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: RELIABILITY OF THE VELOCITY ACHIEVED DURING THE LAST REPETITION OF SETS TO FAILURE AND ITS ASSOCIATION WITH THE VELOCITY OF THE 1-REPETITION MAXIMUM
Review round: 1
Reviewer: 2

Output:
Basic reporting: No comment. All comments in the general comment section.
Experimental design: No comment. All comments in the general comment section.
Validity of the findings: No comment. All comments in the general comment section.
Additional comments: Overall Comment

Overall, I thought this study was well-conducted. I have some thoughts which I believe will improve the manuscript. However, consistent with PeerJ’s reviewing policy which is centered around the validity of a paper, this study has undoubtedly met that. Therefore, the below is my opinion on what I would like to see if the authors agree. I do think the below will improve the impact of the paper, but again, PeerJ does not require this as criteria in the review. So, I am offering what I can. Please feel free to agree or disagree.

Introduction

1.	%1RM should be changed to percentage of 1RM throughout.

2.	Introduction, Line 68: I don’t believe the Torrejon 2018 study is a good study to use as evidence for men and women having different velocity profiles. First, this sentence states that men have higher velocities than women at the same percentage of 1RM, which is not at all what the study shows. It does show that at lower intensities (<60%), but at higher intensity this study shows the opposite, which is that men have slower velocities than women. Further, the men in the Torrejon study had a much higher training age and relative strength level than the women, so it would be inappropriate to conclude that sex was the determining factor. In fact, other data from Zourdos et al. (https://www.ncbi.nlm.nih.gov/pubmed/?term=26049792) and Ormsbee et al. (https://www.ncbi.nlm.nih.gov/pubmed/?term=28301439) have shown that experienced lifters have slower velocities than novice lifters at high intensities. So, while we cannot know for sure what is driving the results of the Torrejon study, the conclusion with the most support in the literature would be that training status is influencing the velocity and not sex.

3.	Lines 101-105 state that the two main bench press variants are benching with a pause and without a pause and that benching with a pause is a “concentric-only” movement, which is a false statement. A bench press with a pause, even in powerlifting meets, means that you press the bar as soon as the bar comes to a complete stop on the chest, which could be less than a second. Some studies may use a full second (they shouldn’t), but the stretch reflex only completely dissipates after 4 seconds, and this study used a 2-second pause, thus this is not a concentric only movement. I would change that wording.

4.	The last comment leads me to the final paragraph of the introduction. Concentric-only should be changed to “paused bench press”. Eccentric-Concentric should then probably be changed to “touch and go bench press”.

5.	I would improve the rationale a bit since the hypotheses are essentially that significance would not be found.

Materials and Methods

1.	Why did some participants only perform one of the types of movement? Was it that there was a recording error? Or did some participants simply not perform the other by choice? If the latter, why?

2.	Line 147, as noted above, please change to “75% of 1RM” and “90% of 1RM” and do so throughout.

3.	I don’t understand how individuals with over a year of experience on average can have a 1RM smith machine bench press of only about 65kg…that is very light. I must assume that some participants were completely untrained? If so, this should be clarified.  I would just report more details of training experience.

4.	Lines 169-170, how was the load determined for the 2 sets to failure? My apologies if I am missing more specifics.

5.	I would change mean velocity to mean concentric velocity throughout. Since the term “eccentric-concentric” and “concentric-only” (although those should be changed) are used, then used mean concentric velocity will clarify for the reader that only concentric velocity was assessed.

6.	The most important finding, in my opinion, is that the velocity of the 1RM was different than the velocity of the last rep during the set to failure. Therefore, in the text of the results I would mention the average number of reps on the sets to failure and what the average intensity used was for these sets.

7.	Was there a difference in the last set mean velocity of the last rep between set 1 to failure and set 2 to failure? Even if there was not, the 2nd set tended to have a slower last rep velocity. Why? To me this is very interesting for programming purposes. If this number is static, and presumably all velocity/RPE/RIR relationships leading up to it are accurate, then an individual can program using velocity to be at a certain RPE/RIR each set. If this number is not static, then using velocity-based training in this regard has limitations and RPE/RIR may be a better choice. So, what does the analysis say? Is this number static? I would then add more of this into the discussion.

Discussion

1.	Lines 281-287 miss the point of the relationship between 1RM strength and 1RM velocity. We do indeed know from the Zourdos and Ormsbee studies mentioned above and I believe from the Torrejon study mentioned above that a higher training status is associated with a slower 1RM velocity. However, at a certain point (i.e. a few years of training) the difference isn’t as pronounced between moderate and experienced lifters as it is between experienced and novice; presumably because neural adaptations play less of a role later on in a training career. Although, when trained lifters perform ultra-specific training we do know that 1RM velocity becomes slower (https://www.redalyc.org/pdf/3092/309245773040.pdf). Therefore, this line is a bit too strong in its claims. If anything, we are still very much searching for why velocity profiles are individualized, and training status probably has the most support for influencing velocity profiles. I think reporting minimums and maximums of the training ages and perhaps confidence intervals could help here.

Final Comments

I’d like to say, that despite my comments above, the study was well-conducted and deserving of publication. I just would like to see the above clarified, but it is just my opinion. I think more consideration should be given to the difference between the 1RM velocity and the velocity on the last rep of the sets to failure. Further, the velocities all various RIR points (5-0RIR) could be compared between the 2 sets to failure. If these are reliable then that is a very practical finding for velocity based training. This would also reveal that using velocity cutoffs would be superior to using velocity loss in many programming cases. A practical and useful discussion could be written around this. I think that could be a cool addition, but not necessary, just my thoughts.


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: RELIABILITY OF THE VELOCITY ACHIEVED DURING THE LAST REPETITION OF SETS TO FAILURE AND ITS ASSOCIATION WITH THE VELOCITY OF THE 1-REPETITION MAXIMUM
Review round: 1
Reviewer: 3

Output:
Basic reporting: This study provides interesting data regarding the reliability of the velocity achieved during the last repetition of sets to failure (Vlast) and the association of Vlast with the velocity of the 1-repetition maximum (V1RM) during the concentric-only and eccentric-concentric bench press (BP) exercises. Present results demonstrated that reliability of Vlast was below the threshold of acceptable reliability for both BP variants. Vlast was always significantly lower than V1RM, while no significant differences between the BP variants were observed for V1RM or Vlast. Finally, the authors concluded that even though Vlast could be a more appropriate indicator of the minimal velocity threshold than V1RM, a general V1RM could be more appropriate to estimate the 1RM during the BP exercise performed in a Smith machine.

The paper is well written and provides interesting findings for those coaches and athletes who perform velocity based training in a daily manner.
Experimental design: The research question falls within the scope of the journal. The rationale of the study is clearly stated and the research question fills a gap in the velocity-based training literature. The methods are described with sufficient detail.

I have only minor comments that are outlined in the "comments to the authors" section.
Validity of the findings: All underlying data have been provided. The statistics are ok. I only have a minor comment on implementing a new statistical test (Bland-Atman) to represent the bias between the two outcomes (Vlast and V1RM) measured. Finally, conclusions are well stated and linked to the original research question & limited to supporting results.
Additional comments: This study provides interesting data regarding the reliability of the velocity achieved during the last repetition of sets to failure (Vlast) and the association of Vlast with the velocity of the 1-repetition maximum (V1RM) during the concentric-only and eccentric-concentric bench press (BP) exercises. Present results demonstrated that reliability of Vlast was below the threshold of acceptable reliability for both BP variants. Vlast was always significantly lower than V1RM, while no significant differences between the BP variants were observed for V1RM or Vlast. Finally, the authors concluded that even though Vlast could be a more appropriate indicator of the minimal velocity threshold than V1RM, a general V1RM could be more appropriate to estimate the 1RM during the BP exercise performed in a Smith machine.
The paper is well written and provides interesting findings for those coaches and athletes who perform velocity based training in a daily manner. I only have minor comments as outlined below.

Although authors provide the training experience of the subjects (1.3  2.4 years), was a familiarization session performed? If so, please insert into the text. If not, would this compromise the reliability results?
The protocol is well described, however, I am concerned about how the accumulated fatigue during the session (the incremental loading test, 1st set to failure and finally 2nd set to failure) could compromise the reliability results for the Vlast. Please comment.
Why the mean velocity was chosen instead of peak or mean propulsive velocity? Please, provide a rationale.
Regarding the statistical analysis, I think it would be also appropriate using the Bland-Atman method to contrast the bias from the Vlast and V1RM.


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: RELIABILITY OF THE VELOCITY ACHIEVED DURING THE LAST REPETITION OF SETS TO FAILURE AND ITS ASSOCIATION WITH THE VELOCITY OF THE 1-REPETITION MAXIMUM
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Thank you for considering my revisions and responding to them.


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

Input:
Title: RELIABILITY OF THE VELOCITY ACHIEVED DURING THE LAST REPETITION OF SETS TO FAILURE AND ITS ASSOCIATION WITH THE VELOCITY OF THE 1-REPETITION MAXIMUM
Review round: 2
Reviewer: 2

Output:
Basic reporting: Clear
Experimental design: Within aims of journal and sufficient
Validity of the findings: Valid
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: RELIABILITY OF THE VELOCITY ACHIEVED DURING THE LAST REPETITION OF SETS TO FAILURE AND ITS ASSOCIATION WITH THE VELOCITY OF THE 1-REPETITION MAXIMUM
Review round: 2
Reviewer: 3

Output:
Basic reporting: The authors carefully addressed all my previous concerns.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The authors have made a good job with the reply to my previous comments.


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

Input:
Title: APPLICATION OF ARTIFICIALLY INTELLIGENT SYSTEMS FOR THE IDENTIFICATION OF DISCRETE FOSSILIFEROUS LEVELS
Review round: 1
Reviewer: 1

Output:
Basic reporting: This paper is well written in clear professional English with just a few exceptions that can be easily fixed.  Line 89, I think the authors mean to say “restoration”. On lines 118-119, it might be better stated that “At both sites, standard fossil vertebrate excavation protocols were followed in the extraction of paleontological remains (Eberth et al. 20007)”. On lines 123-124: “Additional data were also collected concerning the degree…”. The final sentence on lines 161-162 should be revised…while “conflictive” is apparently an English word, it is not an often used word, and I think the sentence can be phrased more clearly by using an alternative form, perhaps some form of the verb “to conflict”. Lines 165-166…”The algorithm works by separating points within the cluster from those on the border of the cluster…”. Lines 177-178…”The final components that define point density for clustering ARE established…”. Line 221…” separated and assigning these clusters to a new labelled layer”. Line 224-226…”in as much as the expert knowledge is used for troubleshooting and debugging (Dellerman et al., 2017:70: this is also known as a sense-making approach.” Lines 254-255…”These loop algorithms ran for 50 iterations and were then extrapolated and used for the final classification models.” Line 258 I would drop “These consisted in:”.  Line 273…”The RD algorithms USE small random numbers”. Line 282…use either “Model evaluations were performed” or “Model evaluation was performed”. Line 288…”that measure model agreement”.  Lines 316-317…”This is a result of the irregular density patterns detected in the data and probably results from numerous geological and paleontological…”.  Please make clearer the meaning of the sentence beginning with “Nevertheless” on lines 318-320.  Line 327 “highlights”, and please edit/clarify the sentence on Lines 324-325 beginning with “For Batallones-3 right slice”. Line 331…”a large number of clusters”.  Line 333…”could be recognized as products of”.  Line 342, “effectivity” is not the word you want here (not sure if it is a word)…please rephrase. Line 435…”rather than  the entire upper or lower part of the cavity”.  Lines 429-432 “In the case of Batallones-10, the encasing rock has not yet been found and, therefore fossil material recovered in future excavations may reveal additional discrete and separable fossiliferous layers”. Thus, the increase in the number of levels at Batallones-10 cannot be discarded.” Line 436…”such as those described by Lopez-…” Line 477-478…”including three discrete levels at both Batallones-3 and Batallones-10.” Line 493…”an even finer tuning of these models”.
The Intro and Background sections are reasonable, although contrary to the claim made on lines 91-92, a number of vertebrate paleontologists have been developing AI approaches to site location (including Paul Barrett, Amy Chew and Kate Oheim, RL Anemone, CW Emerson, GC Conroy) and this work should be referenced in this paper.
Figures are nicely put together and relevant and raw data are supplied along with R code.
Experimental design: In most respects, the manuscript fits within the scope of Peer J, but there are some issues worth considering.  While the investigation is rigorous in terms of experimental methods and the methods utilized are highly appropriate, some important aspects seems to be missing.  The nature of the fossiliferous levels that the paper explores is not clearly described.  Are the authors attempting to identify biostratigraphic layers that differ in time from within a site, or are they trying to identify assemblages that have different depositional or post-depositional histories? What meaning do the authors ascribe to the purported “discrete fossiliferous levels” is never made clear.  As I understand it, the two sites under consideration were never separated into discrete fossil-bearing levels. Therefore, I’m unclear what the training for the supervised classification was based on and I’m puzzled about the absence of a confusion matrix to identify how well the algorithm worked.  I imagine that the authors used the DBSCAN results and geological interpretations presented in Figures 3 and 4 as the basis for identifying 3 discrete levels, and then trained the supervised classifiers based on these results. Is this correct? If so, I’m unsure about the process of drawing the dotted lines in these plots to determine the existence of 3 levels…this seems arbitrary (why not 2 or 4 levels?), but perhaps the authors can better explain this to my satisfaction.  The need for a confusion matrix remains in order to evaluate the operation of the predictive algorithms.
Validity of the findings: I believe that many of my comments in the previous section are perhaps relevant to this section too.  The authors need to do a better job of convincing me that there is nothing arbitrary about their conclusion of 3 and only 3 discrete layers at Batallones -3 and 10, as well as their understanding of what these layers mean for interpretation of the sites under consideration.
Additional comments: I commend the authors for their innovative application of sophisticated AI approaches to the problems of taphonomy and biostratigraphy and I’m convinced that this work establishes a proof-of-principle for this kind of work.  I wonder if a better test of their methods might be to try to reproduce a clearly determined, a priori biostratigraphic zonation (based on standard approaches) at some site in order to see if their AI approach could replicate it.  Or alternatively, they could compare the results they present in this manuscript to a standard zonation of the same site in a blinded fashion. The reader would then be able to more easily understand how well the new approach works in relation to the previous methods used.


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

Input:
Title: APPLICATION OF ARTIFICIALLY INTELLIGENT SYSTEMS FOR THE IDENTIFICATION OF DISCRETE FOSSILIFEROUS LEVELS
Review round: 1
Reviewer: 2

Output:
Basic reporting: This article is generally well written with only a few minor grammar or spelling issues.  Most style guides recommend that terms like "Machine Learning" and "Artificial Intelligence" should only be capitalized when they are a proper noun, such as when they are in a journal or conference title.  The article is structured according to the Peerj guidelines.  The references are generally ok (some are separated by a blank line, others are not), but more descriptive background on the characteristics of the fossils is needed.  The distinction between the upper herbivores and lower carnivores in the two lobes of the caves is understood, but do the three modeled layers at each site contain different species?  Much more background on the taphonomy and paleoenvironment at the two sites would give the reader a better idea of the problem domain.  A simple map of the two localities that shows how the slices are oriented with respect to the local Cartesian coordinate system is needed to fully comprehend the spatial configuration of the fossil point cloud.  Other issues with figures are that the font size in Figure 2 is very small—this should probably be split into two separate figures at larger scales (one for each locality) as was done in Figures 3, 4, 6, and 7. Why is only the right slice of Batallones-3 depicted in Figure 4?  In Figure 5, the legends need units.  All of the Importance axes of the Figure 8 plots should be on the same scale to facilitate comparison. The DBSCAN unsupervised clustering algorithm requires a minimum points parameter along with epsilon, a maximum distance value.  The latter is determined using the “elbow” of k-distance graphs.  The epsilon parameter used in the final model needs to be listed, and the appropriate k-distance graph from which this value was derived should be included as well.  Line 375 incorrectly refers to Figure 6B as the left profile.  Lines 404-410 in the Discussion section repeat what was said in lines 371-379.  Similarly, lines 412-417 repeat lines 381-386.
Experimental design: The unsupervised clustering of the 3D locations of fossils in the two sites is fairly well explained (with the exception of the epsilon parameter noted above) but the collaborative learning discussion needs much more detail.  In my reading of the text, a number of geologists collaborate to draw the layer boundaries between clusters along the slice (x-direction for Batallones-3) and across the 2 meter slices.  In Batallones-10 the layer boundaries are drawn between clusters that extend along the longitudinal axes of the x and y slices.  It is never made clear why the slices are parallel at Batallones-3 and orthogonal at Batellones-10.  70 percent of the points were then used to train a support vector machine or random forest supervised classification algorithms.  These results had very high accuracy statistics, but one has to wonder what the results would be if the classifiers were trained on 30 percent of the points and assessed on the larger portion.  It isn’t really made clear exactly how the supervised classifications moved the layer boundaries or otherwise improved on the expert-in-the-loop.  The formula for mean squared error on line 294 is incorrect (missing the squared exponent).  The fine tuning of the levels is not explained sufficiently.  Was this another supervised classification of the noise points or was it manual reassignment of the points like the expert-in-the-loop approach?
Validity of the findings: It was helpful having the R script to get a better idea of the methodology.
Lines 104-106 state that the goal is to establish whether or not machine learning can quantitatively identify fossiliferous levels in paleontological and archaeological sites based on the spatial distribution of fossils.  Lines 487-488 in the conclusions state that artificial intelligence algorithms were shown to be an objective means of automating spatial pattern detection.  The DBSCAN clusters certainly provide a valuable quantitative input to the expert geologists who identified the layers, but the entire process is not really automated.  The authors admit this on lines 458-469 and the conclusion that taphonomic features can fine tune the model is a point well taken.  It may be a good thing to adjust the goal and conclusions to emphasize how unsupervised and supervised techniques can reduce (but not eliminate) the amount of subjectivity in decisions made using the expert-in-the-loop process.
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: APPLICATION OF ARTIFICIALLY INTELLIGENT SYSTEMS FOR THE IDENTIFICATION OF DISCRETE FOSSILIFEROUS LEVELS
Review round: 1
Reviewer: 3

Output:
Basic reporting: This paper introduces a new quantitative method for classifying fossiliferous levels, using the following pipeline: 1 – clustering of xyz coordinates (dbscan), 2 – domain-expert intervention (hard-coded grouping of clusters), 3 – classification (svm, rf). This approach might be useful when there are no clear stratigraphic horizons. The paper is well structured, figures are clear, data is available, and the code provided is documented. Overall, the manuscript is clearly written but I have worries over some use of terminology, and I believe there are many things that can be improved in that regard.
The introduction is strong, providing important background and contextualization for the late Miocene fossil sites. There is however a large gap in the literature references of AI applications to palaeontology and a quite strong statement (lines 91-93) that needs revision. Palaeontologists have been using machine learning for a myriad of problems, there is not just one exception! Just recently, Püschel et al (DOI: 10.1098/rsif.2018.0520) used multiple supervised classification (and other algorithms) to tackle a specific hypothesis (concerning functional/morphological data) in palaeontology – I am sure there are many more papers like this. But far more relevant to the authors are the several papers on paleontological remote site detection using neural nets and other approaches. See Wills et al. (DOI: 10.1016/j.palaeo.2017.10.009) a simple MDS + LDA pipeline (but still); Block et al (DOI: 10.1371/journal.pone.0151090) uses an “ensemble”-like tactic combining Bioclim, MaxEnt, GLMs and logistic regressions; and see also the several papers of Conroy, Anemone, Emerson, and others (ca. 2011-2015) using unsupervised and supervised methods to find fossil sites in Utah and Wyoming. The recently published book “New Geospatial Approaches to the Anthropological Sciences” also has some chapters about these machine learning approaches for fossil site detection from satellite images. I consider these additions are essential to show how your work fits into the broader field of AI applications to palaeontology.
Experimental design: The documentation of the spatial distribution of remains is the chosen method of data acquisition. Thus, the dataset is exclusively composed of non-labelled triplets of 3D-coordinates. The authors mention the collection of the following variables: taxon/id; bone element; degree of articulation; preservation; and so on. Nevertheless, such variables were not used in any step of the statistical modelling pipeline. It is not very clear why.
First step proposed by the authors is to apply the popular outlier-detection algorithm, dbscan. In line 152 the authors mentioned they used the dbscan package implementation, however in their code the fpc package implementation (which is quite different) is used instead. This needs clarification, since it looks like the dbscan package was only used to find hyperparameters through the visual/manual elbow method. It can also confuse amateur R users, e.g. method = "hybrid" (in the code provided) works in the fpc::dbscan but in the dbscan package implementation it is an unknown parameter leading to an output error. In line 201 you mentioned dbscan (step 1) “removing noises” – however in the code you provided this is manually hard-coded in the end of step 2. Maybe rephrase it to “identifying noises” which is what dbscan does by assigning noisy rows to cluster 0.
Step two is a manual labelling step, effectively clustering all the clusters into less clusters. In my view, it is described in a very glorified and puzzling way. But before going into that, there is a problem of designations. I believe it is less confusing if authors would instead stick to just one designation (or explain why there might be many and then stick with one). In my view, this seems ultimately just a simple step for reorganizing labels, as dbscan alone did not match the desired results. Yet, we are confronted with the following terminology: “Collaborative Intelligence Learning”; “human-in-the-loop collaborative strategy”; “hybrid intelligence”; “Expert-in-the-Loop (EitL)”; “geologist-in-the-loop”; “Machine Teaching (MT)”; “sense-making approach”; “MT-DBSCAN”. I suggest authors to keep it simple and thus clearer. Lines 232-234 say that with this hybrid approach noise can finally be identified, but previously in line 201 noises were removed. Very contradictory, please clarify. If the problem step 2 is trying to solve is dbscan’s final output over-generating clusters, I think hdbscan developed by Campello, Moulavi, and Sander (2013) might work as an alternative to step 1+2. If the authors have not tried this before, I suggest it might be worth a try, because relabelling by geologists as a mandatory mid-step in the pipeline makes it harder to streamline the method and generalize it to other sites.
Final step is a supervised classification of the labels reorganized by the experts in the previous step. Train/test split is correctly done, as well as 10-fold cross-validation. However, authors describe at length they used a special version of the k-fold CV algorithm for spatial data (lines 243-250). Notwithstanding, the code instead provides a standard implementation of the CV algorithm from the caret package: trainControl(method = "cv", repeats = 10). Also, just for clarity, repeats= control repeats, folds are controlled by the “number = 10” argument. Moreover, the following lines (251-255) described a systematic hyperparameter search that I also did not find in the code provided. Lines 268-269 mentioned e1701 and kernlab for applying svm, but in the code caret was used instead. Line 282 mentions deep learning again, and I really fail to see how DL is relevant for this paper’s methods. Also, DL is not a different thing from ML, it is a subset of it. Lines 302-307 mentioned an 80% security threshold to allow correct identification of the unknown datapoints during the predict(), which is also not available in the code. Thus, the code to generate Table 2 is also not available.
Validity of the findings: My main concern in terms of the validity is that many parts of the methods were described in ways that do not fully correspond with the code provided. It seems like right now the experimental design and results are not fully reproducible even though all the data was provided. Which I find extremely troublesome. The results section also has some details I would like to see clarified. It is never explained how the proper “corresponding palaeontostratigraphic level” is defined for noisy points and how the success can be measured if the true label is not known a priori (lines 358-360). If this is achieved based on a strict prediction that excludes the possibility of the “noise”-label, it should be stated in a straightforward manner as this means you do not have a statistical test of success, just a prediction. I found the use of the term “cleaned” (line 372) to not be the best choice. After all, supervised algorithms are classifying/discriminating the data, not “cleaning” it (data cleaning as a technical term is usually for pre-processing steps, before modelling, like removing NAs, etc.).
Discussion/conclusions do a good job at highlighting the relevance of this work and providing a framework for future directions. If the new stratigraphic horizons make sense, future work can refine geochronological relationships using e.g. biostratigraphy of micromammals. However, before that, the pipeline needs some improvements. Maybe the next steps are indeed to add more variables as suggested by the authors, specifically containing taphonomic, geological and faunal information to refine this approach so it can be really automated or close to automation. Trying different unsupervised approaches might also improve the results in the first step of the pipeline. Ideally so we do not even need step 2.
I am glad that this approach was useful to better understand the boundaries of stratigraphic horizons at the Batallones sites 3 and 10. This is undoubtedly the strong point of the paper, and it shows the method described has clear promise. Yet, I find the last sentence of the Conclusions to be a bit “hyped”. I disagree this is an important step for automation in the disciplines, since all step 3 is doing is learning what the geologists manually re-labelled in step 2… How can this be considered automation? Automation was only attempted at step 1 and it failed. Furthermore, it could be argued that determination of clusters by dbscan is never a true automation because of the problematics of generalizing MinPoints and eps (manually selected here as well), which are always dataset-specific and therefore site-specific. I think automation should not be addressed in the paper, or if addressed at least in a more realistic perspective considering what was achieved.
Additional comments: Good job, I believe that with the right adjustments to the manuscript, this contribution might help other palaeontologists working in sites with similar problems of complex/unclear horizon diagnosis. I hope my comments can help you improve the quality of the manuscript.
Below, a list of some details that can easily be improved:
In the abstract “stratigraphical horizons” reads better as “stratigraphic horizons”.
In line 119, the reference protocol cited (Eberth et al, 2007) seems to be missing in References.
In lines 127 and 129 “For the purpose of this study” is repeated.
In line 241 “Considering the amount of data produced by the DBSCAN algorithm” is not clear, i.e. makes it sound dbscan is a simulator/data-generation approach instead of a clustering algorithm. Please rephrase.
Line 351 “exponentially small” is a technical term for describing decay or a tendency in a function.
I highly disagree of using “machine teaching unsupervised algorithms” (lines 443-444), which is not a thing. Maybe you meant “learning” instead of “teaching”? If you are manually adding labels, deleting labels, reordering labels, reclassifying labels, grouping labels, etc. it stops being unsupervised. In fact, “Machine teaching” and “unsupervised algorithms” are almost perfect antonyms!
Best regards,


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: CO-EXPRESSION CLUSTERING ACROSS FLOWER DEVELOPMENT IDENTIFIES MODULES FOR DIVERSE FLORAL FORMS IN ACHIMENES (GESNERIACEAE)
Review round: 1
Reviewer: 1

Output:
Basic reporting: Language comments
The manuscript is written in ambiguous landuage in some part, eg. P46-47, P51, P58-59 ……and so on. Writing skills must be improved before acceptance.
Introduction
1.	The introduction lack the literature about the specific pollinators of 10 species.
2.	The correct citation format should be (Pickrell et al. 2010; Raherison et al. 2015) in P59, so as the follows.
Experimental design: 1.	The flower forms of 10 species should be described more clearly, such as the colors and types of each species.
2.	The bud stage and D stage should be describe by the paraffin sections to clarify the difference of them. And you can also supply the pictures under the dissecting microscope.
Validity of the findings: 1.	P377-378 More figures are needed to prove it or summarize it.
2.	P384-385 Please provide evidence to support this sentence.
3.	P389-390 It is inconsistent with the figures, please check it. \
4.	There are only few hub genes are mentioned in the results and more hub genes relevant the flower development should be discussed. And the expression of hub and candidate genes should be vertificated by the qRT-PCR.
Additional comments: I am glad to have the opportunity to evaluate your article titled “Co-expression clustering across flower development identifies modules and candidate genes for diverse floral forms in Achimenes (Gesneriaceae)”. In general, it is a reasonable article as you built a transcriptome database using 10 species of Achemenes. And Co-expression clustering and relationship between network connectivity and evolutionary rates (dN/dS) were done to identify modules and candidate genes for diverse floral forms in Achemenes. Nevertheless, there are a few issues in the MS need to be clarified.


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: CO-EXPRESSION CLUSTERING ACROSS FLOWER DEVELOPMENT IDENTIFIES MODULES FOR DIVERSE FLORAL FORMS IN ACHIMENES (GESNERIACEAE)
Review round: 1
Reviewer: 2

Output:
Basic reporting: English is of sufficient quality, references are updated and data is shared in public repositories.
Experimental design: No comment
Validity of the findings: The validity of the findings depends on a better description of the developmental stages sampled.  The section "Hub nodes contain important candidates for floral form" requires a more comprehensive discussion as in its current form only an ad hoc example is used to assess their contribution to floral form but extensive expression and functional literature is available for each of the genes reported.
Additional comments: PeerJ
Co-expression clustering across flower development identifies modules and candidate genes for diverse floral forms in Achimenes (Gesneriaceae)

The authors generate floral transcriptomes from 10 species of Achimenes in two floral developmental stages. Their goal is to identify the genes, gene clusters and possibly gene networks underlying floral shape and other features responsible for shifts in pollination syndromes. The strengths of the manuscript lay on the ambitious computational approach undertaken and the generation of a large dataset for comparative transcriptomics in this non-model taxon. The weaknesses are the lack of specific developmental landmarks for the floral stages selected, and the lack of candidate genes at the end of the analyses that are never presented but that are suggested from the title. In addition, my recommendation is to rescue the biological significance of the results. Currently much of the descriptions are concentrated in module description (i.e. (‘brown4’, ‘coral2’, ‘floralwhite’, ‘lavenderblush3’, ‘lightcyan1’, ‘lightsteelblue1’, ‘maroon’, ‘mediumpurple3’) and the real floral features are harder to pick up from these descriptions. Can clusters at least be numbered instead of described by colors?.

Introduction

Line 54. “flowers may be under constant and strong selective pressure”. Strong selective pressure might be associated with the whole plant, reflecting adaptation to abiotic or biotic selective pressures. Color variation is also related to drought stress, soil changes, herbivory, and other factors that vary spatially.

Line 61. “The transcriptome is highly dynamic”. Which transcriptome?. I think the sentence can be removed as it corresponds to a general statement on transcriptomes.

Line 72. “It is now recognized that most genes act as members of biological pathways or of co-regulated modules”. There are other recent studies that could be cited (2014-2018), with emphasis in plants co-regulated modules, that explained even more complexes interaction than just co-expressed pairs of genes as suggested in Stuart et al. 2003. For example, Ma et al., 2018. Co-expression gene network analysis and functional module identification in Bamboo growth and development.

Line 79. Syndromes are in parenthesis and the sentence really refers to pollinators. Please revise.

Line 80. Figure 1. The authors included an informative and clear figure showing the phylogenetic relationships in Achimenes. However, despite the fact that the figure title indicates  “floral form” such trait is not easy to identify from the pictures of A. longiflora, A. cettoana, A. grandiflora, etc. New pictures perhaps similar to Figure 1B of Roberts and Roalson, 2017 may be necessary.

Line 83. “Repeated origins and transitions between these pollination syndromes have been hypothesized in Achimenes”. Please include a citation.

Line 100. “to identify candidate genes and pathways that may be associated with the repeated evolution of floral forms underlying pollinator specificity”. Only form was significant to the pollinator specificity? What happens with the color? Any relevant or significative finding linked to this trait?

Materials and Methods

Line 114. “an intermediate stage before anthesis”. All stages need to be described in terms of developmental timing and landmarks. Size does not suffice to make stages comparable.  This is one of the weakest points of the manuscript as later on the hubs go on to identify floral traits (for instance spurs)  associated modules and it is unclear if they are already beginning to form in the sampled points.

Line 145. “Grabherr et al. 2011; Haas et al. 2013”

Line 178. This information: “Rows corresponded to orthogroups and columns corresponded to individual samples” is associated with a Table or Suppl. Material?

Line 193. What was the threshold used to determine the edges of the corresponding TOM similarity results?

Results

Line 274. Due to the information included in this section: “Our focus in our comparative study was on the presence of conserved orthologs, and not on the presence of taxonomically restricted genes, which are not likely preserved across species. We subsequently identified 83595 orthologous clusters (orthogroups), each containing at least 2 species”. I suggest changing the title “Transcriptome assembly” to “Transcriptome assembly and orthogroups identification” or move this part to the beginning of the next section “Constructing the co-expression network for 12 species”.

Line 281. “De novo assembly enables functional genomics studies in non-model systems without a reference genome, but has the potential for misassemblies (Hornett and Wheat 2012) and subsequent downstream biases”. This paragraph seems to be part of the discussion and it suggests the approach is not free from bias which is somehow negative.

Line 282. Although, the misassembly is a possible consequence of the De novo assembly process; Hornett and Wheat (2012), also suggest a level of bias in the genes that can be annotated in the resulting transcriptome, were genes might be potentially missing during the analyses.

Line 309. It might be interesting if the genes inside these non-preserved modules could be assigned to other functional categories, such as transcription factors or constitutive genes.

Line 316. Figure 2: I suggest split this figure in two different figures, one for the current A and B (co-expression network analyses) and put the correspondence of Bud and D stage modules (C) in a different figure. As it is the shared modules between the Bud and D stage, and their specific number of genes are hard to read.

Line 346. In “Modules associated with floral traits” it is stated that “WGCNA does not use trait information when inferring modules, so modules that correlated strongly with any floral trait were inferred without a priori knowledge”. However, it is interesting only few species are correlated to each module for a specific trait. Please explain the phylogenetic mixed model, and how was that used to avoid or control the phylogenetic bias and their possible influence in the association that was done with the floral traits.

Line 352. Presence/absence of spurs is unclear in Fig 2. Please add the information missing.

Line 369. Please include information about specific functional categories, regarding the genes in each module associated with the pollination syndromes, flower color, etc.

Discussion

Line 442. In the eigengene expression results: modules without significant association (> 1.0 or < -1.0), for example, “bisque4”, “honeydew1”, and “ivory”, in Figures 3 and 4, might suggest these are housekeeping genes?

Also, why are these rows lacking colors for “strongly positive”, “weakly positive”, “strongly negative” or “weakly negative”,  when same rows show species with significant values of eigengene expression (>1.0 or <-1.0), in the two right columns in Figures 3 and 4?

Line 477. This is important and might be interesting to test this approach of co-expression network analyses, using quantitative variables in the “eigengene” correlation. For example: the presence of nectar (nectar volume, sucrose concentration, etc). [See: Vandelook et al., 2019. Nectar traits differ between pollination syndromes in Balsaminaceae. Annals of Botany, Vol 124, Issue 2, 269-279.]

Line 493. The section "Hub nodes contain important candidates for floral form" requires a more comprehensive discussion as in its current form only an ad hoc example is used to assess their contribution to floral form but extensive expression and functional literature is available for each of the genes reported. At this point this section requires a more rigorous literature revision.

Line 496. Genes identified (AG, TCP4, GLO, etc.) are only discussed selectively from some species, but the choice for discussing in such particular taxa is unclear. Sometimes the reference is Arabidopsis, sometimes Aquilegia, sometimes Antirrhinum. Authors need to explain why specific roles are highlighted and not others.

Line 567. There is no year of publication for Hahn and Kern (2004) in the references.

Line 583. Number of modules or the percentage of modules with correlation to any specific trait (shape, color, etc.) at the Bud and D stages is not shown. Can authors report the number of sets of co-expressed genes consistent between the predicted trait and the actual trait of the flowers in each species or species clade?.

Line 585. The module “darkturquoise” in the Bud and D stages, shows a correlation with the expected pollination syndrome (butterfly) and color (purple). However, the eigengene expression is strongly positive in both traits for A. grandiflora (AG) and A. patens (AP) at the D stage, and A. acettoana (AC) and A. longiflora (AL) at the Bud stage. Is there any possible explanation for the differences regarding the evaluated developmental stage?

Line 594. The module “palevioletred3” was correlated to corolla spurs in the D stage network in the species, A. grandiflora (AG), A. patens (AP), and E. verticillate (EV). However it is not clear if spurs have been identified in these species and when does it develop in these species?

Line 647. Please include Suzuki et al. 2018 in references. In references was only included Suzuki et al. 2017 (cited in line 635).

Line 661. Please include a little discussion or conclusion about the results obtained for the two outgroup species that were included in this study (E. verticillata and G. cuneifolia).

Line 665. The sentence “It will be interesting to apply network analyses to study floral diversification in additional lineages and examine how conserved or divergent the patterns are across angiosperms” is an over statement and this will likely change group by group. Please remove and replace with a conclusion more specific to Gesneriaceae flower evolution.


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: CO-EXPRESSION CLUSTERING ACROSS FLOWER DEVELOPMENT IDENTIFIES MODULES FOR DIVERSE FLORAL FORMS IN ACHIMENES (GESNERIACEAE)
Review round: 1
Reviewer: 3

Output:
Basic reporting: Everything is fine except for the availability of the raw and processed data that is not available at this point (see general comments below).
Experimental design: Fine.
Validity of the findings: All underlying data not provided yet. The rest is fine.
Additional comments: This manuscript builds co-expression gene networks from RNAseq data across 10 species of Achimenes (Gesneriaceae) plus two outgroups with contrasting pollination strategies (bees, hummingbirds, and butterflies) to investigate the genetic architecture of flower differentiation. The study seems novel in that I have not seen such an approach applied to investigate the genetic of flower shape across species. Even if few genes are discussed specifically—the attention is given more to the modules—the results are interesting and relevant. The link between the ratio of synonymous to nonsynonymous nucleotide substitutions and the position of genes in the networks is also very interesting to my opinion and tends to validate the whole approach. Overall, the results are certainly of great interest to all scientists that are interested in the genetic determination of flower shape and color and its impact on floral diversity.

Although I don’t have much personal experience with co-expression modules, all analyses conducted in the manuscript seemed very robust and performed adequately (but see comments below). I also found the discussion pertinent and well written.

Most of my comments are rather minor, but I have one that could be slightly more important. It has to do with the delimitation of the co-expression networks as well as their interpretation and discussion. I was surprised to see that several modules that should be independent by definition tend to correlate with the same floral traits. Why is this so? Is it because the threshold of some analyses was too low (either for the module construction or for the correlation analyses)? For instance, how were the settings for the construction of the modules determined? I would be curious to know what happens if you lower the threshold for including genes within a module.

One possibility to explain these results would be that most traits are highly correlated and that it is difficult (maybe impossible) to distinguish the correlations between modules and traits that are due to causation from those that are correlational. Indeed, the fact that numerous traits tend to be selected together by pollinators and this in a convergent manner in different evolutionary lineages could make it impossible to make a causal link between expression modules and the traits they affect. A discussion of these issues seems important in the section on the limitation of co-expression networks in the discussion. This is perhaps where other approaches like QTL analysis becomes very handy to distinguish the effect of genes on specific floral traits. Most QTL studies to data have shown that distinct genes are involved in color, floral shape, nectar, etc. even if they show a strong evolutionary correlation because they are all selected in a convergent manner by pollinators. It seems highly likely that comparative approaches between species will often fail to precisely define the genetic architecture of the traits selected concomitantly and rapidly along specific branches of the trees. This doesn't minimize the conclusions of this study, but this limit should be acknowledged.

Also, I noticed that the authors have decided to keep only the genes that had a positive correlation in expression in the modules (type="signed"). I think this should be justified. Actually, it might explain why different modules are correlated with the same traits (at least partially). Again, I am not an expert in such analyses, but it would have seemed logical to me to keep in a module all the genes that are strongly correlated, either positively or negatively.

Minor comments:

1.	Why keeping orthogroups that are common to the bud and D stages? It seems likely that the genes expressed at these two stages are quite different. Since modules are built separately for the two developmental stages, why not keep distinct sets of genes for each of them? Is it to facilitate comparison of modules between developmental stages ?
2.	Line 454: be more precise than “relatively few genes”. This can have different meanings for different persons. Also, although moderate numbers of genes are found to be different involve in floral changes between species (QTL studies), many more genes are involved in flower development in each species.
3.	The first paragraph of the intro lacks a main trend. Presently looks like different sentences stitched together.
4.	It would be important that all the data was made available following the manuscript acceptance, including genes info, GO terms, modules to which they belong, expression data, phylogenies, tables for analyses, etc. Presently, none of these are available and nothing is said in the manuscript of where they will be archived.


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: TESTING THE INDIVIDUAL AND SOCIAL LEARNING ABILITIES OF TASK-NAÏVE CAPTIVE CHIMPANZEES (PAN TROGLODYTES SP.) IN A NUT-CRACKING TASK
Review round: 1
Reviewer: 1

Output:
Basic reporting: This paper is an interesting approach to an important and widely discussed research topic. In recent years, research has shifted from debating the existence of culture in great apes to trying to dissect its underlying mechanisms and potential similarities and differences to human culture. Those mechanisms underlying animal culture are still debated with controversial input from different scientific fields. I congratulate the authors for publishing negative results, which are mostly still absent in our research field, yet they can provide important information in itself as well as information to improve future research into similar topics. Field work with great apes is often limited in performing experiments and this study has addressed this with standardized experiment in a captive setting, building upon previous work on testing the occurrence of spontaneous behaviour that has been labelled cultural in wild animals.
Experimental design: The paper is well written, and the study was carefully designed. Similar tests have been done beofore, but the stepwise approach to test the hypothesis in this paper is adding a new and coherent level. However, I have some suggestions for improvement as well as some more serious concerns that I would like the authors to address before I can support the publication of this work in PeerJ.
Validity of the findings: The conclusions presented in the manuscript are not supported by the results. Neither social nor individual learning was found to trigger nut cracking using this setup, however the authors seem to favour the option where nut cracking can be learned individually. This “conclusion” needs to be toned down. Especially as in the introduction (Line 140) the authors state that if nut cracking is a CDT it should not re-appear. Listing the limitations of the study in the discussion is a very valuable contribution to future research using a similar set up. However, it seems that the authors then disregard the severity of these limitations and conclude in favour of the ZLS.  In captive animals there is most likely a lack of motivation, these animals are well fed and safe and do not depend on cultural dependent traits for survival. This does not hold true for wild chimpanzees and needs to be discussed in the manuscript.
Nut cracking in wild animals takes years to acquire. Maybe the length of the task needs to be extended. The exposed time period might have been too short. If the conclusions are to assume an age sensitive learning phase, then testing chimpanzees in the predicted age within this learning phase would be critical. I would recommend emphasising this in the discussion part for other researchers to take this into account when replicating the study.
Additional comments: Recent research (Gumert et al. 2019) suggested that potentially some degree of genetic predisposition might help facilitate the learning of proficient tool use in primates. Until today only Western chimpanzees (Pan troglodytes verus) have been observed to use stone tools. It would be important if the authors could inform the reader of the subspecies of chimpanzees that were participating in the experiments. In case this is not known I suggest to at least discuss the possibility of the importance of the sub species.
Your introduction needs more detail. There is a body of literature that needs to be included into this work when discussing potential formative phases in primates. Research of migrating primates has repeatedly shown that that adult wild chimpanzees as well as vervet monkeys conform to behaviours of their new groups, demonstrating awareness of behavioural traits even past what the authors claim to be a formative phase. I would like to see this literature discussed or at least acknowledged in order to provide the reader with adequate information of the topic at hand (see work by Luncz et al. and van de Waal et al.) For further examples of behavioural awareness during migration in wild animals please see Aplin et al. and her work on birds.
Wild chimpanzees are very neophobe and learn what is eatable and what is not from their mothers during upbringing. Later in life they hardly ever explore new food sources as it can come with detrimental costs (which is different from a “formative phase” as they are still “culturally aware” and adjust to local behaviour). Therefore, nut cracking is not only a tool behaviour but also it needs to be learned that this food is harmless. Acquiring the knowledge of eatable food is already social learning and a crucial step in the CDT of nut cracking. This needs to be considered and cannot be disregarded as some prerequisite for the “actual” nut cracking behaviour of lifting a stone up in the air.
In the abstract as well as in the discussion the phrasing “at the very edge of individual learning” or “at the brink of the ZLS” needs to be changed. That is confusing to the reader and does not help the debate of social learning. Either a behaviour can be individually learned or not. If the authors intend to say that a behaviour can be learned but not to full proficiency, they need to make this clear in the text. However, if a behaviour cannot be learned to proficient levels, I would assume that it does not classify for the ZLS.
Nut cracking is also known in Liberia and other locations in the Republic of Guinea (see Kuehl et al. 2019 sub material for a complete table of the distribution of nut cracking in West Africa).
The report of nut cracking in Cameroon (Morgan and Abwe 2006) is based in secondary evidence of nut cracking (shells and stone tools). Chimpanzees in Cameroon have never been observed to nut crack and efforts to find further evidence has not been successful (also see Kuehl et al. 2019). The report of this behaviour in Cameroon therefore has been treated with caution recently as it might have well been carried out by humans. To build a strong argument on this study is disregarding the concerns experts have raised with this finding. The controversy of this paper needs to be discussed. Strong claims like that need to based on more evidence.

Minor issues:
Line 157: Tennie 2009 in press, what does that mean. In press usually does not have a publication year.
161-164: Please rephrase the hypothesis, and explain in more details what you are going to test. It is not easy to follow.
Methods: Please include more details of the setup of this study (zoo, sanctuary, feeding times, group composition)
Line 240: Age nine is not adult
Add the total number of hours tested. In the Abstract the authors state extensive learning opportunities for nut cracking are provided in this experiment. In the wild nut cracking takes years to acquire, please delete extensive.
Line 271-275: Please explain this further. Break down this sentence into smaller sections, is very long and contains multiple lines of information.
Line 280: typo: texting
Figure 2: we cannot see the anvil. Please provide a picture that shows the dimensions of the objects included.


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: TESTING THE INDIVIDUAL AND SOCIAL LEARNING ABILITIES OF TASK-NAÏVE CAPTIVE CHIMPANZEES (PAN TROGLODYTES SP.) IN A NUT-CRACKING TASK
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript is well written in clear language. There are places in the introduction that feel slightly overwhelmed by terminology. I suggest a table with definitions might make it easier for the reader to keep on top of the terms. Terms included in the table could include cultural trait, CDT, cumulative culture, ZLS, accumulation of traits etc.

I do feel that the authors miss out some relevant literature on the development of nut cracking abilities in wild chimpanzees – especially with regard to the time scale of the development of this skill (see below for more discussion).

Raw data and code are provided online.
Experimental design: The methods were detailed well in text and using clear figures and I believe they are in enough detail to sufficiently replicate the study.

However, there are some issues with the experimental design that I feel should be addressed in the manuscript which I detail below:

Line 135, the authors state that: “If nut-cracking requires social learning (if it is indeed a CDT), it should re-appear when a naïve chimpanzee has access to a model nut cracker to observe.”

Although the authors go on to say that to test if it’s a CDT, testing for its re-innovation without social learning is necessary, this sentence still suggests that behaviours that require social learning should reappear if given social demonstrations. There could be many reasons why a behaviour reliant on social learning wouldn’t emerge after demonstration, including insufficient period of demonstration, social reasons such as rank, social network, and individual differences such as age, motivation, learning ability and many more. I would suggest rephrasing to avoid giving the impression that the lack of a behaviour after a demonstration is good evidence that it’s not a CDT.

The social opportunities presented by the authors to the captive chimpanzees are very different to those afforded to the chimpanzees that exhibit these nut-cracking behaviours in the wild. Whilst the effort to separate the different types of social learning (through stimulus enhancement and ghost condition) is commendable and interesting, these opportunities are extremely restricted when compared to their wild counterparts and I think this needs to be discussed.

The authors mention themselves in the discussion that (L518) “some chimpanzee populations in the wild regularly crack nuts (on average 270 nuts per day for as long as 2 hours 15 minutes in Taï Forest)”. You also mention very briefly (on line 625) the long trial and error learning required by wild chimps to crack nuts. So the number of social demonstrations provided to the learner must be many, many times more than the 30 used in the current study. I’m surprised therefore that the authors have not mentioned this before in the introduction or in relation to their own results as it seems to be extremely pertinent – if wild chimps take so long to exhibit this behaviour, whether through individual learning or action copying - why then did the authors decide that 5 trials of roughly 3 hours would be sufficient to test this behaviour at each stage?
The authors could mention here that the (young) chimps in Marshall-Pescini & Whiten (2008) learned to crack nuts in a very short time period – was this the justification for the short time period? I feel that there needs to be a lengthier discussion of this extended learning time in the wild in relation to the aims, results and limitations of this study.

Similarly, given the well-known literature on critical learning periods in nut-cracking in wild chimps (which the authors discuss in relation to why innovation was not seen), I feel that the authors should provide some rationale in the introduction for testing adult chimps in this context.
Validity of the findings: The nature of the study meant that the authors were unable to use inferential stats, but provide descriptive stats of their results. I think more details are required about the behaviours that did occur (particularly the "place" behaviours, see detailed comments below).

The study has interesting aims and I think the results would provide valuable information to other researchers in the field. However, I suggest that the authors need to be clearer in the manuscript about the limitations of the study, how this may have affected the results, and what they can conclude from the results.

Since the chimps did not exhibit nut cracking behaviour under any conditions, the authors conclude that the data did not provide conclusive evidence for either of their hypotheses. However, they also claim that (L628) “the findings of this study, and others, do not support the view that nut-cracking has to be reliant on social learning, i.e., it does not seem to be a CDT. Therefore, it remains possible that nut-cracking, while inside the chimpanzees’ ZLS, is at the very brink of it.”
The language used here seems to suggest that the authors find the results to point more towards the ZSL hypothesis than the CDT hypothesis. However, I'm not convinced that this is warranted from the current results.
The main results, as far as I can see, are that these adult, naïve chimps did not individually innovate nut-cracking, nor did they copy nut-cracking from a human demonstrator (or by using the other tested social learning forms) during a relatively short time period. There is support for neither hypothesis and I think the authors need to be clearer about this in some areas.
Additional comments: Please consider formatting your ms in double space for future reviews – it makes it a lot easier to read.

Abstract:
I suggest making clear in the abstract that it is a human doing the full demo as this is quite an important point that the reader probably wants to know at the earliest opportunity.

You say the chimps were given “extensive opportunities” to learn the behaviour. Were they really that extensive? Compared to previous experiments or wild conditions?

L316 – Is this hammer a similar size/weight/shape to hammers used in wild populations? If so, would be good to state. If not, also state why it differed and whether this may have any effect.

L375 – some chimps cracked the nuts with their teeth pretty early on (you later discuss this with regard to behavioural conservatism). Does this ever occur in the wild or are the available nuts in their habitats all too hard to achieve this?

L475 - It's unclear from the results when these behaviours occurred. Were they during the baseline phase or the social learning phases (if so, which ones?) - this seems especially interesting for the "place" behaviours (see below)

L477 - You recorded a number of "places". Why would the chimps place the nut on the anvil so many times?  Did they similarly place nuts on other surfaces around the enclosure? During which phase did these behaviours occur? It's hard to tell without more information, but it seems possible that this placing behaviour could potentially be the beginning of the nut-cracking sequence. If they were given more time to individually learn/view more demos, would this placing behaviour then be followed by the other stages of nut-cracking? I think the authors need to give more details about the context of these behaviours.


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: TESTING THE INDIVIDUAL AND SOCIAL LEARNING ABILITIES OF TASK-NAÏVE CAPTIVE CHIMPANZEES (PAN TROGLODYTES SP.) IN A NUT-CRACKING TASK
Review round: 1
Reviewer: 3

Output:
Basic reporting: Overall, this manuscript clearly explains the experimental design and results of the research, and does so while citing a wide range of the relevant literature. The extensive data collection phase consisted of baseline, end-state, ghost, and full action demonstration conditions wherein 13 captive adult chimpanzees were afforded the raw materials (hammer, anvil, nuts) for nut-cracking. Although none of the chimpanzees used the tools to crack the supplied nuts (some used their teeth), a number of interesting conclusions regarding, e.g., sensitive periods, are posited. Several improvements to the manuscript are desirable before it is suitable for publication.

First, the Introduction lacks focus. The descriptions of the competing hypotheses (nut-cracking as a culture-dependent trait vs. latent solution) are separated from each other by several paragraphs, making it difficult to properly contrast them in meaning & implication. The paragraphs beginning on Lines 93 (complexity) and 166 (latent solutions tests) could be cut down significantly or even eliminated.

Related to this, it was difficult to follow what the requirements of culture-dependent traits are. It seems that social learning is required (line 74), and that change of a trait via transmission (lines 86-89) is also required. Is this the case? Or would a trait that requires social learning but is unchanged after transmission qualify as a CDT as well?

Second, why is it important to determine whether nut cracking (and other potentially cultural behaviours) are CDTs versus individually acquired/innovated?

Third, it is correct to state in the Abstract (lines 50-52) and Conclusion that the results obtained here do not rule out the possibility that tool-based nut cracking is a behaviour that could be re-innovated in the absence of social learning. It is, I think, important to acknowledge in both places that the results also do not rule out the possibility that nut cracking is a behaviour which requires social learning/a CDT (as is done in the Discussion).

The shared data file contains information about the individuals observing full action nut-cracking demonstrations. Can the data for the ghost demonstrations also be shared? It is difficult to link an individual chimpanzee listed by name in the data file to their number from Table 1.
Experimental design: Useful experimental design, clearly described. A few questions for clarification:

-How many types of familiar foods were given in motivation trials? Just the 2 listed?

-What does “preference testing” (line 273) refer to?

-How would the not-carried-out “local enhancement” condition have differed from the end-state condition? Would all of the scattered nuts (not just those on the anvil) be half-shelled?
Validity of the findings: Statistics were not performed on the nut-cracking data, as in the end none of the chimpanzees used the tools to crack the nuts. However, the authors provided a good amount of detail regarding inter-rater reliability, trial duration, the number of chimpanzees who observed/did not observe various demonstrations, and other events.

Some important information that should be included in the Results is the condition(s) in which the relevant behaviours (place, hold, stamp, and throw, lines 476-482) occurred, in either the text or a table.

Would it be possible to report information about the number of nuts that ended up being consumed in the trials? i.e., was it possible to retrieve any unopened/opened nut shells from the enclosure(s) after the trials? That could give a sense of how many of the nuts were opened by mouth and consumed.

An additional useful piece of information would be whether the end-state condition had (one of) the desired effect of increased chimpanzee interest in the anvil area compared to the baseline condition, if this is straightforward to extract from the existing data.
Additional comments: If the authors so desire, the title could be re-worded to “…task-naïve captive adult chimpanzees…” for readability.

In the Abstract, do lines 34-39 refer to a particular study? It would be helpful to cite this here.

In the Abstract, it is noted that “none of the chimpanzees tested here developed the behaviour”. However, some of the individuals were able to open the nuts with their teeth; therefore, it would be useful to specify that none of them developed the method of nut-cracking *which required the use of tools*. Same for Conclusions, line 586.

Check spelling of author name in reference Odling-Smee et al. 2003.

In the Introduction (line 153-156), the contingency should go the other way.

Regarding the minimal reported “hammering” behaviour in this group of chimpanzees, I am curious if they are ever given whole coconuts. In other zoos, these are given as enrichment and are opened by banging/dropping/throwing. This could be a relevant antecedent behaviour.

Line 278 complimented -> complemented

Line 280 texting -> testing

In Figure 2 (and 3), it is not immediately clear which thing is the anvil, and which is the hammer. Labelling would be helpful.

What are the “relevant behaviours” referred to in Line 335? The ones listed in Table 2, or others?

Throughout: check subjects’ vs subject’s vs subjects (and individuals’ vs individual’s) (lines 364, 403, 425, 466)

Table 2: was “place” required before “throw” for it to count? If not, please note this where coding is described (line 448-450) or in a footnote to the table.

Why was C13 present for the motivation test (before the baseline condition) but not during the baseline condition? Were there motivation tests before every condition?

Please clarify what “(n=13)” in lines 500-501 refers to.

I am curious whether, in the behavioural flexibility account for why these chimpanzees did not re-innovate tool-based nut-cracking behaviour (lines 538-556), the behaviour "counts" as a CDT, an individually innovated solution, or could be either one? (This is mentioned for the other accounts.)

I’m not sure how it logically follows from the fact that other species use stones to crack nuts in the wild that social learning is not necessary for nut cracking in chimpanzees (Lines 610-613).

Specify that it is *wild* chimpanzees who go through a long trial-and-error learning process (line 626)?


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: TESTING THE INDIVIDUAL AND SOCIAL LEARNING ABILITIES OF TASK-NAÏVE CAPTIVE CHIMPANZEES (PAN TROGLODYTES SP.) IN A NUT-CRACKING TASK
Review round: 2
Reviewer: 1

Output:
Basic reporting: The revisions have been addressed in a thorough way and I am happy to recommend this manuscript now for publication.
Experimental design: see above
Validity of the findings: see above
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: TESTING THE INDIVIDUAL AND SOCIAL LEARNING ABILITIES OF TASK-NAÏVE CAPTIVE CHIMPANZEES (PAN TROGLODYTES SP.) IN A NUT-CRACKING TASK
Review round: 2
Reviewer: 2

Output:
Basic reporting: Thank you to the authors for their detailed answers to my original questions. I find that the manuscript has been much improved and suggestions by the editor and three reviewers have been sufficiently answered and used to revise the paper. There are still a few occasions where the language suggests that the results favour one explanation over another that I think should be changed, and these are listed below with other, minor comments. Overall, I think the paper provides interesting new data in the field of the evolution of tool use/culture and recommend it for publication in PeerJ once these minor revisions have been addressed.

Minor comments:
Line 38: "...are in line" - "are" is missing

Line 53: “…AND when ecological conditions allow for it” instead?

Abstract: I feel like it might be useful to have a sentence around L48 along the lines of “..therefore, we did not find strong evidence for either hypothesis” – just to easily clarify the findings?

Line 80: “Some animal cultures may be culture dependent”….some traits?

Line 93: “….ratchet effect’ (), which underlies cumulative culture () – and is responsible for the special product of cumulative culture: CDTs” – Are CDTs a product of cumulative culture? Wouldn’t they be the basis of cumulative culture? I suggest rephrasing

Line 126: “..emphasis added), Biro…” – full stop instead of comma?

Line 152: “This would provide evidence for the view that social learning is required for nut-cracking to occur.” – even when tempered by the following sentences, I still find this statement too strong, but will leave it to the Editor’s judgement on whether it should be further changed.

Line 209 – Hypotheses instead of hypothesis

Line 504 – “nuts were/are palatable”

Line 686 – I think the sentence in parenthesis should be removed – after all the same could be said of their failure to innovate the behaviour in this study

Line 693 – Again, you could delete the ‘fully’ here – the language is still subtly pointing towards ZSL as the most likely explanation, even though the results of the study clearly do not provide support for either

There are a couple of issues with the supp materials:

- In response to my prior comment (2a in their rebuttal), the authors say they've added a supplementary table with definitions of terminology, but I don't see this. Perhaps they forgot to upload it?

- There are two supp files labelled as attention to full demos, but one of these is attention to the ghost demos I believe.
Experimental design: NA
Validity of the findings: NA
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: TESTING THE INDIVIDUAL AND SOCIAL LEARNING ABILITIES OF TASK-NAÏVE CAPTIVE CHIMPANZEES (PAN TROGLODYTES SP.) IN A NUT-CRACKING TASK
Review round: 2
Reviewer: 3

Output:
Basic reporting: The majority of my comments have been addressed with precision in the revised manuscript. The Introduction lays out the competing theories more concisely, and it is now clearer in which experimental phases the target behaviours occurred. Unfortunately, I did not receive a copy of the glossary mentioned in the authors’ responses (p. 13). My outstanding concerns are as follows.

The reader gets a hint as to why this study was done/what the implications are in Lines 95-97 (“the presence or absence of CDTs in chimpanzees is of particular interest”)/Lines 178-180 (“This would support the ZLS hypothesis and would suggest that chimpanzees are capable […] of individually learning […] nut-cracking”). This gestures in the direction of answering the question “Why is it important to test these hypotheses?” It would be helpful to situate the work you have put in on this question in the context of current understandings of cultures and cognition; this question was answered eloquently in the review responses (“to determine whether the reliance on social learning to develop culture is restricted to our own species or whether it is also common to other apes”). What would it mean for the theory/field if nut-cracking is found to be in chimpanzees’ ZLS (or conversely, a CDT)? Would that make chimpanzee culture a more/less apt comparison to human culture? Would it signify a larger discontinuity in human and chimpanzee cognition than previously supposed? Or, per the review responses, would it allow us to make a particular type of inference about the last common ancestor? A simple statement in a few lines could really clear this up.

I am still confused about what a culture-dependent trait (CDT) is: in Line 78-79 it is stated that CDTs are cultural traits that rely on (cannot occur in the absence of) some form of copying social learning. In Lines 92-95, it is stated that CDTs are the special products of cumulative culture. The first description appears to be much more relaxed than the second: i.e., according to the first definition, a culture-dependent trait does not *need* to be a product of cumulative culture (as in the example of whale song), while according to the second (with CDTs as special products of cumulative culture), essentially any animal “cultural trait”, if needing to be a product of cumulative culture to qualify as a CDT, would fall short.

Lines 154-157: it feels premature to discuss the results of the study before any of the details have been provided. Perhaps part of this could be moved to the Discussion.
Experimental design: Experimental design and methods are clearly described, and points from the initial review have been addressed.
Validity of the findings: Data have been provided, and conclusions are balanced. Points from the initial review have been addressed.
Additional comments: Abstract Line 38: Sentence beginning “The latter findings in line with…” seems to be missing a word.
Abstract Line 49: Sentence beginning “We conclude”: interplay -> an interplay?
Line 113: “alongside with”: one of these words is extraneous.
Line 129: are -> is?
Line 136/140: for “migratory”/”migrating”, “dispersing” (implying not just movement but a change of group) might be a clearer word to use.
Line 292-295: This long sentence should be at least 2 sentences.
Line 326: rope -> ropes?
Line 328-329: missing a “)” somewhere.
Line 502-506: sentence seems to be missing a word.
Line 506: individual’s -> individuals’
Line 536: this title seems to be missing a word.
Line 544: sentence seems to be missing a word.
Lines 629-630, 641, 645: Check spellings.
Can you rephrase the sentence in Lines 710-712? Its meaning is unclear.


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: UPTAKE AND TOXICITY OF CLOTHIANIDIN TO MONARCH BUTTERFLIES FROM MILKWEED CONSUMPTION
Review round: 1
Reviewer: 1

Output:
Basic reporting: Professional language is used throughout the manuscript.  The introduction is reasonable, but some areas of clarification are needed.

Line 48 and other locations: Clarify that clothianidin is not registered for foliar applications on corn or soybean, which are the use sites most relevant for assessing monarch risks, at least in the Midwestern summer breeding range.  Given the nature of the study, the results are primarily relevant to soil drench, soil-applied/granular or seed-treatment formulations/applications.  The study design is marginally relevant for foliar applications. If the authors wish to ‘extrapolate’ their findings to foliar applications, it may be appropriate in the Discussion section.

Line 53: Suggested edit: “Also because of its high-water solubility, there is the potential for clothianidin to move downslope from a crop field with shallow ground and surface water runoff, which makes it available for uptake by non-target plants and potential exposure to animals that utilize those plants (Hladik, Main & Goulson, 2018).”

Line 80:  Insecticides may degrade habitat in agricultural settings …  While the Oberhauser et al 2006 paper is relevant for mosquito adulticide applications, it is not a relevant citation for the application and use site scenario in the current study.  In addition, Anderson et al. and Dively et al address Bt toxin exposure, which is a significantly different story than soil applied/seed treatment formulation of a chemical insecticide.  However, without citing these papers, the case can easily be made that testing the hypothesis that soil applied/seed treatment uses of clothianidin could cause adverse effects is reasonable given the existing, published studies documenting detection of clothianidin and other neonics in milkweed growing in and around corn/soybean fields. Also, here, or lines 96 – 98, or in the discussion also reference the study by Krischik et al 2015 (PLoS ONE 10(3): e0119133. doi:10.1371/journal.pone.0119133), who assessed effects of imidacloprid on monarch larvae (and adults) in a manner similar to this study.

Line 88:  Provide a citation supporting near 100% use (it’s correct – but suggest citing Tooker and Douglas)

Line 89:  what does ‘high’ mean? More accurate to say: ‘exposure cannot be precluded’

Line 102: soil application – be specific; i.e.., via granular soil application.
Experimental design: Line 109:  Confirm distance between nursery and ag fields that could be using foliar or soil applied insecticides in the area.

Line 114-115:  Provide here or later in the methods section, the average height of the plants, and number of leaves per plant at the start of each experiment.  This information facilitates interpretation of the design and study results (i.e., the extent of potential bias in treatments – not withstanding random assignment of plants to treatments).

Line 132 – 133:  Confusing sentence.  Do the authors mean they didn’t want to plant clothianidin treated corn or soybean seeds in the pots since the resultant variability in soil concentrations would likely be extreme given the corn/soybean plants would also be absorbing the active ingredient etc etc?  Totally reasonable approach for this study, but the sentence isn’t clear.

Lines 147 – 152: The aphid infestation creates a confounding factor(s).  Even with treatment prior to initiation of Experiment 2 the plants were likely stressed and their nutritional status compromised.  During the study the control larvae were likely experiencing greater adverse effects due to the aphids than the larvae on the treated plants. While this confounding issue does not preclude publication of the study, it does need to be addressed in the discussion section with regard to the uncertainty in the results and the generalizability of the findings.

Lines 162 – 163:  For Experiments 1 and 2 provide additional detail as to where the larvae were placed on the plants.  Were locations selected randomly, or were locations evenly dispersed on the bottom 1/3, middle 1/3, top 1/3 and new vegetation when 4 or more larvae on a plant?  If less than 4 larvae how were they placed?  This information probably relevant in terms of interpretation of the residue data – residue concentrations may be different based on the age of the leaf.  Also females tend to lay eggs on newer vegetation, presumably due to higher nutritional content.  But if multiple larvae (e.g., 4 to 8) are placed in close proximity on younger vegetation, there may not be sufficient biomass per larvae (as compared to a plant that was infested with 2 or 3 larvae), which could elicit intraspecific competition and or increased on or off plant movement of larvae. If some larvae were placed on older leaves, and less nutritional value, they may have a higher likelihood of mortality independent of clothianidin exposure.

Line 175:  Was the condition of the plants also recorded daily and/or at the point larvae on a plant were all dead or missing or when they reached the pupal stage; i.e., number leaves with feeding, number of total leaves without feeding)?  Was there evidence of feeding on plant leaves even when larvae went missing? This information could help assess the extent to which higher larval infestation rates did or did not create a potential bias due to limited biomass – especially with the 4th and 5th instars.

Line 179 – Missing larvae.  Missing control larvae are likely dead assuming they didn’t escape the cages and a 4th or 5th instar or pupa didn’t ‘suddenly appear’ near the end of the study.  Also double-check the raw data.  For example, it seems in Experiment Two,  7, 2, and 6 larvae were placed on the three Treatment 4 plants; however, the number missing were 0, 4, and 3, respectively (i.e., more larvae were missing than originally assigned to the second plant).

Line 203:  The leaf sampling isn’t clear.  For Experiment 2, was a composite leaf sample collected for each of the 18 plants?  Are residue results plant-specific?

Line 218:  Is this method the same or similar to previous methods use by Hladik et al.?  If so provide a reference or two.

Lines 249, 286, 295:  Provide additional details as to the methods used to calculate dose-response relationships (i.e., what software package and code: R, drc?). Was Abbott’s formula used to correct for control mortality?  Presumably, mortality rates per plant were used as inputs to the dose-response analyses.  Confirm mortality events were based on observation of dead larvae. In addition to calculating a LC50 based on the sum of mortality across larvae, prepupae and pupa, also calculate the cumulative larval LC50 to enhance the means to discern differences in life stage susceptibility. As noted above, it would also be appropriate to calculate the dose-response relationships assuming missing larvae are dead (for control and treated plants) to assess to what extent that assumption influences the results.

As noted by the SD values in the text and data in the supplemental files, the variability of leaf concentrations is very high for levels 2 (196.6, 44.7, 75 ng/g), 4 (433.8, 140.4, 215.1 ng/g) and 5 (155.1, 1036.8, 1337.6 ng/g).  In addition, the mean values for levels 2 and 3 are essentially the same.  Is there any (qualitative) relationship between the location of  sampled leaves (e.g., bottom 1/3, middle 1/3, top 1/3, new vegetation) and residue concentration? Using the mean leaf concentrations in the probit analysis masks the variability in the data. With Level 4 plants mortality (with missing larvae ‘dropped’), rates of 100%, 50%, and 50% is associated with 155.1, 1036,8, and 1337.6 ng/g, respectively. Assuming the residue data for Experiment 2 in the supplemental file are associated with specific plants (e.g., the three concentrations are associated with 3 specific plants) it would be best to consider each of the treated plants as an independent unit.  The LC50 analysis would then use each plant’s specific ng/g leaf concentration and morality rate (i.e., 18 points total – 3 control points and 15 points for the treated plants).
Validity of the findings: Line 269:  Claiming no control mortality is tenuous.  As noted above, missing larvae in the control groups is likely mortality under the assumption a missing larvae did not re-appear in later instars/pupal stage. Perhaps there were some escapes from the cages, but it is unlikely all the missing larvae were escapes.  Based on the data in the spread sheet for Experiment One controls: 3/5, 0/2, 2/2, 3/5, and 0/3 went missing.  Suggest the dose-response analysis be re-done assuming missing = dead to see how much dropping the missing vs. assuming missing = dead influences the findings. Same for Experiment 2.

Line 307:  The trends with the clothianidin treatments is noteworthy.  However, it is difficult to interpret in light of the control data despite the author’s reasonable interpretation that the condition of the control and low dose plants was significantly compromised by the aphids. It is difficult to untangle the aphid X treatment interaction and should be clearly stated in the discussion.

Paragraph starting on line 324: Given the low number of samples and the variability of the plant residue levels care must be taken to not over interpret the significance of these data.  It is reasonable to use the data to indicate there was a complete exposure pathway in the toxicity studies and that the relationship between leaf and larval residues is not inconsistent with the existing body of literature that indicates neonics do not bioaccumulate.

 Paragraph starting on line 340:  Include a summary of https://www.frontiersin.org/articles/10.3389/fevo.2019.00223/full
      that was published after the current manuscript was submitted.  In the paragraph do not use ‘up to’ concentrations.  Only providing upper limit concentrations is a misleading summary of the published data given the skewed distributions of residues in most papers.  Instead provide the % of milkweed samples with detects, the median concentrations. and the range for plants with detections.  A summary along these lines provides a more complete and transparent sense of the residue data and how that data relates to the results of this study.

Paragraph starting on Line 357:  Include a summary/comparison to results reported by Krischik et al 2015 (PLoS ONE 10(3): e0119133. doi:10.1371/journal.pone.0119133) for imadicloprid.

Line 376:  Concur this is a reasonable summary of the Pecenka and Lundgren (2015) paper.

Line 380:  While these may be the first data showing trophic transfer is it all that surprising since this compound is designed to kill piercing/sucking and chewing insect pests?  The data does provide confirmation that there was clothianidin exposure to the larvae in the toxicity studies.  The fact that the adults have a clothianidin load is not all that surprising, unless the authors assumed the pupae are highly efficient metabolizing clothianidin and would degrade all the residues accumulated through the 5th instar. I am not aware of any published data that would support such a hypothesis.

Lines 389, 392:  If the authors wish to raise this issue, even though it is outside the domain of the paper (nectar concentrations were not measured in this study and other than successful eclosion no assessment of adult exposure was undertaken), they should cite and summarize the findings in Krischik et al 2015 (PLoS ONE 10(3): e0119133. doi:10.1371/journal.pone.0119133) for imadicloprid.

Paragraph starting on Line 397: This paragraph is stretching beyond what the data in this paper and the literature supports.  What are the median residue levels in nectar? And what data exists to suggest an adult concentration of 5 ng/g is of toxicological concern?  It would be reasonable to conclude that while this study captures most of the monarch life cycle but the potential effects of neonic exposure on adult survival, behavior, and reproductive performance have yet to be studied (with a note that some work done by Krischik et al.).

Paragraph starting on Line 426 can be deleted. It doesn’t add significant information/interpretation of this study’s results.

Paragraph starting on line 435 should be placed after the paragraph ending on line 424.
Additional comments: This study was challenging to undertake and the authors are congratulated for their efforts.  Undertaking an ecotoxicity study that attempts to mimic an environmental setting, but maintain some degree of control over variables, is very difficult.  This study will contribute to the evolving understanding of the potential risks of neonic exposure to monarchs; however, the paper requires significant revision before it can published.  While it may not be possible to fully address the confounding variables and experimental design constraints, the revised paper needs to provide a more complete and transparent representation of the uncertainty in the results and their limitation for use in assessing risk.