
Thus, the FA for the lure can arguable be evidence for much more than just memory for gist and superficial characteristics, indeed there is no strong indication that it is memory for gist rather than layout or other characteristic specific to that particular scene (though not the view presented originally) .

In this vein, it would be also interesting to see if the FA for lures is stronger in repeated v. non repeated trials (that data should be available).

Design clarification needed:
-It is not clear if the same scenes were used for each of the conditions. Figure 1 seems to suggest it but it isn't actually stated that I could find. If so, is the scene-condition pairing counterbalances across participants? If not, was there any attempt to equate the scenes in the different conditions?
-Was the selection of lower or upper parts of the scene distributed similarly across lure and old conditions? (see line155) This may be important in how much of the scene layout can be understood from the patch.
- The method section doesn't report recording RT (there is mention of it in the results only)
- Line 188 reports that the patches were always presented in the center. I could find a similar statement for the full photographs. I assume it was but, particularly given the discussion in Exp. 3, I recommend stating outright that the full photographs were also presented in the center, if that was so.
-Figure 2 seems to show a patch where the objects are bigger than in the full photograph, if this is incorrect, please fix the figure, if not this may be a problem, please explain in the text.
- The conceptual significance of bias in the SDT analysis should be explained more. Was a difference expected? what would it mean?
- Line 311- Introduces the terms "vigilance patches" v. "test patches" without defining them.  Is there need for new terminology here? if so define.
Validity of the findings: The results are well analyzed overall. with a few issues that I think should be addressed.
- First, the conclusion that "participants base their decisions only on rough semantic and perceptual similarities" (line 270) is arguable because the lure patches are not just similar, they are parts of the same scenes as the presented images. There is no direct test of similarity that is reported.
-The discussion of correlations (lines 326-332) should be more carefully worded as none of the effects are statistically significant.

Smaller issues:
-line 204- not clear what mean is referred to- how was it calculated? (right section memorability - left. for each picture, averaged across pictures?)
-I would like to see descriptions of the trends in the figures in the text itself (missing for several of the figures. e.g. line 314 refers just to "differences";  what differences were observed?)
-Figure 7 is particularly confusing, I was not clear what you were trying to demonstrate in it, and it wasn't very effective.
Additional comments: I think this research is very interesting and it would be more effective if you re-frame it to emphasize more of what you did find rather then what you didn't, particularly with respect to your results for lures. I am torn between classifying this as minor or major revisions. I think the procedure and analysis were probably fine even in the areas that were not clear in the manuscript but just in case my inferences were incorrect I would like to see it spelled out.


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

Input:
Title: FALSE MEMORIES WHEN VIEWING OVERLAPPING SCENES
Review round: 2
Reviewer: 1

Output:
Basic reporting: I think the manuscript is greatly improved.  Additional research and possible theoretical viewpoints are presented and the terminology used is much clearer. For the most part, the terminology is more sensitive to the distinction between discussing truly different scenes (e.g., Bar v. mountain stream) and discussing unseen parts of previously viewed scene (e.g., the right part of the bar compared to the left part of the same bar). The use of “Image, versus image part” works well here but there are a couple of places where the use of the term scene is still confusing.
This is a difficult issue to define: What is a “scene”?  What do you mean by it? Is the scene just what was shown in the picture or is it the environment that was photographed? I can take two pictures of my kitchen showing different parts of it; are they two pictures of the same scene (possibility 1)? If not, are they different scenes in the same way as one of these pictures would be different compared to a picture taken in my friends’ kitchen (possibility 2), even if we had very similar furniture and fixtures? I want to clarify that this is where I think the significance of the BE work really lies.  It is not in the actually boundary memory error, which as you say is not necessarily relevant here., but in the possibility that BE is evidence for the viewer’s greater understanding of the actual scene, beyond what is presented (as in possibility 1). The viewer obviously knows they didn’t see the whole scene but when trying to place the boundaries accurately (as in the BE paradigms) or when trying to judge if they’ve seen a patch of a scene (in your paradigm), both different but somewhat challenging tasks, they are revealing their access to a greater representation of the scene, than was visible in the view presented in the photograph. I believe that is the relevance to your findings.
Whether you agree with this argument or not, it would be less confusing if you didn’t use “scene” as synonymous with “the photograph of the scene”, this happened rarely in this version but it still does. Here are a couple of placed where I found this:
74: “The usage of overlapping stimuli allows us to study repeated exposure and
measure how individual scenes are integrated into coherent memory.”
The words “Individual scenes” suggest to me different scenes, like the kitchen and the hallway. Consistent with the rest of your discussion, I think you are really saying something like
 “individual scene parts”

110: “We were interested in whether the repeated presentation of the whole scene
111 would lead to increased recognition of smaller parts similarly due to repeated exposure of the
112 whole stimuli (Konkle et al., 2010).”
First, as discussed above if you are taking the “possibility 1” definition of scene, you are not presenting the whole scene but the “the whole photograph” or “the whole stimulus”.  Photographs rarely, if ever, show a whole scene.
Moreover, can this sentence be broken up? Do you even need the second part after “due”? It seems repetitive to me.

This is my main concern for clarity. Beyond this, there are several small clarity issues, particularly in the introduction.  I will discuss them in Additional Comments as I believe they are mainly typographical in nature, though I may be wrong in places where I was confused.
Experimental design: The experimental design description was greatly clarified compared to version 1 and reveal solid experimental design. Difficulties and imperfections were addressed adequately.
Validity of the findings: Many complex cumbersome sections and sentences have been un-packaged compared to Version 1, and valuable clarifications were added. For the most part, the results are interesting and alternative possible explanations are offered.

There is just one point that I found difficult to fit with the rest of the work. I am not sure if it’s an error of expression or is attempting to make a point that is not coming across.  In Experiment 2 you said:

302 Experiment 1 showed that participants were unable to easily recognize small areas from the
303 presented stimuli.

I think this is a pretty unconvincing statement. I guess this comes down to what how you define "easy" I would argue that 73% accuracy for old patches is not negligible. You contradict this statement in line 548 yourself. If you want to make this argument here you should qualify it better.
Additional comments: I think what I have below are all minor issues but they need to be addressed to make the manuscript clearer. I am listing the parts I stumbled on; I do not want to rewrite your manuscript but I put some suggestions of my own, just to illustrate what I feel the difficulty is. Of course, I may have missed the point in some of these places, as I was confused by them, so my suggestions may not work, but I hope they will help you to understand my confusion.

Abstract
25 were observed. In Experiment 2 (N=28), neither the recognition accuracy for an image part nor
26 the tendency for false alarms correlated with the memorability of the corresponding larger image
27 estimated by pretrained deep neural network. Finally, in Experiment 3 (N=21), we repeated the

I recommend breaking up this sentence. Something like “In Experiment 2 (N=28), the memorability of the larger image was estimated by a pretrained deep neural network. Neither the recognition accuracy for an image part nor the tendency for false alarms correlated with the memorability”’

Introduction:
40 : a large number of stimuli are presented

“A large number is presented”, or “large numbers are presented”

116 Experiment 2, we focused on the consistency of correctly responding to whether the recognition
117 accuracy is explained by the properties of individual images, namely, their memorability.

This sentence is not clear. Is the “consistency of correctly responding to” not the same as recognition accuracy? Is it not enough to just say “we focused on whether the recognition
accuracy is explained by the properties of individual images, namely, their memorability.” What am I missing?

197 shown), while verbal cues were provided below each image to reduce the effect of response
198 mistakes.

“Verbal cues” can mean different things. What does it here? If it’s something like “press left for ‘patch was shown’ press right for ‘patch was not shown’” I recommend putting it under that patch in Figure 2 as it would have appeared on the participant’s screen, or clarify in a different way.

226 patches (or in hits between old-1 and old-2)

Why is this statement in parentheses? Is seems very important in itself.

241 to avoid perfect performance (which we observed in three participants)
Last part of this sentence is stated twice.

242 Macmillan & Creelman (2004). Changes in d’/bias were measured using a paired t-test. The
243 theoretical meaning of the expected decrease in sensitivity between immediate and delayed
244 recognition corresponds to decreased memory capabilities over time. On the other hand,
245 theoretical changes in bias would represent changes in response pattern; in particular, lower
246 bias values correspond to more false alarm responses.

I asked you for the theoretical meaning here, so I like this clarification but you don’t need the actual words “theoretical meaning”. They make the sentences cumbersome.  “the expected decrease in sensitivity between immediate and delayed recognition would corresponds to decreased memory capabilities over time…. etc,” will work better.

Experiment 2

312 color (Isola, et al., 2011) or spatial frequency (Bainbridge, Dilks, & Oliva, 2017). Additionally,
313 memorability has been defined not only as correct recognition but also as a false alarm rate

What false alarm rate? low? high?

Experiment 3

456 To make our results more salient, we will denote the
457 thirds of the original image as lateral (left third), central, and contralateral (right third) to make
458 our results more salient.

Repeated phrase.

Figure 1 caption:
one too many “about” in “we asked about either about patches…”


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: FALSE MEMORIES WHEN VIEWING OVERLAPPING SCENES
Review round: 3
Reviewer: 1

Output:
Basic reporting: The manuscript successfully addressed the concerns raised by prior reviews. The language and terminology are clear.  The impetus for the study is convincing and enough context is provided.
Experimental design: The design and procedure have be successfully clarified.
typographical error: There is an extra word "about" in the heading of Figure 1
"In the recognition phase, we asked [about] either about..." remove []
Validity of the findings: The results are interesting and compelling. There are several significant effects and the nulls effects are also interesting in themselves. The power needed for the null results to achieve significance is not reported but the authors make a compelling argument that the effects are so small as to make achieving significance very unlikely.
The conclusions are warranted from the results.
Typographical error: Line 578 the word "this" repeated twice at the end.
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: EARLY PLEISTOCENE LARGE MAMMALS FROM MAKA’AMITALU, HADAR, LOWER AWASH VALLEY, ETHIOPIA
Review round: 1
Reviewer: 1

Output:
Basic reporting: I’d like to commend the authors for providing an overall well-written, grounded and sober analysis of the Maka’amitalu faunas. Relative to some trends in the recent literature, I appreciate the efforts made by the authors to provide primary descriptions and grounded systematic palaeontology within the context of a peer-reviewed submission instead of an emphasis on offering just a ‘species table’ or sole emphasis on interpretation over primary data on the fossil materials.
Most of my comments are brief and, in most cases, merely reflect stylistic considerations that the authors can elect to accept/reject. A few more substantive comments do crop up, and I hope the authors will consider expanding a bit of the manuscript to address them.
Minor Comments
Lines 57-59: The authors use terms like ‘medium’, ‘large’ and ‘megaherbivore’ within the abstract that don’t really come up much within the remainder of the document (megaherbivore, for example) and aren’t grounded by a definition as to what designates these categories. Body size is integrated into the faunal analyses but follows a more discrete system. I appreciate the authors are trying to delineate their consideration of ‘macromammals’ vs. ‘micromammals’, but absent some sort of criterion I just assume… the taxa described are the ones collected and there isn’t a collection of collected but undescribed materials?

Line 78: ‘witnessed’ is a bit awkward
Line 84: ‘formations’ vs. ‘Formations’ – given that later and in most broad use a singular Formation (e.g., Shungura Formation) is capitalised, would capitalising this be appropriate? The use here is in a list of named ‘formations’ rather than use of the term generally.
Lines 100-104: Might consider reordering the sentence structure. I don’t know that the taxonomic turnover and palaeoecological analyses of faunal change come ‘from’ the systematic description as currently phrased.

Line 145 (and across manuscript): ‘orders’ vs. ‘Orders’ as a formal Linnean rank
Line 286: ‘Younger in age is Syncerus acoelotus…’ is a bit of an awkward word ordering to my ear.
Line 308 (and across manuscript): The use of ‘pedicel’ vs. ‘pedicle’ – I’m just flagging that the use of the former in the manuscript somewhat falls in the less common occurrence in the literature than the latter.
Line 395: Overall the authors are great with their anatomical nomenclature, and I appreciate the challenges of describing horn core shapes/orientations; ‘backwards’ somewhat stands out as a result, but may be unavoidable.
Line 656: In this circumstance I appreciate the authors are wanting to signal a potential allocation here, though equally one could argue that the ambiguity in the ability to attribute these specimens to either genus could push towards ‘Reduncini gen. et sp. indet’ with notes on the potential allocation.

Line 690: Given the defined use of dental nomenclature, ‘lower p4’ seems redundant (and only seems to arise here).

Lines 712-759: I appreciate the challenges of wrangling multiple, taxon-focused contributors into a single voice within a manuscript. That said, the section on the hippo remains stands out as being quite stylistically different and with a number of awkward sentence structures/grammatical choices. I would suggest a hand in editing to eliminate some unnecessary commas (across section) and run on sentences (e.g., 729-733).
Experimental design: Geological Setting Section (pre- Line 135): I would appreciate some bridging paragraph or sentence(s) to clarify whether all the ~40m of Busidima formations are exposed within the limited Maka’amitalu area that was sampled. The overall description of the geological setting is comprehensive, just lost within this is whether all these described tuffs and sequences are potentially represented within the sampling area. This speaks to an additional question, which is whether the authors could expand a bit on the nature of the potential time averaging and the internal integrity of the ‘assemblage’. When moving forward with ecological and turnover analyses there is the underlying assumption of association, but how reasonable that assumption is comes from how confident the associations are between samples (or at least tempered with known sources of distortion in the sample). As the authors note, it’s a relatively small faunal sample to start with and from surface exposures… so a bit of unpacking around what makes this a discrete sample to analyse would help with later discussion/interpretations (e.g., abundance data and cross-site comparisons in lines 1155-onwards).
Validity of the findings: Lines 870-911: Given where the identification of four specimens lands (particularly with biochronological implications that are later discussed in lines 1178-on), I will admit to being let down by the discussion section that simple states that the Maka’amitalu specimens ‘is a better match for M. modestus’ in lieu of a clear basis for attributing the materials as such relative to other metriodiochoerines (e.g., the noted similarities to M. andrewsi). This does not mean that the authors are ultimately incorrect in the attribution, but the entire primary description provided here is more focused on a clear case for the generic attribution… but no specific call outs to provide strong support for the ultimate specific diagnosis. With this attribution later noted as a potential extension of the FAD, I really urge the authors to clarify within the description/discussion of these specimens why they are M. modestus to the exclusion of M. andrewsi beyond the relatively vague statement that it is “similar to M. andrewsi… but we are going with M. modestus”. This is really my only substantive concern in the primary attribution of the remains across the entire manuscript.

Turnover and Paleoecology/Geological Setting (Lines 1114-on): On reaching this section and considering the results of the analysis, I would suggest a bit more information (if possible) on the nature of the depositional settings and whether there is supporting information on the nature of the hydrological setting for the sampled region? In line 1150 we get the statement that there are ‘higher-energy fluvial deposits’ at Maka’amitalu, but does that mean that the entire sequence is fluvial? All high energy? I don’t see this content in the prior geological setting description, and a somewhat clearer description of what is known about the hydrological setting across the set of deposits potentially aggregated in this assemblage would assist a bit in the context of interpreting the local regional palaeoecology.
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: EARLY PLEISTOCENE LARGE MAMMALS FROM MAKA’AMITALU, HADAR, LOWER AWASH VALLEY, ETHIOPIA
Review round: 1
Reviewer: 2

Output:
Basic reporting: This is an excellent contribution to the knowledge of Eastern African hominid environments, written by several of the best specialists of fossil mammals of this period. The presentation and style are clear, the introduction and 'Geological setting' clearly present the context, the length of the paper is neither too short nor too long, the figures are good (minor corrections needed -see below), the raw data are provided (except perhaps for Theropithecus – see below). The paper should definitely be published, with only a few minor changes or improvements.
Experimental design: All requirements (primary research within Aims and scope, research question ell defined, relevant and meaningful, rigorous investigation, details and information provided) are fulfilled, but see 3. Validity of the findings
Validity of the findings: My main concern is about chronology. The authors conclude to an age range of 2.4 – 1.9 Ma but there are several indications that the lower part of this range is unlikely; I suspect that this extension of the range towards early ages has been influenced by the dating of the BKT-3, but this is irrelevant to biochronology.
My arguments are:
- first, the presence of Equus unambiguously points to an age younger than 2.3 Ma
- the authors themselves believe that Hippopotamus cf. gorgops points to an age not older 2 Ma
- the authors' estimate of a gap of almost 0.6 Ma (their Fig. 12A) between Lee Adoyta and Maka'amitalu also suggest that their own age estimate is close to 2 Ma…
- l. 1043-1044, we are told that the Maka'amitalu specimens 'fit best with T. o. oswaldi', and  l. 1187, it is mentioned that the 'best fit' based on T. oswaldi is 2.4 Ma; I am sure that C. Gilbert and S. Frost have good arguments for that, but they should be provided.
- l. 1213 – 1214, the authors correctly observe that 'few species [from the Uraitele exposures] are shared with the Maka'amitalu'. But, since the sites are geographically close, isn't this precisely because the ages are different ? The differences in faunal composition with the nearby MLP sites (even accounting for the possible Kolpochoerus/Metridiochoerus issue) is striking, and points to a significant age difference.
	In my opinion, the authors should either provide biochronological arguments for extending the possible time-range towards older dates, or address the disagreement between the radiometric age and the biochronological data.
Additional comments: Additional, minor comments:
l. 84: capitalize Formations ?
check lines 112-113
l. 168-170: some bovids are small and very likely to be impacted by taphonomic and collection biases
l. 437-438: Beatragus is also known from Ahl al Oughlam, Morocco
l. 450: what is the meaning of 'Parmularius spp. (cf. Damaliscus spp.)' ?
l. 519: 'that is very slender'
l. 521: backward
l. 576 et seq.: on the basis of the photos, it is difficult for me to imagine that this is right horncore, so Parantidorcas can probably be excluded from the comparison.
l. 983: assignment to E. cf. oldowayensis is poorly supported; either provide stronger arguments, or just call it Equus sp.
l. 988-989: I would use 'anterior' and 'posterior' rather than 'dorsal' and 'ventral'
l. 1000: 'L 7-4 from member G'
l. 1083: explain in a few words why this is an m3; please note that Beden (1987, tab. 42) mentions an m3 of E.recki ileretensis whose hypsodonty index is 116. Couldn't the hypsodonty index of your tooth be higher than 129.5 in another, missing part of the crown ? I would not identify your tooth fragment to subspecies.
l. 1154: don't you know what were the sampling procedures ? Since members of the Hadar Research Project are among the authors, they should know whether the hippos were systematically collected or not.
Figures: several of the symbols of XY plots are quite hard to see. Please check.
Fig. 2: since the caption mentions "Hadar Research Project area" it is awkward to plot here localities that are no longer part of this Research Project; either remove them or add a historical note.
Fig. 5. check captions for LMNO (JKLM in the figure)
Fig 7: scales bars are 40 and 10 mm (not cm)
Fig. 12C: this is a personal opinion, but I think this is highly sensitive to incomplete sampling

Reference list
Jablonski & Frost 2010, Vrba 1995 are not mentioned in the text
Szalay & Delson 1979, Gentry 2006 are missing in the ref. list
Boisserie & Gilbert 2008 or 2009 ?
Souron et al. 2013 or 2015 ?
Bengtson, not Bengston
Delson et al., not Delson & Dean
Locke & Rowan 2016, not Locke et al.
Frost 2007a & b in the ref. list
Give full ref. for Geraads et al. 2021


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 LOW-COST BENTHIC INCUBATION CHAMBER FOR IN-SITU COMMUNITY METABOLISM MEASUREMENTS
Review round: 1
Reviewer: 1

Output:
Basic reporting: Language is clear and unambiguous. Professional English is used throughout. Literature references are adequate and up-to-date. Figures and tables are informative and clear. Raw data shared. Article is self-contained and results are relevant to research question.
Experimental design: The research presented is original and within the Aims and Scope of PeerJ. The research question is well defined, relevant and meaningful. It is stated how the research fills an identified gap in methodology. The research is of a high technical and ethical standard. Investigation could have been performed more rigorously, by performing additional analyses. Methods are described with sufficient detail to replicate.
Validity of the findings: All underlying data have been provided. Annotation of headers could be improved to be made more descriptive, and include units. Conclusions are well stated, linked to original research question and mostly supported by results.
Additional comments: The paper by Mallon and coauthors presents a benthic incubation chamber for measurement of community metabolism. While many chamber designs exist, this chamber design is different because it is based on materials that are low-cost and are easy to source. The authors test the design in the laboratory and in the field through performing incubations on sediments, seagrasses, and coral reefs.
Overall, I appreciate the effort to make such a technology more accessible. The paper itself is well-written, and figures are for the large part clear and relevant. The flux dataset seems to be of a high quality. Please find my main comments to the paper as well as detailed comments below.
Main comments
1.	Description of chamber performance: The authors do a good job describing light attenuation inside the chamber bags. There are two points that could be improved:
a.	Description of mixing inside the chamber: I appreciate that bags allow some water movement inside the chamber and this is superior to having a Plexiglas chamber with no stirring. However, I suspect that gradients will build up inside the bags, so the resolved flux will be dependent upon the location of the valve. This is my main concern with the design of the chamber, and it is unfortunate that the authors do not quantify this directly. Perhaps the authors can expand on this point, based on previously published work using similar bags? Similarly, one concern I have with applying chambers in highly productive habitats is the build-up of supersaturated or hypoxic conditions during light and dark incubations. Since no data are presented on this, I am curious to know the highest and lowest O2 values observed inside the chamber, and how this compares to what can be expected for these habitats to experience naturally?
b.	Leakage tests were not performed under field conditions. There are straightforward ways to assess leakage, which the authors describe, but this was not done. I do not think that the laboratory conditions tested are representative of many of the habitats studied. If the authors could perform a field test, then this will improve design validation.
2.	The premise of the paper seems to be low-cost and accessible technologies. I agree that this is the case with the chamber itself. However, the 3D modelling used to reconstruct benthic surfaces to calculate reef surface area and volume is far from trivial, and requires specialized expertise, software, and high-performance computers. Since these measurements are used to normalize metabolic rates, it seems that it is hard to argue that this is overall a low-cost and accessible method. I must say that I fully appreciate the advantages of photogrammetry and what this brings to metabolic studies, but I hope the authors are able to see these conflicting points. In principle, you could normalize to reef planar surface area and still obtain a flux, although this will of course not be as informative. I believe the text should be adjusted to better represent this.

Detailed comments
L23: I do not think that chambers are non-invasive. There are true non-invasive methods out there such as eddy covariance and gradient methods.
L38: Sequestration. Replace with ‘cycling’. Sequestration refers to organic matter buried deep in sediments, which is not the focus of the study.
L46: Again here, focus on cycling rather than sequestration.
L48: One can calculate more than the NCP from O2 flux measurements: photosynthesis (gross and net), respiration, and the balance between the two (NCP).
L51: ‘autonomous sensing’. I suggest replacing this with ‘benthic boundary layer approaches’
L52: Berg et al. 2019. A better reference is Berg et al. (2022) Aquatic Eddy Covariance: The Method and Its Contributions to Defining Oxygen and Carbon Fluxes in Marine Environments. Annual Review of Marine Science.
L52: ‘Flow respirometry’. I suggest replacing this with ‘Eulerian approaches’.
L56: I don't think that chambers can be easily deployed on rocky surfaces such as corals. I suggest rewording to say 'have been deployed'.
L105: Again here, I question whether chambers are non-invasive.
L138: Replace ‘course’ with ‘coarse’
L138: Was there any flow inside the aquarium, as you’d expect to find in situ?
L175: Was this done in the field or lab?
L185: I think ‘join’ should be ‘joint’
L198: How was this deduced?
L201: Did individual deployments last four days?
L203: What is CCA?
L208: How did you convert from volume or surface area to biomass?
L218-219: Wasn’t this done using the 100 ml syringes, as described in L174-176?
L251: You should specify that this was done in the lab.
L260-261: It really depends how significance was tested. I find it hard to believe that there was no significant difference during the high light periods. The take home message is that there is some light attenuation, not that there isn't any.
L263: It is not clear to me why you performed this test. Is it because you thought that water inside the chamber might heat up relative to the outside? What are the reasons/mechanisms for this? It would be useful to include a sentence in the intro or methods about why this may be important.
L270: It would be useful to know how much O2 increased/decreased during the incubation. One of the drawbacks of chambers is that O2 can become strongly supersaturated or turn hypoxic, which would influence metabolic processes.
L284-287: This should be in the methods section.
L303: Here too. Chambers are not non-invasive.
L313-314: The chambers are low-cost, but the overall approach requires specialist expertise, software, and computational power.
L328: I agree that the chambers can be deployed by non-experts, but the data processing presented herein, particularly related to 3D models of benthic communities is far from trivial. I think this needs to be represented a bit better.
L352: Placing a chamber onto organisms is always going to be invasive. For instance, the rubber tubing base on the seafloor will curb the supply of oxygen to the sediments, which if left for long enough will turn the surface sediments beneath the tube anoxic. I can imagine that the base will move around some in a swell or current too, causing abrasion. So the chambers likely have some impact, albeit small.
L357: ’without causing damage’. Again here, perhaps say ‘incurring minimal damage’
L360: effective for accurate measurement. It should be stated that this was done under laboratory conditions.
L369: I highly doubt the bags maintain natural water movement. How do you know this is the case?
L372-373: Again here, you did not test it, so you do not know this is the case.
L373: I do not see how this was demonstrated in the paper by Camp et al. 2015. Can you expand?
L376-384: This paragraph is mostly a repetition. Can be greatly reduced or removed.
L388: Did you measure seagrass shoot densities? The Duarte paper is a global compilation, it would be more interesting to compare like with like.
L391-394: If I understood this correctly, you are comparing NCP at solar noon with average daily NCP. It is not the same thing.
L408: In what way/s are they in agreement?
L412-413: More eutrophic sites might have higher rates of O2 consumption at nighttime. Was this the case?
Figure 2: Panel labels missing
Figure 3 and Figure 4: to my understanding, they contain the same data, so I suggest keeping one of them (I personally prefer Fig. 4).
Figure 7: x-Axis label should be µmol m-2 s-1


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

Input:
Title: A LOW-COST BENTHIC INCUBATION CHAMBER FOR IN-SITU COMMUNITY METABOLISM MEASUREMENTS
Review round: 1
Reviewer: 2

Output:
Basic reporting: General comments:

This paper by Mallon et al. provides a new design for controlled studies of the benthic communities. In general, the proposed method in this paper can be used by many scientists and citizen-scientists to record flux values in locations with poor access to advanced methods and materials. Thus, I believe this proposed design can be very useful in special circumstances.
Light, waves, flow, and temperature are 4 factors that can significantly impact the benthic fluxes. Benthic enclosure methods in general interfere with these factors and thus these methods are usually called invasive or intrusive methods. The proposed method in this paper is therefore not excluded from these limitations. Considering the purpose of the paper that is to provide an accessible method for circumstances with limited resources, these limitations can be acceptable.
Flow can be recreated in a category of benthic chambers using stirring mechanisms. Including flow is fundamentally crucial for measuring benthic fluxes over many benthic communities such as permeable sediments. Mallon et al. paper does not provide information about these types of chambers (please see: Benthic metabolism and degradation of natural particulate organic matter in carbonate and silicate reef sands of the northern Red Sea by Huettel et al.). I think it is crucial for the reader to be aware of current state of technology before proposing a simplified version.
The language of the manuscript is clear, and the text is relatively cohesive with a good flow. There are a few suggestions in this regard that will follow.
In conclusion, this paper is a useful paper that tries to provide the scientific community with a handy solution where other more precise technologies are not accessible. I will include a few recommendations that can improve the accuracy of statements and the quality of the paper.

Specific comments to the authors:

table 1 please include benthic chamber design that I mentioned.
table 4 please clarify what the significance is describing. Various statistical test has different meanings.
table 5 you may transform this table to a very clear plot. Readers are mostly visual, and plots are better in general.
figure 2 the unit for light is umol photons m-2 s-1 please fix it here and on the plots. Why do you report transmission? please report the date of measurements on each graph of the panel b or in the caption.
figure 3 the unit in the caption does not match the unit on the graph. Usually, researchers report day and night NCP. I understand that you wanted to make 1.5h measurement times, but please change this plot to daytime and nighttime NCP.
figure 4 As you correctly mention in your other plot of Fig. 7 PAR-NCP should follow a nonlinear relationship. The reason for this linear relationship might be insufficient data-points. I recommend you to explain this in the text. Usually in these plots only the daytime data is reported, please remove the night data from the plot.
figure 7 This hyperbolic tangent function is called Michaelis–Menten function that explains productivity change with PAR. Please rephrase the caption and add the Michaelis–Menten regression equations on this plot. It is well possible to have negative fluxes during the daytime, but I think you included night data in this plot which must be excluded.

Line 22: Please change specialist equipment to specialized equipment here, and in other places.
Line 23: Please change non-invasive to another term as it usually refers to not interfering with natural conditions.
Line 51: autonomous sensing is not a common phrase used in the field. These are true noninvasive methods that does not interfere with light flow or hydrodynamic that are either boundary layer methods or eddy covariance methods. These measure metabolism of a large surface area. Please distinguish these in the text and cite a few papers for each of them
Line 52: I think flow respirometry is not usually used in the field for benthic flux measurements.
Line 53: please provide a few examples and citations for enclosed incubation methods.
Line 59: standard benthic chamber might have different designs for different purposes. You should look at the paper that I mentioned in my general comments to see what benthic chambers are referred to when studying metabolism of sediments.
Experimental design: Line 111: please explain the benthic ecosystem, fauna, and flora in your deployment site. Please report the deployment dates.
Line 122: Your experimental design does not accommodate mixing which is understandable with your goal of building an inexpensive and handy incubation method. Please explain this here or in the discussion.
Line 212: the metric unit for distance is meter please change the cm to m.
Line 215: In many benthic situations pumping action by waves and tides may change the volume of these flexible chambers. Please explain if you considered this in your calculations.
Line 227: please change the unit of PAR to the correct one.
Validity of the findings: This is very appropriate and useful to report two different cases for testing this method. Unfortunately authors did not compare the results of their methods with other available methods in the field, which is understandable because methods such as traditional benthic chambers or eddy covariance method might not have been accessible for the authors.

Line 368: Any enclosure flexible or rigid obstructs the flow. The flexibility might help but because pumping action and circulation is not guaranteed there is always a need for water circulation in the chamber. In permeable sediments flow impacts the fluxes that I doubt your design accommodates this efficient circulation. For this reason, your design is not considered a noninvasive design. You did not support your claim that the flexibility of the enclosure provides efficient circulation with sufficient evidence.
Line 399: there is a possibility that you did not have enough data point to fit on the Michaelis–Menten equation. I think you should rephrase the hyperbolic tangent equations to the Michaelis–Menten.
Line 419: I think your design is very practical but not very novel.
Line 423 and 425: As I understood you are trying to simplify an expensive method to make it available for special circumstances. Of course, always there are needs for further studies, but the benthic chambers are rather an older method for benthic flux measurements and an established technology. I suggest you rephrase the intention of your research here.
Additional comments: Thank you to the authors for their effort in providing an inexpensive method that helps increase the availability of benthic flux measurement methods.


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 LOW-COST BENTHIC INCUBATION CHAMBER FOR IN-SITU COMMUNITY METABOLISM MEASUREMENTS
Review round: 1
Reviewer: 3

Output:
Basic reporting: The article is written in professional style throughout.
Literature references are sufficient and context is provided.
Experimental design: Methods (i.e., chamber construction and application) are not sufficiently described to replicate experiments. Please provide additional information. See comments below for details.
Validity of the findings: Conclusions are often rather broad and limitations of the work is not well discussed. See comments below for details.
Additional comments: The study presents a low-cost approach to measure benthic community metabolism in situ. Although neither the method nor the topics the paper touches are exceedingly novel, I believe that the creative idea may benefit coastal ecosystem studies where resources are limited. The authors present sufficient evidence for the method's functionality and explain well how to replicate measurements. I am optimistic that the approach will benefit coastal ecosystem studies where resources are limited. I only have a few comments to improve clarity and encourage scientific discussion.

1)	Chamber construction and deployment description are incomplete in many instances. Please refer to line-by-line comments for specific sections. Make sure that the reader can replicate your procedures.
2)	I suggest adding two sections to the discussion. First, please discuss the limitations of your work and the use of chambers in general. They are not the perfect methods for all types of applications. Second, please discuss how your chamber can be used for various applications and measurements. Here, you can add even more value to your work. Oxygen fluxes are interesting and show very well the functionality of the chamber. However, other measurements (e.g., nutrients, carbonate chemistry) etc. may be performed too, increasing the chambers' application range. On the other hand, some measurements may not be suitable for this type of chamber material (e.g., DOC measurements that are sensitive to organic carbon contamination by various types of plastic). Guiding the reader through the application ranges will improve the strength of your study.

Line-by-line comments:

18 – 20: Benthic incubations are "invasive", enclosing organisms from the surrounding water. I would specify the environmental variables here: i.e., temperature and light. On top, I suggest highlighting the most critical benefit of in-situ incubations: Using natural communities with all associated organisms rather than simplified, reconstructed communities used in ex-situ laboratory measurements.

23: Non-invasive only in the sense that you keep the incubated community intact. Nevertheless, the organisms are enclosed from their surroundings, critically changing the exchange of solubles with the surrounding water.

30: Patches of reef comprised of coral, algae and sand? Or did you measure all three types of substrates?

33: Please finish the abstract with a section including the primary take-home message, the additional findings of importance and a perspective on how your work will benefit others.

51: I would refer to autonomous sensing as Aquatic Eddy Covariance.

54: The argumentation here on why you tried to improve incubation approaches is weak. What are the benefits over the other methods? (e.g., other variables than O2 fluxes can be measured by discrete sampling, something that is not possible with AEC). Benthic incubations also have many limitations over the other approaches. I suggest being open with this throughout the manuscript and having a specific section on the "limitations" of this approach in the discussion.

63: Inserted where? Unclear here.

101: I would outline here or elsewhere in the introduction what size your chambers are able to cover and why this is a "good" choice. What is the issue with smaller or larger chambers?

104: You may want to add what this chamber is suitable of measuring.

122: I suggest adding the materials to the listing, otherwise the materials in the following lines (125 – 126) are without context to where they belong to.

125: What was the shape and size of the plastic bags?

129: I miss a more detailed description on how the chambers are put together. These details will help the reader to reproduce your design.

133: You use many synonyms for your plastic bag "water-tight enclosure" (l 122), "transparent polyethylene" (l 125), "plastic membrane" (l 133), "polyethylene tent" (l 343)… I suggest introducing a definition once and using one term throughout the manuscript to avoid confusion.

135 – 137: This is a non-quantitative approach without any scientific meaning.

140: On what substrate was the chamber placed? If only on the bottom of the tank, how can you be sure the sealing works in other environments, too?

145: I like the approach using salinity differences. Great idea!

159: Incubations ran for 4 days? Please clarify.

174: How were the chambers flushed? Lifting the base from the sediment causes disturbance through stirred up sediment.

174 – 176: How was the water volume within the chamber assessed? This does not become clear from this section but is crucial for correct estimates of water chemistry changes.

207 – 208: How did you calculate biomass of corals and algae from surface area and volume? The surface area depends strongly on your resolution of the raster of the 3D model; i.e., higher resolution = larger surface area. Volume calculations are only marginally affected by this.

211: How were incubations "initiated"? There is evidence that oxygen fluxes exhibit a lag after closing incubation chambers, especially during dark incubations (i.e., oxygen is increasing for a few minutes before respiration dominates). Did you consider using oxygen sensors inside the chambers rather than making start-end measurements? What would be the dis/advantages?

217: How was the volume within the chamber assessed exactly?

217: Did you use the 3D surface area of the incubated community or the planar reef area of the incubated reef patch? The difference in the outcome is detrimental for interpreting your results.

250: How did you assure that no sediments were stirred-up?

256: Please provide calculations/results of the water exchange rather than only referring to the change in salinity.

259: You are referring to Fig 2a here. In Fig 2a, I assume the x-axis label is wrong and should be the wavelength? In 2b, the x-axis label is missing and should, likely, be local time?

287: Again, wouldn't it make more sense to normalize fluxes to the planar reef area enclosed by the chambers? All other types of measurements (e.g., larger chambers, eddy covariance etc) are based on the planar surface area.

350: What is the impact of the chosen plastic on UV radiation? Please discuss how this may influence rates of photosynthesis for very shallow waters, where UV may inhibit some photosynthetic processes.

367: Please also discuss how the seal works on rugged, uneven surfaces in this section. There were no tests performed with this regard, weren't there?
375: Very good and important advance to other midsized chambers!!

Figures and Tables:

Figure 1: Please separate the background picture from the other figures to improve clarity. The most important parts of this figure are pictures b) and c) and the schematic d).

Figure 5: Is not mentioned in the text?

Figure 6: Is mentioned in the text after referring to Figure 7. Please rearrange the order

Figure 7: Is referred to in the text before Figure 6.

Figure S1: Is missing?

Figure S2: Is mentioned in the text but I cannot find the file to it. It is also referred to in the text before Fig. S2.

Table 3: What is the surface area referring to? Isn't the enclosed planar surface area around 0.1 m2?


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: DOES SIZE MATTER? AN ANALYSIS OF THE NICHE WIDTH AND VULNERABILITY TO CLIMATE CHANGE OF FOURTEEN SPECIES OF THE GENUS CROTALUS FROM NORTH AMERICA
Review round: 1
Reviewer: 1

Output:
Basic reporting: Generally, your study is interesting, well thought out, and well written, and has been a pleasure to review. It is a complete body of work worthy of publication. I do have some general suggestions for the written aspects of your study which could strengthen your work if clarified.

Line 91-94: ‘Climatic variations’ is a little bit vague, and you could make this statement for most species – could you please be more specific here, and mention some examples of exactly which climatic variables are important for this genus. The second half of this sentence also is a bit vague – when you say ‘precise effects’, are you talking about how climate change might vary these climatic variables? If so, please specify this, and perhaps give examples of how the specific variables (or at least a subset of these) are predicted to change in study region under climate change (this might mean re-writing the following sentence to flow on from this).

Line 120: GBIF is ‘Global Biodiversity Information Facility’

Throughout the manuscript, after the initial introduction in the methods, it would be of greater clarity to the reader to refer to your variables by their full (or abbreviated) name. For example, rather than ‘bio12’, say ‘annual precipitation’ (or even ‘AP’, after first spelling out annual precipitation).

Line 249: Perhaps you could change this reference to the most recent IPCC report?

Line 260-261: How did you define the three levels of vulnerability?

Line 114: Is the presence data you collated from various sources (excluding GBIF) shared?

In general, your writing is clear, however there are some grammatical errors throughout. Some sections, especially the discussion, will need some restructuring, so I have just given some examples of things to look out for:
Line 80-81: Change to …provides a predictive measure about how the habitat suitability…
Line 101: lower case ‘t’ needed after colon. Change order of sentence to ‘…question arises: can the breadth of niche, by itself…’
Line 151: change ‘was’ to ‘were’
Line 246: I’m not sure the wording is right here. Perhaps: ‘…present a relative stable contribution…’. I’m not 100% clear on what you are saying here.

Perhaps as a supplementary figure, could you provide spatial projections of your SDM for each species to complement Figure 1? This would not be essential to publication, however would be beneficial to your overall body of work.
Experimental design: Your general experimental approach is robust and clearly explained. There are some decisions that you have made throughout that need more justification, and there are some approaches to your design that could be amended to produce more robust results. Below, I have outlined some considerations you could take with aspects of your experiment, and also asked for some clarification on some aspects. This may result in you needing to adjust some of your experimental paramaters and re-run analysis.

Presence data: did you take steps to ensure that spatial projections were identical for all data points, and that there were no duplicate records in your data? See Gueta, T., & Carmel, Y. (2016). Quantifying the value of user-level data cleaning for big data: A case study using mammal distribution models. Ecological Informatics, 34, 139-145 for some examples of steps you may want to take in ensuring your presence data is accurate.

Climatic variables: Your methods for detecting collinearity are robust. However, you have not provided biological reasoning for why you included each of the variables you did. You do mention that Maxent performs more poorly under complex and non-complex models. You have included 9 variables here, which is perhaps more than most studies, and in your results you show some variables to have consistently little input to models – perhaps these could be eliminated, and models re-run. I suggest Elith, J., Phillips, S. J., Hastie, T., Dudík, M., Chee, Y. E., & Yates, C. J. (2011). A statistical explanation of MaxEnt for ecologists. Diversity and distributions, 17(1), 43-57 for further reading about how model selection could be impacted by variable choice.

Also, you only consider the ‘worst case’ ssp585 scenario. Given you are predicting short term, and perhaps this is the most likely outcome given current action on climate change: perhaps this is reasonable, but please provide some clarification and/or justification for this choice, over other scenarios (e.g. ssp370). I presume that you chose this scenario because it would most likely result in the greatest change to species distribution, thus would be the best way to test your hypothesis, but please clarify this.

Niche range: you provide a reference to the method of defining niche range, but could you please add one or two sentences giving a very brief overview of what is involved, given there are many differing ways of calculating niche breadth. Additionally, perhaps you could consider calculating niche hypervolume as a metric of niche breadth as a comparative measure? See Blonder, B., Lamanna, C., Violle, C., & Enquist, B. J. (2014). The n‐dimensional hypervolume. Global Ecology and Biogeography, 23(5), 595-609.

SDM: you do not discuss any steps you took to account for bias in your presence data when sampling background points. Steps should be taken to address this, and the background selected manually rather than using the default maxent settings to account for bias in presence data (see Elith et al, 2011 again, as well as Fourcade, Y., Engler, J. O., Rödder, D., & Secondi, J. (2014). Mapping species distributions with MAXENT using a geographically biased sample of presence data: a performance assessment of methods for correcting sampling bias. PloS one, 9(5), e97122.

You talk about using the ENMeval package. You mention ‘calibration’ and ‘evaluation’ of models. Did this involve using the ENMevaluate function? If so, please mention which feature classes and regularisation multipliers you used. If not, I would suggest that this extra step could be a useful addition to your methodology. Perhaps the results of this process could be added to Table 4?

Regarding your transformation to binary models, did you consistently use one threshold (e.g. maxSSS) or do this differently for each species? Please clarify and provide justification for your choice.
Validity of the findings: Your findings are interesting and contribute to this field of science. However, particularly in your discussion, there are some points you need to address relating to potential caveats with your study to provide greater context for your results.

You should discuss the fundamental caveat that is part of your study – measuring niche breadth, and SDM in general, makes the assumption that a species is occurring at its physiological limits. This means that when you are measuring niche breadth, you are making the assumption that a species would not be able to occur at a level above or below your defined niche. However, if your species isn’t occurring at its limits, due to other, non-climatic reasons such as dispersal barriers, competition and/or under-sampling, for example, you will be definition be underestimating that species’ tolerance of environment. While this doesn’t make your study invalid, you should address this in your discussion when discussing your results. See Bush, A., Mokany, K., Catullo, R., Hoffmann, A., Kellermann, V., Sgro, C., ... & Ferrier, S. (2016). Incorporating evolutionary adaptation in species distribution modelling reduces projected vulnerability to climate change. Ecology letters, 19(12), 1468-1478 for further reading.

Throughout your paper, you often mention ‘habitat’ suitability and change. Please change this throughout to descriptors such as ‘climatic niche’, ‘suitable climatic space’ etc. Habitat encompasses many aspects of the landscape, such as land use, vegetation, etc., but you only consider climatic variables – this is an important distinction to make.

Paragraph 2 of discussion – I am not sure this is contributing any new information, as it is confirming other studies, and also you are not using climate models you have developed, but rather just interpreting public data. This needs to be re-written to focus more on how your results are showing climate change with more explicit reference to your specific species. Also, this is a minor point, but you say ‘throughout the current century’, but you are only considering to 2040 in your study.
Additional comments: Thank you for the chance to review your study. It is an interesting piece of science. I hope that my comments will be able to improve your 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: DOES SIZE MATTER? AN ANALYSIS OF THE NICHE WIDTH AND VULNERABILITY TO CLIMATE CHANGE OF FOURTEEN SPECIES OF THE GENUS CROTALUS FROM NORTH AMERICA
Review round: 1
Reviewer: 2

Output:
Basic reporting: This paper on the correlation between niche width and susceptibility to habitat loss under climate change for multiple species of rattlesnakes was, overall, very clear (except in a few places as noted below) and well written. The authors have done an excellent job reviewing the literature and have included all the key papers that I am aware of. All the figure and tables were clear.
This piece was a coherent unit – and all relevant results were presented.

I saw the supplemental table that included the collections where specimen localities originated, but I did not see any raw data with exact latitude and longitude for each record. Including that would fulfil the Peer J data sharing policy (I believe).
Experimental design: The design falls within the Aims and Scope of PeerJ, and the research question was clear and compelling and addresses a pressing issue of adaptability of an underappreciated taxonomic group. Overall, most of the methods were appropriate and clear enough to allow replication of the results. I had a few questions, mostly to help with clarity.

Line 106 – was there a particular reason why you chose these particular 14 species?
Line 136 – the sample size for each species was perfectly appropriate for Maxent, but I was wondering whether you could say that these points were well distributed across the known range? That is, do you think the species distribution records accurately reflect the total range of each species, or might some species have an under-sampled range?
Line 147 – could you briefly explain what ssp585 is? You mention it in the legend, but not in the text.
Validity of the findings: Their findings seem valid for the methods used.
Additional comments: There were several very minor typos throughout; I highlighted a few that I noticed below.

Line 80: I believe this should read “a predictive measure about how the habitat suitability of a species”
Line 91: I believe this should read “with the greatest number found in Mexico”
Line 101: Rephrasing the phrase to “Can the breadth…” would help with clarity.
Line 203: Table 2, not Tables 2 as written
Line 245: Could you clarify here that bio 12 and 18 are variables related to precipitation, while 1, 2 and 8 are temperature variables?


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: DOES SIZE MATTER? AN ANALYSIS OF THE NICHE WIDTH AND VULNERABILITY TO CLIMATE CHANGE OF FOURTEEN SPECIES OF THE GENUS CROTALUS FROM NORTH AMERICA
Review round: 1
Reviewer: 3

Output:
Basic reporting: This manuscript by Becerra-López and colleagues, analyses the vulnerability to climate change related to niche width of 14 species of Crotalus. The authors performed typical correlative models with Maxent, using occurrence records, bioclimatic layers and three global climate models.

My main concern is the selection of the study model. It is not clear why they selected this genus and in particular those 14 species. The work does not indicate specific reasons. The premise on which this manuscript is based seems coherent and interesting to me, however, it is poorly justified. This is a comparative study between species, however, nowhere in the manuscript do the authors address the phylogenetic context, which can help to understand their results. Therefore, despite his descriptive analysis of the breadth of niches, his results are not robust.

After reading it carefully, this manuscript is written in an extremely simple way and throughout the text, it is not very descriptive. There are no details and justify why this genus, species, methods, algorithm, global climate models, scenarios, etc. Why only one scenario (SSPs-585)? This is a serious disadvantage in terms of replicability. Otherwise, it is not comparable to future work. I found the discussion superficial and uninteresting. At the end of my recommendations, I list some references using snakes as a study model in the context of climate change (not cited here).

Besides I consider the information provided in the present manuscript should be highlighted considering the present state of the reptiles all over the world and the extinction risks due to global warming. This work is not located in this context; it could be exploited in the introduction and discussion sections. While there is not enough information for snakes, in general, there is more information for lizards, which share natural history traits.

Finally, the direction of the new wave of modeling and extinction risk is towards projections that can be verifiable. For example, supported by demographic, physiological data, or even with local present extirpations. Otherwise, these are only projections with high levels of uncertainty. Despite being correlative models, which have less power of predictability (according to many authors), they can be related to possible current extirpations or populations at risk of extinction. On the other hand, in this work the tendencies in the distribution of the species are not detailed in terms of the direction of possible expansions or extirpations according to the suitable habitat, its results are based only on percentages. This makes it impossible for decision-makers to use your work as a reference.
Experimental design: See previous comments
Validity of the findings: See previous comments
Additional comments: I have additional comments that will help to improve this manuscript for future versions.

Introduction
Line 71-72. The authors emphasize “tolerances”, however, I didn't see any discussion of this.

82-84 “most niche models”, correlative models have been widely used, but this is not a solid justification to be used.

Line 88. Authors mention that Crotalus is a good model, but the justification is not clear why. Why those species and not others? Many other groups, even reptiles, are better models, for example lizards. Authors should better justify this part. It seems that authors first selected the group and then established the study question. There is no solid research design. I believe that the genus Crotalus would be a good model if there were demographic or physiological data, or vulnerable population info to validate their results.

Line 90. “There are 53 species” Does this argument make it a good study model?

Line 93. "Precise"? is it the correct word?

Lines 96-98. Here is one of my main concerns. Species selected by the authors. On the one hand, the premise on the effects of climate change and the niche breadth is interesting. However, there is no ecological, evolutionary, physiological or biogeographic justification/context for why these 14 species. It gives the impression that the species selection was a priori or subjective. I was surprised not to see "microendemic" species from islands or others from the Yucatan peninsula. For this reason, the results could be biased. Authors should work on this point.

I am not familiar with the physiology of Crotalus, however its tolerance limits could be informative and would support your ecological niche breadth results. Physiological references are needed to support this research.

Line 104. "precise effects" how do you know that your projections are accurate?

Line 109-111. Although the authors mention: "This information is of great relevance for the establishment and development of conservation strategies for species of the genus Crotalus", in the results or conclusions section there are no figures, models, or particular projections that specify which are the sites of greatest vulnerability in the genus or in each species of study. It is difficult for decision-makers to interpret the results as they are presented. The only figure is not informative.

Line 120. Do you mean “Global Biodiversity Information Facility”?

Line 120. Take a look how to cite GBIF (https://www.gbif.org/citation-guidelines).

123-126. I wonder what would happen if they had integrated "microendemic" species such as Crotalus lanomi, C. stejnegerí, or some other island in the Gulf of Calfornia (C. estebanensis, C. catalinensis).

127-128. Regarding "precise" models. The 2.5º resolution may be adequate in species with a wide distribution, however, for species with restricted distribution, the resolution at 30 sec (~ 1km) would be better. I understand that new layers are not yet available on WClim. Subscalling?

147. It must be justified why they used these GCMs.

147, 168-169 and 191-193. In the M&M section authors used three different global climate models for “Climate Profile and Niche Range” and “Vulnerability of habitat suitability to climate change”: BCC-CSM-MR, CNRM-CM6-1 and IPSL-CM6A-LR. However, different ones are mentioned in the results section: GISS-E2-R and MIROC-ESM. In addition, the methodology should be more carefully and deeply explained, for example Becerra-López et al. (2020) (Line 152).

Lines 168 do you mean: BCC-CSM”2”-MR?

Line 171-172. In this section all the details about the species distribution models should be included. For example, replicates, runs, test and training percentage, cross-validation/bootsrapping/subsampling, considerations for best models, AUC or TSS values, thersholds criteria, etc. This section is poorly detailed. With this information it is impossible to replicate it.

190. “Scenario” or global climate model?

Discussion.
The discussion superficial and uninteresting.

234-244 You need to insert a new first paragraph. The first paragraph of a discussion should be a summary of the most important points the reader should take away from your results. That first paragraph of the discussion sets the stage for the following paragraphs. Subsequent paragraphs should then put those results into context of relationships to previously published literature (is it consistent with that literature or if not, does it indicate a new understanding?).

255 Your results suggest: “low rainfall will continue”? On line 245-246 (results) you say “…the comparison of means suggests that the variables bio12, bio18 and bio19 will present a relative stability for the period 2021–2040”. It seems to be a misinterpretation of the results.

257-259. This is a very general pattern. The authors could focus their discussion on ectotherms or reptiles.

266-269. Here the authors repeat the premise of the introduction, but it is not discussed.

269. They need references to support this claim.

Figure 1.
I am very concerned about this single figure. This figure presented here is unpublishable. It is not necessary to show Alaska and Northern Canada. I recommend zooming in on the maps. The species with the northernmost distribution is C. viridis (M), this could be the limit extension for all the panels. With the zoom, the distribution of the species can be better observed, for example, E, I, L and N. Finally, if the arrangement by the journal allows it, it could be a vertical figure, for example, 3 columns and 5 rows. It is necessary to work on the art of the figure. I also think that figures on the effects of climate change on the distribution of species would be useful. Otherwise their results in percentages are not very useful in conservation strategies.

308-311. Would the results have changed if the authors had selected a wider range of species, eg "microendemic" (C. stejnegeri) or island endemic?

Extra references that could be used.
Aubret, F. & Shine, R. (2010). Thermal plasticity in young snakes: how will climate change affect the thermoregulatory tactics of ectotherms? J. Exp. Biol. 213, 242–248.

Bombi P, Capula M, D’Amen M, Luiselli L (2011) Climate change threatens the survival of highly endangered Sardinian populations of the snake Hemorrhois hippocrepis. Animal Biology, 61, 239–248.

Cabrelli, A. L., Stow, A. J. & Hughes, L. A  (2014) framework for assessing the vulnerability of species to climate change: a case study of the Australian elapid snakes. Biodivers. Conserv. 23, 3019–3034.

Capula M, Rugiero L, Capizzi D et al. (2014) Long-term, climate change-related shifts in monthly patterns of roadkilled Mediterranean snakes (Hierophis viridiflavus). Herpetological Journal, 24, 97–102.

Freedman AH, Buermann W, Lebreton M, Chirio L, Smith TB (2009) Modeling the Effects of Anthropogenic Habitat Change on Savanna Snake Invasions into African Rainforest. Conservation Biology, 23, 81–92.

Mesquita, P. C. M. D., Pinheiro-Mesquita, S. F. & Pietkzac, C. Are common species endangered by climate change? Habitat suitability projections for the royal ground snake, Liophis reginae (Serpentes, Dipsadidae). North-Western J. Zool. 9, 51–56 (2013).

Moreno-Rueda G, Pleguezuelos JM, Alaminos E (2009) Climate warming and activity period extension in the Mediterranean snake Malpolon monspessulanus. Climatic Change, 92, 235–242.

Nori J, Carrasco PA, Leynaud GC (2014) Venomous snakes and climate change: ophidism as a dynamic problem. Climatic Change, 122, 67–80.

Pomara LY, Ledee OE, Martin KJ, Zuckerberg B (2014) Demographic consequences of climate change and land cover help explain a history of extirpations and range contraction in a declining snake species. Global Change Biology, 20, 2087–2099.

Rugiero L, Milana G, Petrozzi F, Capula M, Luiselli L (2013) Climate-change-related shifts in annual phenology of a temperate snake during the last 20 years. Acta Oecologica, 51, 42–48.

Sahlean TC, Gherghel I, Papes M, Strugariu A, Zamfirescu SR (2014) Refining Climate Change Projections for Organisms with Low Dispersal Abilities: A Case Study of the Caspian Whip Snake. PLOS ONE, 9.

Winter, M., Fiedler, W., Hochachka, W. M., Koehncke, A., Meiri, S. & De la Riva, I. (2016). Patterns and biases in climate change research on amphibians and reptiles: a systematic review. Royal Society Open Science, 3(9), 160158.

I found it surprising that the authors did not discuss their results with this paper (or even other viviparous species):

Lourenço-de-Moraes, R., Lansac-Toha, F. M., Schwind, L. T. F., Arrieira, R. L., Rosa, R. R., Terribile, L. C., Lemes, P., Fernando Rangel, T., Diniz-Filho, J. A. F., Bastos, R. P. & Bailly, D. (2019). Climate change will decrease the range size of snake species under negligible protection in the Brazilian Atlantic Forest hotspot. Scientific Reports, 9(1).


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

Input:
Title: DOES SIZE MATTER? AN ANALYSIS OF THE NICHE WIDTH AND VULNERABILITY TO CLIMATE CHANGE OF FOURTEEN SPECIES OF THE GENUS CROTALUS FROM NORTH AMERICA
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors have addressed each of my points from the first revision. They have also addressed points from the other reviewers to a great standard, and I have no major comments. Some very minor typographical issues I noticed during my review:

Line 128: Typo (‘futher’ -> ‘further’)
Line 136: change ‘recorded’ to ‘obtained’ or similar.
Line 139-140: Perhaps change ‘We carried out a reduction in the number of variables under the criterion that the most robust sets of variables were those that had a direct interaction with the species. These variables were chosen on the basis of ecological theory, and subsequently reduced, when necessary, by statistical analysis (Austin 2007).’ To
We selected a subset of these variables on the basis of ecological theory, and subsequently reduced, when necessary, by statistical analysis (Austin 2007).
Line 161: move your reference for R to the first mention in the paper (Line 127). Also, you have referenced different versions of R – double check which version is correct, and I believe you only need to mention the version in the first instance (for all subsequent times you mention R, simply write ‘R’)
Line 203-205: there is some repetition here from earlier in the methods, you can simplify as you have already said which models you used and where they came from.
Line 322: add a reference for this claim.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The authors have greatly improved their paper in the review process, and have addressed the suggestions of each of the reviewers to a great standard.


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: DOES SIZE MATTER? AN ANALYSIS OF THE NICHE WIDTH AND VULNERABILITY TO CLIMATE CHANGE OF FOURTEEN SPECIES OF THE GENUS CROTALUS FROM NORTH AMERICA
Review round: 2
Reviewer: 2

Output:
Basic reporting: I appreciated having the change to re-review this interesting work. Overall, I thought that the revisions were a big improvement in the clarity and utility of the paper. I only have a few minor suggestions here:
1)	Line 129: You say that you assessed sampling bias, but I wasn’t sure what that meant. Did you address observed sampling bias in some way?
2)	Line 168: I believe tukey’s post hoc should be capitalized here
3)	Line 184: You say that you choose this climate scenario to test your hypothesis “in a better way”. I see what you are saying here, and that this comes from a reviewer’s suggestion, but I think you can phrase it slightly better. Something like “using the most extreme climate scenario provides the best test of our hypothesis as this will result in the largest difference between current and future environmental conditions” or something like that.
Experimental design: No Comment
Validity of the findings: No Comment
Additional comments: I am satisfied with how the authors have addressed my original 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: IDENTIFICATION AND CHARACTERING OF APX GENES PROVIDE NEW INSIGHTS IN ABIOTIC STRESSES RESPONSE IN BRASSICA NAPUS
Review round: 1
Reviewer: 1

Output:
Basic reporting: APX is important for the growth and development of organism to resistant the external stress. In this paper, authors detailedly described the structures and phylogenetic relationship of APX in B.napus, and their functions in abiotic stress were also briefly studied. In general, the paper supplies a professional guidance for the further study and application of APX in B.napus. However, the discussion part is a little bit wordy and did not catch the key point of the discover in this paper, which is encouraged to discuss it more streamlined and in-depth. And also, the last paragraph of introduction should be described more logically. Fig. 6 should be reorganized, as the APX activities and the content of H2O2 are totally different with qPCR graph, they should be set up as independent sub-figure, i.e., Fig 6b and Fig6c. Figure legends also need to be revised to make figures understood easily.
Experimental design: The title is suggested to be modified, as the paper is mainly described the structures and phylogenetic relationship of APX, and the response of APX to abiotic stress only occupies small portion.
Validity of the findings: No comment.
Additional comments: Line 16: Brassica napus (B.napus), abbreviation statement for the first time.
Line 81-83: Suggest to move this part to the behind of ....crop quality (Zhu, 2016), and modify the words to make it more logical.
Line 222: Suggest to be replaced by " Activity of APX under abiotic stress treatment".
Line 229: Replace with "which was basically opposite to APX activity" . Go through all the paper to check the logical of sentences.
In discussion, suggest to speculate why the activity of APX in B.napus was increased firstly, and then decreased with diverse treatments,as showed in Fig 6.
Line 275: ...the gene has..., line 288, played...., etc, check all the manuscript to make the words more correct.
Go through the reference to make them unified.
Line 436-439: describe the mean of lines connection from one gene to another.
Line 452: remove " of the same length" as the length of introns is different. and the gene names on figure should be italic if possible to change.
Line 454-455: Describe the indication of black line in Figure 5.
Line 457: replace three treatments with various treatments, and reorganized Figure 6, i.e., enzyme activity was set as Fig. 6b, and H2O2 content was Fig. 6c.


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: IDENTIFICATION AND CHARACTERING OF APX GENES PROVIDE NEW INSIGHTS IN ABIOTIC STRESSES RESPONSE IN BRASSICA NAPUS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Major:
1. Line 35-48, the authors introduced the ROS background information; however, there is lacking the important information about carotenoids as they play critical roles in the chloroplasts in quenching ROS.  Few references mat be considered: N. Nisar, et al. Carotenoid metabolism in plants. Mol. Plant, 8 (1) (2015), pp. 68-82; Havaux, M. Carotenoid oxidation products as stress signals in plants. Plant J. 79, 597–606 (2014); Wang, J. Y., Lin, P.-Y., & Al-Babili, S. On the biosynthesis and evolution of apocarotenoid plant growth regulators. Semin. Cell. Dev. Biol. 109, 3–11 (2020).
2. Line 164-173, is the localization of the un-mapping APX could be isoforms of some of the APX and that’s why some of the APXs could not be confirmed?  In line 173 the authors claimed AtAPX has the same feature as BnaAPX, but there is no such a figure of AtAPX to support it. Also, figure 4 should be named figure 2.
3.  There is lacking references from lines 175-185 where the authors claimed the functions of APX among different clades and do not repeat the same sentence in the discussion part as it is wordy.
4. Line 188, figure 5 should be figure 4 in the text. Please re-arrange the figures.
5. Line 203-229, if I understood well, there is no localization data as well as whole leaves for qPCR; if this is the case, the authors should not claim the cytosolic or microsomal APXs. Otherwise, they should provide such a dataset. Moreover, there is no statistical test in the transcript and biochemical results, which makes it difficult to assess the data. In addition, please mark those figures clearly linked to the text.
6. Line 251-254, the phylogenetic analysis may not relate to the evolutionary cluster but functions; please check this claim carefully.
7. There is no discussion about the biochemical results?

Minor:
1. I would recommend using the full name with an abbreviation, such as Ascorbate peroxidase (APX), instead of APX (Ascorbate peroxidase) in the text.
2. Strongly suggest the authors re-check and revise the grammar carefully and better to read by naïve speakers.
3. Line 67-68, there is a missing or typo: it is a higher “anity“
4. Gene should be italic and could delete gene, such as APX in line 88 rather than APX gene.
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: IDENTIFICATION AND CHARACTERING OF APX GENES PROVIDE NEW INSIGHTS IN ABIOTIC STRESSES RESPONSE IN BRASSICA NAPUS
Review round: 2
Reviewer: 1

Output:
Basic reporting: Authors have revised all the manuscript based on the reviewers suggestions.
Experimental design: No comment
Validity of the findings: No comment
Additional comments: No comment.


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: IDENTIFICATION AND CHARACTERING OF APX GENES PROVIDE NEW INSIGHTS IN ABIOTIC STRESSES RESPONSE IN BRASSICA NAPUS
Review round: 2
Reviewer: 2

Output:
Basic reporting: The authors have satisfactorily addressed all my and the other reviewers' comments , and I appreciated the authors for improving the text. I have no further major comments.
Experimental design: A minor point, please add the biological replicate numbers (e.g. n=3) in the legends as well as the detailed statistical description, such as Statistical analysis was performed using two-tail student t-test. Different letters denote significant differences (*p < 0.05, **p< 0.01, ***p< 0.001).
Validity of the findings: N/A
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: A NEW JUVENILE YAMACERATOPS (DINOSAURIA, CERATOPSIA) FROM THE JAVKHLANT FORMATION (UPPER CRETACEOUS) OF MONGOLIA
Review round: 1
Reviewer: 1

Output:
Basic reporting: Missing literature in the references:

Line 77: "Norell and Barta, 2016" is not cited in the references.
Line 81: "Tereshchenko, 2020" is not cited in the references.
Line 83: "Tsogtbaatar et al., 2019" is not cited in the references.
Line 84: "Watabe et al., 2010" is not cited in the references.
Line 102: "Hone et al., 2014" and "Griffin et al., 2020" are not cited in the references.
Line 200: "You et al. 2007" is not cited in the references.
Line 358: "Butler et al., 2008" is not cited in the references.
Line 392: "Lambert et al., 2001" is not cited in the references.
Line 821: "Dieudonné et al., 2020" is not cited in the references.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: No additional comments